Reviewer #2 (Public Review):

The authors sought to characterize normal placental aging to better understand how the molecular and cellular events that trigger the labor process. An understanding of these mechanisms would not only provide insight into term labor, but also potential triggers of preterm labor, a common pregnancy complication with no effective intervention. Using bulk transcriptomic analysis of mouse and human placenta at different gestational timepoints, the authors determined that stabilization of HIF-1 signaling accompanied by mitochondrial dysfunction and cellular senescence are molecular signatures of term placenta. They also used in vitro trophoblast (choriocarcinoma) and a uterine myocyte culture system to further validate their findings. Lastly, using chemically induced HIF-1 induction in vivo in mice, the authors showed that stabilization of HIF-1 protein in the placenta reduced the gestational length significantly.

The major strength of this study is the use of multiple model systems to address the question at hand. The consistency of findings between mouse and human placenta, and the validation of mechanisms in vitro and in vivo modeling are strong support for their conclusions. The rationale for studying the term placentas to understand the abnormal process of preterm birth is clearly explained. Although the idea that hypoxic stress and placental senescence are triggers for labor is not novel, the comprehensiveness of the approach and idea to study the normal aging process are appreciated.

There are some areas of the manuscript that lack clarity and weaknesses in the methodology worth noting. The rationale for focusing on senescence and HIF-1 is not clearly given that other pathways were more significantly altered in the WGCNA analysis. The placental gene expression data were from bulk transcriptomic analyses, yet the authors do not explicitly discuss the limitations of this approach. Although the reader can assume that the authors attribute the mRNA signature of aging to trophoblasts - of which, there are different types - clarification regarding their interpretation of the data and the relevant cell types would strengthen the paper. Additionally, while the inclusion of human placenta data is a major strength, the differences between mouse and human placental structure and cell types make highlighting the specific cells of interest even more important; although there are correlations between mouse and human placenta, there are also many differences, and the comparison is further limited when considering the whole placenta rather than specific cell populations.

Additional details regarding methods and the reasons for choosing certain readouts are needed. Trophoblasts are sensitive to oxygen tension which varies according to gestational age, and it is unclear if this variable was taken into consideration in this study. Many of the cellular processes examined are well characterized in the literature yet the rationale for choosing certain markers is unclear (e.g., Glb1 for senescence; the transcripts selected as representative of the senescence-associated secretory phenotype; mtDNA lesion rate).

Overall, the findings presented are a valuable contribution to the field. The authors provide a thoughtful discussion that places their findings in the context of current literature and poses interesting questions for future pursuit. Their efforts to be comprehensive in the characterization of placental aging is a major strength; few placental studies attempt to integrate mouse and human data to this extent, and the validation and presentation of a potential mechanism by which fetal trophoblasts signal to maternal uterine myocytes are exciting. Nevertheless, a clear discussion of the methodologic limitations of the study would strengthen the manuscript.

Reviewer #3 (Public Review):

In this study, Ciampa and colleagues demonstrate that HIF-1α activity is increased with gestation in humans and mice placentas and use several in vitro models to indicate that HIF activation in trophoblasts may release factors (yet to be identified) which promote myometrial contraction. Previous studies have linked placental factors to the preparation of the myometrium for labour (e.g. prostaglandins), but HIF-1α has not been implicated.

Weaknesses and concerns:

1) The author's rebuttal state that placentas undergo subclinical cellular aging as they reach term. Although several future studies are described to test functional deficits at the cellular level, the current manuscript does not provide convincing evidence of cellular aging. The only evidence of cellular senescence provided in both human and mouse data is the mRNA expression of a single gene associated with senescence.

2) The authors have not responded to the concern regarding CoCl2 mediating differentiation. The paragraph from a ref states that JAR cells do not respond as well as BeWOs to forskolin. However, this does not mean that JAR cells do not differentiate. This point is particularly pertinent as a quick search of their RNA-seq data shows upregulation of STB genes following CoCl2 treatment including ERVs (ERVFRD1, ERVV-1, ERVV-2, ERV3-1), CYP19A1 and OVOL1 just to name a few. If the authors' conclusion is that CoCl2 treatment did not alter trophoblast differentiation, the authors should provide additional data showing this. For example, cell fusion assays showing E-cadherin/desmoplakin staining and nuclear localization within stained boundaries.

3) The authors acknowledge the possibility of extraplacental effects of DMOG in the initiation of labour in their model, no additional evidence has been provided to support placental effects of their model. The authors also argue that although PMID 30808919 (which specifically overexpressed HIF-1a in the placenta) did not show changes in birth length, they propose that this may be due to constitutive HIF1a expression at the beginning of pregnancy. This argument is invalid since placental maldevelopment is consistently linked with several pregnancy complications including spontaneous preterm birth. If anything, perturbations in the beginning of pregnancy are more likely to lead to worse outcomes than those at the end of pregnancy.

4) Regarding induction of syncytialisation, please provide additional evidence that the cells have/have not syncytialised.

5) Lack of cohesion between experimental models. Please provide evidence that DMOG mediates similar effects on SA-β gal activity as CoCl2 in JARs.

6) Evidence of senescence and mitochondrial abundance could be strengthened by providing additional markers. E.g. only GLB1 mRNA expression is provided as evidence of senescence, and COX IV protein for mitochondrial abundance in mouse and human placentas. This point has not been addressed. Please provide at least one additional marker of senescence and mitochondrial abundance.

Reviewer #1 (Public Review):

This manuscript employs a string method with swarms of trajectories to extract a free energy map of KcsA channel inactivation and its model dependence. The approach connects X-ray structures for closed, partially and fully open, and inactivated KcsA through optimisation of a string defined in a collective variable space consisting of distances involving gate size, cavity-filter and filter pinching (as defined in the proposed X-ray structure for an inactivated state). The final trajectory includes pore opening and filter collapse with water penetration behind the filter, via different intermediates depending on the force field. The authors propose a role for residue L81 in controlling water entry in the final stage of this process. The results suggest that KcsA more easily inactivates with the Charmm force field, with lower barrier and direct passage from a partially open state, whereas the pathway for Amber involves transition first to a fully open state with higher barrier, despite not being the dominant open state seen experimentally under activating conditions. The results also suggest that PG lipids help activate the channel within the Amber force field, consistent with experimental evidence. The work represents large-scale advanced MD simulation. Some questions remain, however, such as if the CV space chosen is sufficient to capture all possible slow coordinates in the inactivation process, and how the resultant free energy surfaces may potentially depend on the end structures and initial pulling procedure.

Collective variable choice:

The explanation for the choice of CVs on page 5 is not sufficient to understand the process and its likely success. How were the most important and unimportant CVs identified exactly? Table 2 on page 19 shows only gate distances, cavity-filter distances and a single variable related to filter structure itself (77 CA - 77 CA) representing a pinch. Is that pinching really the only slow variable associated with inactivation changes in the filter? Why are there no variables, say for carbonyl flipping, E71 or D80 movements or even for ion and water occupancy (although water may be sampled with control of other interactions, such as involving L81)? I understand that the X-ray structure is the one source of information used to define an inactivated structure and is one with just a pinch and no complete carbonyl flipping away from the pore, as has been identified in past studies and discussed as being involved by the authors on page 14. Key changes like carbonyl flipping surely are part of the story and may be slow variables. At the very least, if not part of the CV space, could be analysed.

On page 10 the authors discuss possible differences in Amber and Charmm involving the extent to which the 4 subunits change in respect to the L81-W67 water pathway and W67-D80 hydrogen bond, arguing the different results for force field could be to do with different numbers of subunits doing different things. If I understand, the chosen CVs are all tetramer-based distances (including across subunits) and not subunit-based CVs, so that random and incomplete changes may occur to subunits for a given point in CV space. There is thus potential for the string to converge on a local minimum pathway with partial changes to its interactions within and between subunits, and may not be a unique global solution. Can the authors please explain whether or not this is possible and what analysis has been done to check it?

X-ray endpoints and initial pathway:

The string was created from a pulling/steered MD between existing X-ray structures for the closed (5VKH), partially open (3FB5), fully open (5VK6) and finally inactivated (5VKE) states. The authors write on page 12 that "The block of conduction during inactivation appears to result from pinching at the selectivity filter...", but given the end point was forced to be the X-ray structure with pinching, wasn't this outcome predetermined? This raises a significant point of how much has choice of endpoints predetermined the final states of the string? i.e. How much is an end state actually allowed to draft away from the initial Xray structure. Was a bead placed at the very endpoint and allowed to update via swarms, or was it fixed and all beads just interpolate between those fixed end states? The reason this is important is that it is plausible the inactivated crystal structure with pinching but not other changes (such as complete V76 carbonyl flipping or outer filter splaying), may not be the actual free energy minimum structure for that state and that force field.

Another obvious concern is the possible reliance on the initial pulling procedure used before string optimisation began. Fig.2 Supp 1 shows generally that the Amber path stayed pretty close to the initial steered MD path, whereas Charmm drifted downward away from that path. One could justifiably ask, if a very different initial path was chosen, might different local minimum pathways result, including Amber sampling a path like Charmm? How does one test whether or not the final path has not been trapped in some local trough of free energy? e.g. Imagine starting the Amber string using an initial path like the more diagonal Charmm-like path, or even a more extreme unphysiological one, such as a steered trajectory that initially inactivates before opening the gate. Would the final results be the same? I appreciate the simulations are very expensive and such trials may not be possible, but what evidence is there that the final path has not been trapped away from the global minimum?

One test offered by the authors is a set of unbiased MD simulations launched from points on the string. The authors ran 200ns simulations and write on page 5 that "These simulations have the expected stability based on their starting values. This is a good quality test to check the correct estimation of the general features of the free energy surface". While this sounds reasonable, 200ns MD may only be sufficient to begin to explore locally within the solved free energy trough, much like the swarms in the iterations were able to do. My own examination of Fig2 Supp 5 is that some of these simulations linger around the expected states and some drift away within the general trough of sampling, which is a good sign. What those 200ns simulations may not be able to do is escape that trough and see evidence of other possible solutions, beyond what was sampled with the string that was tied to Xray endpoints and trapped in the solution pathway that was already formed after 100-300 iterations. Overall, the string involved 800 iterations of 10ps swarms (80ns around each bead; albeit 32 trajectories in parallel), allowing good local sampling around the beads in the free energy trough, but in terms of ability to diffuse away from that point, only being comparable in contiguous trajectory time to the unbiased MD tests. It therefore would have been interesting to see if longer simulations remain in this trough; though I understand the challenges in running so much MD. Such simulations may, however, lead to exploration beyond what was seen in the string solutions.

Force field effects and origin:

Regarding the effect of the chosen force field, the authors state that "Given that our simulations were conducted under activating conditions, we had expected the open states to be more populated than the closed ones. Simulations carried out at higher pH may be able to resolve this inconsistency". Also running at high pH would be a nice thing to do to prove the method is in fact sensitive to conditions to see a shift in the distribution of states. But the question is why were open states not more occupied under low pH and 50mM K+? From my analysis of the figures, the results show that the Charmm force field tends to allow for opening of the channel somewhat (at least with similar free energy for partially and fully open to closed) whereas Amber tends to close the channel more (with more uphill energy as the channel opens than Charmm; Fig 2). i.e. at low pH and 50 K+, isn't the Amber model incorrectly reporting fairly strong bias against opening? Moreover, regarding the free energy of the inactivated state itself, why should we not expect equilibrated channels under activating conditions to eventually fall into an inactivated state, in which case we should expect low free energy of that state (as found with Charmm and not Amber in Fig2), but with a slow rate. While much discussion in the manuscript appears to discuss limitations in Charmm (although on page 12 discussion leans either way), these factors may seem to favour Charmm over Amber.

On page 12 the authors explain the possible causes for force field dependence, although this seems limited to ion interactions, glutamate charges and dihedrals. But it would be nice to get a bit more insight into what terms may have influenced the pathway, in particular involving interactions between TM2 and the base of the selectivity filter and hydration behind the filter. Regarding ion interactions, is there a good reason to believe ions are key to the difference seen? i.e. How were ions involved differently in the state transitions involving Amber and Charmm? The authors have noted a role for ion-carbonyl interactions. It is important that the authors explain which is the two competing models has been used and why. i.e. Off-the-shelf Charmm36 force field includes strong K+-backbone carbonyl interaction, previously seen to promote high ion occupancy, similar to Amber, whereas Lennard-Jones parameters modified to match N-methyl-acetamide and water partitioning (such as early Berneche, Noskov and Roux work) reduce ion occupancy and increase water content inside the filter.

Reviewer #2 (Public Review):

The authors describe a computational study into the energetics of KcsA inactivation. Using enhanced sampling, a converged free energy landscape of the inactivation process is achieved in two modern molecular mechanics force fields. The obtained profiles confirm the literature finding of too rapid inactivation, in particular in simulations using the CHARMM force field. Interestingly, it is found that selectivity filter collapse does not gradually follow opening of the inner gate, but proceeds rather switch-like. A key role for residue L81 is proposed as opening gateway in this process.

The study is impressive and interesting. However, I have a number of concerns that the authors may wish to address in a revised version of the manuscript.

First, concerning a set of unbiased simulations spawned at different regions of the investigated free energy landscapes, the authors write: "These simulations have the expected stability based on their starting values".<br /> Fig 2.c shows a rather smooth downhill slope in the free energy curve towards the closed state for AMBER , so wouldn't the expected behavior in that case be that all unbiased trajectories end up in the closed state, or at least travel a substantial amount in that direction? However, that is not observed. This should be further investigated.

Second, "This suggests that stabilization of the partially open state by the removal of bound lipids can explain the increase in open probability" is an odd statement, as "stabilization of the partially open state" means almost the same as "increase in open probability".

The statement "both force fields yield inactivation barriers that are orders of magnitude lower than what is expected from electrophysiology experiments" seems inaccurate. Perhaps the authors mean "inactivation rates that are orders of magnitude lower" rather than barriers?

In addition, the assertion "The CHARMM force field, on the other hand, results in landscapes in agreement with the fact that one of the dominant states in activating conditions is the partially open state, as revealed by a combination of ssNMR+MD." seems to hold for the AMBER force field without PG lipids rather than for CHARMM?

Together with the higher barrier towards the inactivated state as well as covering most known x-ray structures along the inactivation pathway, this would seem to point all in the direction that the studied AMBER force field provides a more faithful picture of the inactivation pathway than CHARMM. I, therefore, find the somewhat inconclusive summary as presented in Fig. 5 a bit uninformative, as it suggests that both mechanisms might be equally likely.

Overall, the study would benefit from a follow-up step to become more conclusive. This could be either in the form of the suggested L81 mutation or changing the simulation conditions to inactivating conditions such as low salt, in which case the inactivated state would be expected to become a minimum, which would provide an additional reference point for validation. Either of these would narrow down the spectrum of possible mechanisms.

Reviewer #3 (Public Review):

The computational study reported in the manuscript "Free energy landscapes of KcsA inactivation" by Pérez-Conesa and Delemotte is quite interesting and insightful.

The computations provide the first complete analysis of how the opening of the activation gate and the constriction of the selectivity filter are coupled in the KcsA channel.

The analysis is careful and is state-of-the-art. The results reveal remarkable differences between the CHARMM and AMBER force fields.

Unfortunately, the "elephant in the room" with regards to K+ channel inactivation is the significance of the dilated structures more recently obtained by Xray and EM. While it is worthwhile doing our best to really understand the constriction mechanism of KcsA, and the present manuscript does an excellent job at that, the ground has shifted and understanding finer points about KcsA constriction has become, unfortunately, not the most prominent issue in the field at the present time.

Let's discuss the current situation about the inactivation of K+ channels. The situation is fairly unsettled. The KcsA channel was the first for which some atomic structure and mechanism, centered on a constriction of the selectivity filter, were proposed. The constricted conformation really does not conduct because the filter is too narrow. More recently a few structures (Xray and EM) for channel mutants known to have more propensity to inactivate have revealed a different conformation of the filter which appears to be dilated toward the extracellular side. This is a conformation that had never been seen previously. Different "camps" co-exist in the K+ channel community about inactivation. Those who were very skeptical about the constricted conformation claim that the new dilated structures is the final truth. While the dilated structures are certainly part of the body of information that we have now, but their significance remains somewhat unclear if anything because of the fact that they are not perfectly occluded and they allow ion conduction! While it is worthwhile doing our best to really understand the constriction mechanism of KcsA, and the present manuscript does an excellent job at that, the ground has shifted and understanding finer points about KcsA constriction has become, unfortunately, not the most prominent issue in the field at the present time.

Public Review:

The primary goal of this paper is to examine microtubule detyrosination as a potential therapeutic target for axon regeneration. Using dimethylamino-parthenolide (DMAPT), this study extensively examines mechanistic links between microtubule detyrosination, hyper-interleukin-6 (hIL-6), and PTEN in neurite outgrowth in retinal ganglion cells in vitro. These findings provide convincing evidence that parthenolide has a synergistic effect on hIL-6- and PTEN-related mechanisms of neurite outgrowth in vitro. The potential efficacy of systemic DMAPT treatment to promote axon<br /> regeneration in mouse models of optic nerve crush and spinal cord injury was also examined.

Strengths:

1) The examination of synergistic activities between parthenolide, hyperIL-6, and PTEN knockout is leveraged not only for potential therapeutic value, but also to validate and delineate mechanism of action.

2) The in vitro studies utilize a multi-level approach that combines cell biology and biochemistry approaches to dissect the mechanistic link from parthenolide to microtubule dynamics.

3) The studies provide a basis for others to test the role of DMAPT in other settings, particularly in the context of other effective pro-regenerative approaches.

Weaknesses:

1) In vivo studies are limited to select outcomes of recovery and do not validate or address mechanism of action in vivo.

2) Known activities of DMAPT beyond microtubule detyrosination, such as oxidative stress, mitochondrial function and NFkB inhibition, are not considered in experimental examinations or in the interpretation of findings.

Reviewer #1 (Public Review):

Using the colon transcriptomes of 52 BXD mouse strains fed either chow or a high-fat diet (HFD), Li et al. present their findings on gene-by-environment interactions underpinning inflammation and inflammatory bowel disease (IBD). They discovered modules that are enriched for IBD-dysregulated genes using co-expression gene networks. They determined Muc4 and Epha6 to be the leading candidates causing variations in HFD-driven intestinal inflammation by using systems genetics in the mouse and integration with external human datasets. In their analysis, they concluded that their strategy "enabled the prioritization of modulators of IBD susceptibility that were generalizable to the human situation and may have clinical value." This dataset is intriguing and generates hypotheses that will be investigated in the future. However, there were no mechanistic or causation-focused investigations; the results were primarily observational and correlative.

Reviewer #2 (Public Review):

In this paper, the authors seek to identify genes that contribute to gut inflammation by capitalizing on deep phenotyping data in a mouse genetic reference population fed a high-fat or chow diet and then integrating it with human genetic data on gut inflammatory diseases, such as inflammatory bowel disease (IBD) and Ulcerative Colitis (UC). To achieve this the authors performed genome-wide gene expression in the colon of 52 BXD strains of mice fed either a high-fat or chow diet. From this analysis, they observed significant variation in gene expression related to inflammation among the 52 BXD strains and differential gene expression of inflammatory genes fed a high-fat diet. Overlaying this data with existing mouse and human data of inflammatory gut disease identified a significant enrichment. Using the 52 BXD strains the authors were able to identify specific subsets of strains that were susceptible and resistant to gut inflammation and analysis of gene expression within the colon of these strains was enriched with mouse and human IBD. Furthermore, analysis of cytokine levels of IL-10 and IL-15 were analyzed and found to be increased in resistant BXD strains and increased in susceptible BXD strains.

Using the colon genome-wide gene expression data from the 52 BXD strains, the authors performed gene co-expression analysis and were able to find distinct modules (clusters) of genes that correlated with mouse UC and human IBD datasets. Using the two modules, termed HFD_M28 and HFD_M9 that correlated with mouse UC and human IBD, the authors performed biological interrogation along with transcription factor binding motif analysis to identify possible transcriptional regulators of the module. Next, they performed module QTL analysis to identify potential genetic regulators of the two modules and identified a genome-wide significant QTL for the HFD_M28 on mouse chromosome 16. This QTL contained 552 protein-coding genes and through a deduction method, 27 genes were prioritized. These 27 genes were then integrated with human genetic data on IBD and two candidate genes, EPHA6 and MUC4 were prioritized.

Overall, this paper provides a framework and elegant use of data from a mouse genetic reference population coupled with human data to identify two strong candidate genes that contribute to human IBD and UC diseases. In the future, it will be interesting to perform targeted studies with EPHA6 and MUC4 and understand their role in gut inflammatory diseases.

Reviewer #1 (Public Review):

Jamge et al. sought to identify the relationships between histone variants and histone modifications in Arabidopsis by systematic genomic profiling of 13 histone variants and 12 histone modifications to define a set of "chromatin states". They find that H2A variants are key factors defining the major chromatin types (euchromatin, facultative heterochromatin, and constitutive heterochromatin) and that loss of the DDM1 chromatin remodeler leads to loss of typical constitutive heterochromatin and replacement of this state with features common to genes in euchromatin and facultative heterochromatin. This study deepens our understanding of how histone variants shape the Arabidopsis epigenome and provides a wealth of data for other researchers to explore.

Strengths:

1. The manuscript provides convincing evidence supporting the claims that: A) Arabidopsis nucleosomes are homotypic for H2A variants and heterotypic for H3 variants, B) that H3 variants are not associated with specific H2A variants, and C) H2A variants are strongly associated with specific histone post-translational modifications (PTMs) while H3 variants show no such strong associations with specific PTMs. These are important findings that contrast with previous observations in animal systems and suggest differences in plant and animal chromatin dynamics.

2. The authors also performed comprehensive epigenomic profiling of all H2A, H2B, and H3 variants and 12 histone PTMs to produce a Hidden Markov Model-based chromatin state map. These studies revealed that histone H2A variants are as important as histone PTMs in defining the various chromatin states, which is unexpected and of high significance.

3. The authors show that in ddm1 mutants, normally heterochromatic transposable element (TE) genes lose H2A.W and gain H2A.Z, along with the facultative heterochromatin and euchromatin signatures associated with H2A.Z at silent and expressed genes, respectively.

Reviewer #2 (Public Review):

Jamge et al. set out to delineate the relationship between histone variants, histone modifications and chromatin states in Arabidopsis seedlings and leaves. A strength of the study is its use of multiple types of data: the authors present mass-spec, immunoblotting and ChIP-seq from histone variants and histone modifications. They confirm the association between certain marks and variants, in particular for H2A, and nicely describe the loss of constitutive heterochromatin in the ddm1 mutant.

Overall, this study nicely illustrates that, in Arabidopsis, histone variants (and H2A variants in particular) display specificity in modifications and genomic locations, and correlate with some chromatin sub-states. This encourages future work in epigenomics to consider histone variants with as much attention as histone modifications.

Reviewer #3 (Public Review):

How chromatin state is defined is an important question in the epigenetics field. Here, Jamge et al. proposed that the dynamics of histone variant exchange control the organization of histone modifications into chromatin states. They found 1) there is a tight association between H2A variants and histone modifications; 2) H2A variants are major factors that differentiate euchromatin, facultative heterochromatin, and constitutive heterochromatin; 3) the mutation in DDM1, a remodeler of H2A variants, causes the mis-assembly of chromatin states in TE region. The topic of this paper is of general interest and the results are novel.

Overall, the paper is well-written and the results are clearly presented. The biochemical analysis part is solid.

Reviewer #4 (Public Review):

This work aims at analyzing the impact of histone variants and histone modifications on chromatin states of the Arabidopsis genome. Authors claim that histone variants are as significant as histone modifications in determining chromatin states. They also study the effect of mutations in the DDM1 gene on the exchange of H2A.Z to H2A.W, which convert the silent state of transposons into a chromatin state normally found on protein coding genes.

This is an interesting and well done study on the organization of the Arabidopsis genome in different chromatin states, adding to the previous reports on this issue.

Reviewer #1 (Public Review):

In this work, Urbanska and colleagues use a machine-learning based crossing of mechanical characterisations of various cells in different states and their transcriptional profiles. Using this approach, they identify a core set of five genes that systematically vary together with the mechanical state of the cells, although not always in the same direction depending on the conditions. They show that the combined transcriptional changes in this gene set is strongly predictive of a change in the cell mechanical properties, in systems that were not used to identify the genes (a validation set). Finally, they experimentally after the expression level of one of these genes, CAV1, that codes for the caveolin 1 protein, and show that, in a variety of cellular systems and contexts, perturbations in the expression level of CAV1 also induce changes in cell mechanics, cells with lower CAV1 expression being generally softer.

Overall the approach seems accessible, sound and is well described. My personal expertise is not suited to judge its validity, novelty or relevance, so I do not make comments on that. The results it provides seem to have been thoroughly tested by the authors (using different types of mechanical characterisations of the cells) and to be robust in their predictive value. The authors also show convincingly that one of the genes they identified, CAV1, is not only correlated with the mechanical properties of cells, but also that changing its expression level affects cell mechanics. At this stage, the study appears mostly focused on the description and validation of the methodological approach, and it is hard to really understand what the results obtain really mean, the importance of the biological finding - what is this set of 5 genes doing in the context of cell mechanics? Is it really central, or is it just one of the set of knobs on which the cell plays - and it is identified by this method because it is systematically modulated but maybe, for any given context, it is not the dominant player - all these fundamental questions remain unanswered at this stage. On one hand, it means that the study might have identified an important novel module of genes in cell mechanics, but on the other hand, it also reveals that it is not yet easy to interpret the results provided by this type of novel approach.

Reviewer #2 (Public Review):

A key strength is the quantitative approaches all add rigor to what is being attempted. The approach with very different cell culture lines will in principle help identify constitutive genes that vary in a particular and predictable way. To my knowledge, one other study that should be cited posed a similar pan-tissue question using mass spectrometry proteomics instead of gene expression, and also identified a caveolae component (cavin-1, PTRF) that exhibited a trend with stiffness across all sampled tissues. The study focused instead on a nuclear lamina protein that was also perturbed in vitro and shown to follow the expected mechanical trend (Swift et al 2013).

Reviewer #3 (Public Review):

In this work, Urbanska et al. link the mechanical phenotypes of human glioblastoma cell lines and murine iPSCs to their transcriptome, and using machine learning-based network analysis identify genes with putative roles in cell mechanics regulation. The authors identify 5 target genes whose transcription creates a combinatorial marker which can predict cell stiffness in human carcinoma and breast epithelium cell lines as well as in developing mouse neurons. For one of the target genes, caveolin1 (CAV1), the authors perform knockout, knockdown, overexpression and rescue experiments in human carcinoma and breast epithelium cell lines. They determine the cell stiffness via RT-DC, AFM indentation and AFM rheology and confirm that high CAV1 expression levels correlate with increased stiffness in those model systems. This work brings forward an interesting approach to identify novel genes in an unbiased manner, but surprisingly the authors validate caveolin 1, a target gene with known roles in cell mechanics regulation.

I have two main concerns with the current version of this work:<br /> 1) The authors identify a network of 5 genes that can predict mechanics. What is the relationship between the 5 genes? If the authors aim to highlight the power of their approach by knockdown, knockout or over-expression of a single gene why choose CAV1 (which has an individual p-value of 0.16 in Fig S4)? To justify their choice, the authors claim that there is limited data supporting the direct impact of CAV1 on mechanical properties of cells but several studies have previously shown its role in for example zebrafish heart stiffness, where a knockout leads to higher stiffness (Grivas et al., Scientific Reports 2020), in cancer cells, where a knockdown leads to cell softening (Lin et al., Oncotarget 2015), or in endothelial cell, where a knockout leads to cell softening (Le Master et al., Scientific Reports 2022).<br /> 2) The authors do not show how much does PC-Corr outperforms classical co-expression network analysis or an alternative gold standard. It is worth noting that PC-Corr was previously published by the same authors to infer phenotype-associated functional network modules from omics datasets (Ciucci et al., Scientific Reports 2017).

Altogether, the authors provide an interesting approach to identify novel genes associated with cell mechanics changes, but the current version does not fulfill such potential by focusing on a single gene with known roles in cell mechanics.

Reviewer #1 (Public Review):

The authors have approached the study of the mechanism by which the two more antigenic proteins of the influenza A virus, hemagglutinin (HA) and neuraminidase (NA), are expressed later during the infection. For this aim, they set an experimental approach consisting of a 2-hour-long infection at a multiplicity of infection of 2 with the viral strain WSN. They used cells from the lung carcinoma cell line A549. They used the FISH technique to detect the mRNAs in situ and developed an imaging-based assay for mathematically modeling and estimating the nuclear export rate of each of the eight viral segments. They propose that the delay in the expression of HA and NA is based on the retention of their mRNA within the nucleus.

The main strength of this work is the fact that the authors have studied a long-unaddressed mechanism in influenza A virus infectious cycle, as is the late expression of HA and NA, by creating a work flow including mRNA detection (FISH) plus mathematical calculations to arrive at a model, which additionally could be useful for general biological processes where transcription occurs in a burst-like manner. The weakness of this work in its present state is that in order to "quantify" the export rate of the transcripts, several assumptions regarding the viral infection are made without empirical data. It would greatly improve if more precise experiments could be performed and/or include demonstration of the assumptions made (i.e., synchronized infections, empirically demonstrating that cRNA production does not occur within the first 2 hours of infection, and/or separate transcription and replication, inhibiting RNA degradation during viral infection).

Reviewer #2 (Public Review):

In this study the authors developed a framework to investigate the export rates of Influenza viral RNAs translocating from the nucleus to the cytoplasm. This model suggests that the influenza virus may control gene expression at the RNA export level, namely, the retention of certain transcripts in the nucleus for longer times, allows the generation of other viral encoded proteins that are exported regularly, and only later on do certain mRNAs get exported. These encode proteins that alert the cell to the presence of viral molecules, hence keeping their emergence to very end, might help the virus to avoid detection as late as possible in the infection cycle.

The study is of limited scope. The notion that some mRNAs are retained in the nucleus after transcription is concluded early on from the FISH data. The model does not contribute much to the understanding and is mostly confirming the FISH data. The export rate is an ambiguous number and this part is not elaborated upon. One is left with more questions since no mechanistic knowledge emerges, and no additional experimentation is attempted to try drive to a deeper understanding.

Reviewer #1 (Public Review):

This study revealed that one of the mechanisms for iTreg (induced-Treg) lineage instability upon restimulation is through sustained store-operated calcium entry (SOCE), which activates transcription factor NFAT and promotes changes in chromatin accessibility to activated T cell-related genes. The authors revealed that, unlike thymus-derived Tregs (tTreg) with blunted calcium signaling and NFAT activation, iTregs respond to TCR restimulation with fully activated SOCE and NFAT similar to activated conventional T cells. Activated NFAT binds to open chromatin regions in genes related to T helper cells, increases their expression, and leads to the instability of iTreg cells. On the other hand, inhibition of the SOCE/NFAT pathway by chemical inhibitors could partially rescue the loss of Foxp3 expression in iTreg upon restimulation. The conclusion of the study is unexpected since previous studies showed that NFAT is required for Foxp3 induction and iTreg differentiation (Tone Y et al, Nat Immunol. 2008, PMID: 18157133; Vaeth M et al, PNAS, 2012, PMID: 22991461). Additionally, Foxp3 interacts with NFAT to control Treg function (Wu Y et al, Cell, 2006, PMID: 16873067). The data presented in this study demonstrated the complex role NFAT plays in the generation and stability of iTreg cells.

Several concerns are raised from the current study.<br /> 1. Previous studies showed that iTregs generated in vitro from culturing naïve T cells with TGF-b are intrinsically unstable and prone to losing Foxp3 expression due to lack of DNA demethylation in the enhancer region of the Foxp3 locus (Polansky JK et al, Eur J Immunol., 2008, PMID: 18493985). It is known that removing TGF-b from the culture media leads to rapid loss of Foxp3 expression. In the current study, TGF-b was not added to the media during iTreg restimulation, therefore, the primary cause for iTreg instability should be the lack of the positive signal provided by TGF-b. NFAT signal is secondary at best in this culturing condition.

2. It is not clear whether the NFAT pathway is unique in accelerating the loss of Foxp3 expression upon iTreg restimulation. It is also possible that enhancing T cell activation in general could promote iTreg instability. The authors could explore blocking T cell activation by inhibiting other critical pathways, such as NF-kb and c-Jun/c-Fos, to see if a similar effect could be achieved compared to CsA treatment.

3. The authors linked chromatin accessibility and increased expression of T helper cell genes to the loss of Foxp3 expression and iTreg instability. However, it is not clear how the former can lead to the latter. It is also not clear whether NFAT binds directly to the Foxp3 locus in the restimulated iTregs and inhibits Foxp3 expression.

Reviewer #2 (Public Review):

The phenotypic instability of in vitro-induced Treg cells (iTregs) has been discussed for a long time, mainly in the context of the epigenetic landscape of Treg-signature genes; e.g. Treg-specifically CpG-hypomethylated Foxp3 CNS2 enhancer region. However, it has been insufficiently understood the upstream molecular mechanisms, the particularity of intracellular signaling of natural Treg cells, and how they connect to stable/unstable suppressive function.

Huiyun Lv et al. addressed the issue of phenotypic instability of in vitro-induced regulatory T cells (iTregs), which is a different point from the physiological natural Treg cells and an obstacle to the therapeutic use of iTreg cells. The authors focused on the difference between iTreg and nTreg cells from the perspective of their control of store-operated calcium entry (SOCE)-mediated cellular signaling, and they clearly showed that the sustained SOCE signaling in iTreg and nTreg cells led to phenotypic instability. Moreover, the authors pointed the correlation between the incomplete conversion of chromatin configuration and the NFAT-mediated control of effector-type gene expression profile in iTreg cells. These findings potentially cultivate our understanding of the cellular identity of regulatory T cells and may shed light on the therapeutic use of Treg cells in many clinical contexts.

The authors demonstrated the biological contribution of Ca2+ signaling with the variable methods, which ensure the reliability of the results and the claims of the authors. iTreg cells sustained SOCE-signaling upon stimulation while natural Treg cells had lower strength and shorter duration of SOCE-signaling. The result was consistent with the previously-proposed concept; a certain range of optimal strength and duration of TCR-signaling shape the Treg generation and maintenance, and it provides us with further in-depth mechanistic understanding.

In the later section, authors found the incomplete installment of Treg-type open chromatin landscape in some effector/helper function-related gene loci in iTreg cells. These findings propose the significance to focus on not only the "Treg"-associated gene loci but also "Teffector-ness"-associated regions to determine the Treg conversion at epigenetic level.

Limitations and weaknesses;<br /> (1) Some concerns about data processing and statistic analysis.<br /> The authors did not provide sufficient information on statistical data analysis; e.g. lack of detailed descriptions about<br /> -the precise numbers of technical/biological replicates of each experiment<br /> -the method of how the authors analyze data of multiple comparisons... Student t-test alone is generally insufficient to compare multiple groups; e.g. figure 1.<br /> These inappropriate data handlings are ruining the evidence level of the precious findings.

(2) Untransparent data production; e.g. the method of Motif enrichment analysis was not provided.<br /> Thus, we should wait for the author's correction to fully evaluate the significance and reliability of the present study.

(3) Lack of evidence in human cells.<br /> I wonder whether human PBMC-derived iTreg cells are similarly regulated.

(4) NFAT regulation did not explain all of the differences between iTregs and nTregs, as the authors mentioned as a limitation.<br /> Also, it is still an open question whether NFAT can directly modulate the chromatin configuration on the effector-type gene loci, or whether NFAT exploits pre-existing open chromatin due to the incomplete conversion of Treg-type chromatin landscape in iTreg cells. The authors did not fully demonstrate that the distinct pattern of chromatin regional accessibility found in iTreg cells is the direct cause of an effector-type gene expression.

Reviewer #1 (Public Review):

Terzioglu and co-workers tested the provocative hypothesis that mitochondria maintain an internal temperature considerably higher than cytosolic/external environmental temperature due to the inherent thermodynamic inefficiency of mitochondrial oxidative phosphorylation. As a follow-up to a prior paper from some of the same authors, the goal of this study was to conduct additional experiments to assess mitochondrial temperature in cultured cells. Consistent with the prior work, the authors provide consistent evidence that the temperature of mitochondria in four different types of cultured mammalian cells, as well as cells from Drosophila (poikilotherms), is 15oC or more above the external temperature at which cells are maintained (e.g., 37oC). Additional evidence shows that mitochondria maintain higher temperatures under several different types of cellular metabolic stresses predicted to decrease the dependence on OxPhos, adding to the notion that natural thermodynamic inefficiency and heat generation may be an important, and potentially regulated, characteristic of mitochondrial metabolism.

Strengths<br /> Demonstration that both a fluorescent (Mito Thermo Yellow) and a genetic-based (mito-gTEMP) mitochondrial targeted temperature probe elicit similar quantitative changes in mitochondrial temperature under different experimental conditions is a strength. The addition of the genetic probe to the current study supports prior findings using the fluorescent probe and thus achieves a primary objective of the study.

The experiments are well-designed and executed. Specific attention given to potential artifacts affecting probe signal and/or non-specific effects from the different experimental interventions is a strength.

The use of different cultured cell lines from different organisms provides additional evidence of elevated temperature as a general property of functioning mitochondria, representing additional validation.

Weakness:<br /> While the findings and potential interpretations put forward by the authors are intriguing, the severity of the interventions (e.g., mitochondrial complex-specific inhibitors, inhibition of protein synthesis) and the absence of simultaneous or parallel measurements of other key bioenergetic parameters (i.e., membrane potential, oxygen consumption rate, etc.) limits the ability to interpret potential cause and effect - whether the thermogenesis aspect of OxPhos is being sensed and regulated, or whether temperature changes are more of a biproduct of adjustments in OxPhos flux under the experimental circumstances. In other words, the physiological relevance of the findings remains unclear.

Related, several of the interventions are employed to either increase or decrease dependence on OxPhos flux, but no outcome measures are reported to document whether the intended objective was achieved (e.g., increased OxPhos flux in low glucose plus galactose, decreased ATP demand-OxPhos flux with anisomycin, etc.).

Reviewer #2 (Public Review):

An important paper that confirms the validity of the initial findings of Chretien et al regarding the hot temperatures at which the mitochondrion is operating. There are certain gaps in the literature covered in its list of cited references and, as a consequence, in the argumentation of the paper - but these can be easily fixed.

Reviewer #3 (Public Review):

The goal of this study was to use a combination of fluorescent dyes and genetically encoded reporters to estimate the temperature of mitochondria. The authors provide additional evidence that they claim to support "hot" mitochondria.

Strengths:<br /> 1. The authors use several methods, including a mitochondrial fluorescent reporter dye, as well as a genetically encoded gTEMP temperature probe, to estimate mitochondrial temperature.<br /> 2. The authors couple these measurements with other perturbation of mitochondria, such as OXPHOS inhibitors, to show consistency

Weaknesses:<br /> 1. The methodology for inferring mitochondrial temperature is not well-established to begin with and requires additional controls for interpretation.<br /> a. Very little benchmarking is done of the "basal" fluorescence ratio, and whether that fluorescence ratio actually reflects true organelle temperature. For instance, the authors should in parallel compare between different organelles to see if only mitochondria appear "hot" or whether this is some calibration error. Another control is to use different incubator temperatures and see how mitochondrial (vs other organelle) temperature varies as a function of external temperature.<br /> b. The authors do not rigorously control for other factors that may also be changing fluorescence and may be confounders to the delta fluorescence (eg, delta calcium in response to mito inhibitors, membrane potential, redox status, ROS, etc.). There should be additional calibration for all potential confounders.<br /> c. It was unclear where the mito-targeted dyes/probes localized in terms of mitochondrial compartment. Regardless, one important control would be to target these dyes to each of the different compartments eg. Matrix vs IMS vs outer membrane to determine if a gradient of temperatures can be observed.<br /> d. Can these probes be used in isolated mitochondria and other isolated organelles. Such data would also help to clarify whether the high temperature is a specific to mitochondria.<br /> 2. The authors should try to calibrate their fluorescence inference of temperature with an alternative method and benchmark to others in the field. For instance, Okabe et al Nat Comm 2012 used a polymeric thermometer to measure temperature and reported 33degC cytoplasm and 35degC nucleus. Can the authors also show a ~2degC difference in their hands between those two compartments, and under those conditions are mitochondria still 10degC hotter?<br /> 3. There are some theoretical considerations and critiques about temperature imaging in cells (eg Baffou et al Nat Methods 2014; Lane et al Plos Biology 2018), and the possible magnitude of theoretical variation between compartments. The authors should address some of those theoretical concerns, either experimentally or in the discussion.

Based on the aforementioned weaknesses, in my opinion, the authors did not achieve their Aims to accurately determine the temperature of mitochondria. The results, while interesting, are preliminary and require additional controls before conclusions can be drawn. Previous studies have indicated intra-organelle temperature variations within cells; typically, previous reports have estimated that the variation is within a few degrees (Okabe et al Nat Comm 2012). Only one report has previously suggested that mitochondria are at 50degC (Cretien, Plos biology 2018). The study does not substantially clarify the true temperature of mitochondria or resolve potential discrepancies in previous estimates of mitochondrial temperature.

Reviewer #1 (Public Review):

This is an interesting study deploying convergent methodologies to address a timely question: can non-human primates distinguish theory of mind from random behaviours during passive viewing of animated shapes, and what brain regions are implicated? As the authors note, fMRI studies of brain activation in response to the theory of mind stimuli in non-human primates are scarce, and none have explored the processing of abstract stimuli in this context.

The major strengths of the study are the application of the Frith-Happé shapes task in a group of marmosets during fMRI in conjunction with concurrent eye tracking recording. Eye tracking is a very nice addition as it enables the authors to determine the gaze patterns and fixation duration on distinct aspects of the task stimuli (e.g., large triangle versus small triangle) as well as group differences. Overall, the study seems well-designed and technically rigorous, and the major conclusions appear to be supported by the data.

However, there is one aspect I would appreciate some clarity on, namely the failure to include the original "Goal directed condition" from the Frith-Happé task. The authors contrast visuo-oculomotor and fMRI activation between the Random (no discernible interaction or purposeful behaviour) and the ToM (goal-directed behaviours with mental interaction) but neglect the intermediate step of physical interaction between the shapes that the Goal-directed behaviour condition portrays. As such, it is difficult to make clear statements as to what the activation patterns in the ToM condition represent - perhaps this merely reflects the processing of an unfolding narrative rather than random movements.

Reviewer #2 (Public Review):

In this study, Dureux and colleagues show that marmosets are sensitive to the Frith and Happe social illusion. This result is particularly interesting from an evolutionary perspective as rhesus macaques are insensitive to this social illusion.

Although marmosets show sensitivity to the illusion of social interaction between two geometric shapes, behavioural and neuronal evidence also show differences between humans and marmosets.

Reviewer #3 (Public Review):

To assess the degree to which highly social primates like marmosets share a human-like Theory of Mind (ToM), the authors used eye tracking and functional magnetic resonance brain imaging on marmosets and humans who were viewing two of the three categories from classic Frith-Happé animations. Humans viewing the ToM animations showed, relative to the random movement animations, longer fixation times, more viewing of the large shape, and more viewing of the small shape. In contrast, the marmosets did not differ in their viewing of the ToM videos as a category and did not show differential viewing of the small shape. The marmosets did show differential viewing of the large shape, but this difference was blunted relative to that seen in humans. Neurally, both species showed widespread brain activation in many areas that discriminated between ToM videos and random movement videos. This pattern of activation partially overlapped and partially was different in humans and marmosets. It was also partially overlapping and partially different when comparing humans in this study to humans in another study. Overall, the authors conclude that their evidence cannot address whether marmosets have a Theory of Mind, but that marmosets show a "clear preference for interacting shapes" that may be an ancestral form of human Theory of Mind.

There are several laudable strengths to this report. It reports a direct human/monkey comparison. It uses a robust population of subjects, especially for the monkey experiment. It uses strong imaging methods that use modern parcellation maps, compares human data from this study to comparable data from another study, and accounts for lateralization differences convincingly using maps of signal-to-noise ratio. It uses eye-tracking methods and stimuli that are solidly grounded in the human literature and that has recently been used in a different monkey species.

Unfortunately, the weaknesses of this report limit its interpretability. First, it omits one of the three major categories of the Frith-Happé animations: Goal-Directed actions. Data from this category are critical because they provide a case where the shapes are engaging in biological motion but are not behaving as if they attribute minds to each other. Without including it, readers cannot interpret whether any given finding is due to biological motion or mentalizing. Second, the study did not gather explicit reports of mental state attribution from humans. This does not allow for a manipulation check about whether humans were even engaging in mentalizing and does not allow the researchers to separate out what brain activation patterns are due to mentalizing and which are due to eye movements or stimulus movement. Third, in interpreting the data, the researchers gloss over the major species differences and primarily focus on one small species similarity. Both this study and a previous human study (Klein et al., 2009, Quart. J. Exp. Psychol.) have shown longer fixations for the ToM videos relative to the random motion videos and that these fixations correlate with explicit ratings of the intentionality of the shapes (Klein et al., 2009). That the marmosets don't show this difference should be a major piece of evidence against the hypothesis that they are engaging in anything like mentalizing. The marmosets also failed to show a viewing difference for the small shape. In short, the small viewing difference in the large shape, itself blunted relative to that seen in humans, is not sufficient evidence to justify the conclusion that marmosets engage in anything like ToM or even that they show a "clear preference for interacting shapes". Fourth, alternative explanations for the small differences that do exist were not sufficiently explored. The videos that make up the categories in the Frith-Happé animations differ in many ways, such as in the amount of visual motion, smoothness/jerkiness of motion, amount of the screen taken up by shapes vs white space, etc. Indeed, in the prior study to use these stimuli with monkeys, the authors also found that the categories differed in viewing parameters but that this difference disappeared once low-level visual motion was accounted for (Schafroth et al., 2021, Sci. Rep.). Without a similar analysis here or a second experiment that assesses generalization to stimuli that don't differ on low-level perceptual features, readers cannot know whether the small viewing difference that exists is due to something like mentalizing or something about low-level visual motion. Indeed, other studies have found overlapping brain activity patterns in monkeys that are driven primarily by low-level visual motion (e.g., Russ et al., 2015, Neuroimage). Fifth, the prior monkey study to use these stimuli raised the point that these stimuli may not even be appropriate to test ToM in nonhumans. Human-like displays of "mocking", "coaxing", or "seducing" are likely meaningless to monkeys. This weakness has not been addressed in the current study.

Considering the weaknesses in the behavioral methods, the well-collected neural activity patterns cannot be interpreted in a meaningful way. As such, the authors' conclusions are not justified at the current time. Nevertheless, this report may be useful to others who attempt similar experiments of their own.

Reviewer #1 (Public Review):

The study of Aso and colleagues seeks to understand how learned information is steering motor output. Using an artificial training paradigm consisting of odor presentation combined with dopamine neuron activation, they identify upwind orientation as an important parameter of appetitive memory recall (as has been shown before - e.g. Handler 2019). Using the Drosophila genetic targeting library and optogenetic activation, they identify several populations of neurons responsible for upwind orientation by analyzing freely moving animals in an airflow chamber. They concentrate on a specific subset, which they call upwind neurons (UPWINs), and which they can anatomically link downstream to the flies' memory center, the mushroom body (MB), building on the ultrastructural connectome brain atlas. In combination with electrophysiology, in-vivo calcium imaging, and memory assays, they successfully show that (1) UPWINs promote upwind orientation including acceleration of angular speed and bias turning towards the upwind direction, (2) UPWINs receive excitatory and inhibitory input from specific parts of the MB, (3) UPWINs increase odor-evoked activity upon (artificial) appetitive training and (4) appetitive memory recall is impaired when blocking UPWIN neurons only during the memory test.

The authors use state-of-the-art techniques combining tools like optogenetics, connectome analysis as well as electrophysiology, in-vivo calcium imaging, and memory/behavioral assays tracking individual flies. It provides new insights into mushroom body memory retrieval circuits and how they integrate with information from other brain areas. However, some concerns remain regarding some claims of the paper. The timeline of the behavioral and the physiological experiments differ. It is therefore difficult to define the memory phases when upwind orientation is important for recall. Moreover, one main conclusion the authors draw from their data is that upwind orientation is promoted by disinhibition from a specific MB output connection, however, physiological evidence of this effect is missing. The UPWINs seem to have a more complex function in behavioral control beyond memory recall. The fact that optogenetic UPWIN activation is leading to upwind orientation only in starved flies together with the fact that flies show a high returning probability even without any odor present suggests a functional role in state-dependent exploration behavior.

Reviewer #2 (Public Review):

Associative learning assigns valence to sensory cues paired with reward or punishment. Brain regions such as the amygdala in mammals and the mushroom body in insects have been identified as primary sites where valence assignment takes place. However, little is known about the neural mechanisms that translate valence-specific activity in these brain regions into appropriate behavioral actions. This study identifies a small set of upwind neurons (UpWiNs) in the Drosophila brain that receive direct inputs from two mushroom body output neurons (MBONs) representing opposite valences. Through a series of behavioral, imaging, and electrophysiological experiments, the authors show that UpWiNs are differentially regulated by the two MBONs, i.e., inhibited by the glutamatergic MBON-α1(encoding negative valence) while activated by the cholinergic MBON-α3 (encoding positive valence). They also show that UpWiNs control the wind-directed behavior of flies. Activation of UpWiNs is sufficient to drive flies to orient and move upwind, and inhibition of UpWiNs reduces flies' upwind movement toward the source of reward-predicting odors (CS+). These results, together with existing knowledge about the function of the mushroom body in memory processing, suggest an appealing model in which reward learning decreases and increases the responses of MBON-α1 and MBON-α3 to the CS+ odor, respectively, and these changes cause UpWiNs to respond more strongly to the CS+ odor and drive upwind locomotion. Interestingly, in the final part of the results, the authors reveal a wind-independent function of UpWiNs: increasing the probability that flies will revisit the site where UpWiNs were activated. Thus, UpWiNs guide learned reward-seeking behavior with and without airflow. Although the mushroom body has been extensively studied for its role in learning and memory, the downstream neural circuits that read the information from the mushroom body to guide memory-driven behaviors remain poorly characterized. This study provides an important piece of the puzzle for this knowledge gap.

Strength

1. Memory studies have predominantly relied on binary choice (go or no-go) assays as measures of memory performance. While these assays are convenient and efficient, they fall short of providing a comprehensive understanding of underlying behavioral structures. In an effort to overcome this limitation, the current study used video recording and tracking software to delve deeper into memory-guided behavior. This innovative approach allowed the authors to uncover novel neurons and examine their contribution to behavior with a level of detail not possible with binary choice assays.

2. This study used electron microscopy-based Drosophila hemibrain connectome data to reveal the synaptic connection between UpWiNs and MBON-α1 and MBON-α3. Using this method, the study shows that a single UpWiN receives direct input from both MBON-α1 and MBON- α3, which is confirmed by a functional imaging experiment. The connectome dataset also reveals several neurons downstream of UpWiNs, opening avenues for further research into the neural mechanisms linking memory and behavior.

Weakness

1. The authors repeatedly state in the manuscript that MBON-α1 and MBON-α3 convey appetitive or aversive memories, respectively. This assertion may not be entirely accurate. Evidence from sugar reward conditioning experiments suggests that MBON-α3 is potentiated and required for sugar reward memory retrieval. Therefore, the compartmentalization for appetitive and aversive memories appears not as obvious at the level of MBONs.

2. This study did not conclusively establish the importance of the MBON-α1/α3 to UpWiN pathways in memory-driven behavior. In the experiments shown in Figure 5, flies were trained to associate the activation of reward-related DANs with a specific odor (CS+). After conditioning, UpWiNs were observed to show enhanced responses to the CS+ odor. However, the results should be interpreted with caution because the driver line used to activate DANs (R58E02-LexAp65) labels not only DANs projecting to the MBON-α1 compartment, but all DANs in the protocerebral anterior medial (PAM) cluster. Thus, it remains unclear to what extent the observed enhanced responses are influenced by changes in inhibitory inputs from MBON-α1. While UpWiNs have been shown to play a critical role in the expression of sugar reward memory (Figure 7), it should be noted that UpWiNs receive inputs from multiple upstream neurons, making it difficult to accurately assess the contribution of MBON-α1/α3 to UpWiN pathways in UpWiN recruitment. Further research is needed to fully address this issue.

3. UpWind neurons (UpWiNs) were so named because their activation promotes upwind locomotion. However, when activated in the absence of airflow, flies show increased locomotor speed and an increased probability of revisiting the same location (Figure 7 and Figure 7-figure supplement 1). The revisiting behavior can be observed during the activation of UpWiNs, which is distinct from the local search behavior that typically begins after a reward stimulus is turned off (e.g., Gr64f-GAL4 results in Figure 7-figure supplement 1). Because revisiting a location can also be a consequence of repeated turns, it seems more accurate to describe UpWiNs as controlling the speed and likelihood of turns and promoting upwind movement by integrating with neurons that sense the direction of airflow.

Reviewer #3 (Public Review):

Aso et al. provide insight into how learned valences are transformed into concrete memory-driven actions, using a diverse set of proven techniques.

Here the authors use a four-armed arena to evaluate flies' preference for a reward-predicting odor and measure upwind locomotion. This behavioral paradigm was combined with the photoactivation of different memory-eliciting neurons, revealing that appetitive memories stored in different compartments of the mushroom bodies (center of olfactory memory) induce different levels of upwind locomotion. The authors then proceed to a non-exhaustive optogenetic screen of the neurons located downstream of the output neurons of the mushroom bodies (MBONs) and identify a group of 8-11 Cholinergic neurons promoting significant changes in upwind locomotion, the UpWins. By combining confocal immunolabelling of these neurons with electron microscope images, they manage to establish the UpWins' connectome within themselves and with the MBONs. Then, using two in vivo cell recording techniques, electrophysiology, and calcium imaging, they define that UpWins integrate both inhibitory and excitatory synaptic inputs from the MBONs encoding appetitive and aversive memory, respectively. In addition, they show that the UpWins' response to a reward-predicting odor is increased after appetitive training. On a behavioral level, the authors establish that the UpWins respond to wind direction only and are not involved in lower-level motor parameters, such as turning direction and acceleration. Finally, they demonstrate that the UpWins' activity is necessary for long-term appetitive memory retrieval, and even suggest a broader role for the UpWins in olfactory navigation, as their photoactivation increases the probability of revisiting behavior. In the end, the authors state that they provide new insights into how memory is translated into concrete behavior, which is fully supported by their data. Altogether, the authors present a pretty complete study that provides very interesting and reliable data, and that opens a new field of investigation into memory-driven behaviors.

Strengths of the study:

- To support their conclusions, the authors provide detailed data from different levels of analysis (behavioral, cellular, and molecular), using multiple sophisticated techniques.

- The measurement of multiple parameters in the behavioral analysis supports the strong changes in upwind locomotion. In addition, taken individually these parameters provide precise insights into how upwind locomotion changes, and allow the authors to more precisely define the role of the UpWins.

- The authors use split-Gal4 drivers instead of Gal4, allowing them to better refine neuron labelling.

The authors discussed and investigated all possible biases, making their data very reliable. For example, they demonstrated that the phenotypes observed in the behavioral assay were wind-directed behaviors and could not be explained by bias avoidance of the arena's center area.

Limitations of the study:

- In the absence of more precise drivers, the UpWins' labelling lacks precision. For example, there is no way to know exactly which UpWin is responding in the electrophysiological experiment presented in Figure 4.

- The screening of neurons located downstream of the MBONs is not exhaustive, meaning that other groups of neurons might be involved in memory-driven upwind locomotion. Although, it does not diminish the authors' conclusions.

- All data were obtained with walking flies. So far, there have been no experiments on flying flies.

Reviewer #1 (Public Review):

The authors present a PyTorch-based simulator for prosthetic vision. The model takes in the anatomical location of a visual cortical prostheses as well as a series of electrical stimuli to be applied to each electrode, and outputs the resulting phosphenes. To demonstrate the usefulness of the simulator, the paper reproduces psychometric curves from the literature and uses the simulator in the loop to learn optimized stimuli.

One of the major strengths of the paper is its modeling work - the authors make good use of existing knowledge about retinotopic maps and psychometric curves that describe phosphene appearance in response to single-electrode stimulation. Using PyTorch as a backbone is another strength, as it allows for GPU integration and seamless integration with common deep learning models. This work is likely to be impactful for the field of sight restoration.

However, one of the major weaknesses of the paper is its model validation - while some results seem to be presented for data the model was fit on (as opposed to held-out test data), other results lack quantitative metrics and a comparison to a baseline ("null hypothesis") model.<br /> - On the one hand, it appears that the data presented in Figs. 3-5 was used to fit some of the open parameters of the model, as mentioned in Subsection G of the Methods. Hence it is misleading to present these as model "predictions", which are typically presented for held-out test data to demonstrate a model's ability to generalize. Instead, this is more of a descriptive model than a predictive one, and its ability to generalize to new patients remains yet to be demonstrated.<br /> - On the other hand, the results presented in Fig. 8 as part of the end-to-end learning process are not accompanied by any sorts of quantitative metrics or comparison to a baseline model. The results seem to assume that all phosphenes are small Gaussian blobs, and that these phosphenes combine linearly when multiple electrodes are stimulated. Both assumptions are frequently challenged by the field. For all these reasons, it is challenging to assess the potential and practical utility of this approach as well as get a sense of its limitations.

Another weakness of the paper is the term "biologically plausible", which appears throughout the manuscript but is not clearly defined. In its current form, it is not clear what makes this simulator "biologically plausible" - it certainly contains a retinotopic map and is fit on psychophysical data, but it does not seem to contain any other "biological" detail. In fact, for the most part the paper seems to ignore the fact that implanting a prosthesis in one cerebral hemisphere will produce phosphenes that are restricted to one half of the visual field. Yet Figures 6 and 8 present phosphenes that seemingly appear in both hemifields. I do not find this very "biologically plausible".

Reviewer #2 (Public Review):

Van der Grinten and De Ruyter van Steveninck et al. present a design for simulating cortical-visual-prosthesis phosphenes that emphasizes features important for optimizing the use of such prostheses. The characteristics of simulated individual phosphenes were shown to agree well with data published from the use of cortical visual prostheses in humans. By ensuring that functions used to generate the simulations were differentiable, the authors permitted and demonstrated integration of the simulations into deep-learning algorithms. In concept, such algorithms could thereby identify parameters for translating images or videos into stimulation sequences that would be most effective for artificial vision. There are, however, limitations to the simulation that will limit its applicability to current prostheses.

The verification of how phosphenes are simulated for individual electrodes is very compelling. Visual-prosthesis simulations often do ignore the physiologic foundation underlying the generation of phosphenes. The authors' simulation takes into account how stimulation parameters contribute to phosphene appearance and show how that relationship can fit data from actual implanted volunteers. This provides an excellent foundation for determining optimal stimulation parameters with reasonable confidence in how parameter selections will affect individual-electrode phosphenes.

Issues with the applicability and reliability of the simulation are detailed below:

1) The utility of this simulation design, as described, unfortunately breaks down beyond the scope of individual electrodes. To model the simultaneous activation of multiple electrodes, the authors' design linearly adds individual-electrode phosphenes together. This produces relatively clean collections of dots that one could think of as pixels in a crude digital display. Modeling phosphenes in such a way assumes that each electrode and the network it activates operate independently of other electrodes and their neuronal targets. Unfortunately, as the authors acknowledge and as noted in the studies they used to fit and verify individual-electrode phosphene characteristics, simultaneous stimulation of multiple electrodes often obscures features of individual-electrode phosphenes and can produce unexpected phosphene patterns. This simulation does not reflect these nonlinearities in how electrode activations combine. Nonlinearities in electrode combinations can be as subtle the phosphenes becoming brighter while still remaining distinct, or as problematic as generating only a single small phosphene that is indistinguishable from the activation of a subset of the electrodes activated, or that of a single electrode.

If a visual prosthesis happens to generate some phosphenes that can be elicited independently, a simulator of this type could perhaps be used by processing stimulation from independent groups of electrodes and adding their phosphenes together in the visual field.

2) Verification of how the simulation renders individual phosphenes based on stimulation parameters is an important step in confirming agreement between the simulation and the function of implanted devices. That verification was well demonstrated. The end use a visual-prosthesis simulation, however, would likely not be optimizing just the appearance of phosphenes, but predicting and optimizing functional performance in visual tasks. Investigating whether this simulator can suggest visual-task performance, either with sighted volunteers or a decoder model, that is similar to published task performance from visual-prosthesis implantees would be a necessary step for true validation.

3) A feature of this simulation is being able to convert stimulation of V1 to phosphenes in the visual field. If used, this feature would likely only be able to simulate a subset of phosphenes generated by a prosthesis. Much of V1 is buried within the calcarine sulcus, and electrode placement within the calcarine sulcus is not currently feasible. As a result, stimulation of visual cortex typically involves combinations of the limited portions of V1 that lie outside the sulcus and higher visual areas, such as V2.

Reviewer #3 (Public Review):

The authors are presenting a new simulation for artificial vision that incorporates many recent advances in our understanding of the neural response to electrical stimulation, specifically within the field of visual prosthetics. The authors succeed in integrating multiple results from other researchers on aspects of V1 response to electrical stimulation to create a system that more accurately models V1 activation in a visual prosthesis than other simulators. The authors then attempt to demonstrate the value of such a system by adding a decoding stage and using machine-learning techniques to optimize the system to various configurations. While there is merit to being able to apply various constraints (such as maximum current levels) and have the system attempt to find a solution that maximizes recoverable information, the interpretability of such encodings to a hypothetical recipient of such a system is not addressed. The authors demonstrate that they are able to recapitulate various standard encodings through this automated mechanism, but the advantages to using it as opposed to mechanisms that directly detect and encode, e.g., edges, are insufficiently justified. The authors make a few mistakes in their interpretation of biological mechanisms, and the introduction lacks appropriate depth of review of existing literature, giving the reader the mistaken impression that this is simulator is the only attempt ever made at biologically plausible simulation, rather than merely the most recent refinement that builds on decades of work across the field. The authors have importantly not included gaze position compensation which adds more complexity than the authors suggest it would, and also means the simulator lacks a basic, fundamental feature that strongly limits it utility. Finally, the computational capacity required to run the described system is substantial and is not one that would plausibly be used as part of an actual device, suggesting that there may be difficulties with converting results from this simulator to an implantable system. With all of that said, the results do represent an advance, and one that could have wider impact if the authors were to reduce the computational requirements, and add gaze correction.

Review #1 Public Review:

This is an interesting study which attempts to assess the effect of the pandemic on diagnoses of pancreatic cancer. The authors have used a large national database to evaluate this, however, it should be noted that this database only captures 40% of the population in England. The authors have looked at specific parameters including Body Mass Index (BMI) as well as markers of diabetes and liver function. Only BMI had a difference in the frequency of measurements during the pandemic, presumably due to reduced face-to-face visits to allow weight and height to be captured.

Interestingly the authors noticed a reduction in surgery for pancreatic cancer by 25%, yet reported that there were no differences in the frequency of death within 6 months following the diagnosis of pancreatic cancer. The reduction in surgery is likely related at least in part to the loss of operating lists due to pandemic restrictions, however, this paper is not equipped to address another important possibility behind this, which is that pancreatic cancers were presenting too late for surgical intervention. It is not sufficient to comment that pancreatic cancer treatment was not affected by the pandemic based on the data presented on deaths within 6 months of the diagnosis of pancreatic cancer alone, as the median survival of patients diagnosed with pancreatic cancer within the pandemic has not been captured and compared to that of patients diagnosed in the preceding 5 years.

Therefore while the study can conclude no difference in pancreatic cancer diagnoses before and during the pandemic, more work needs to be done to truly assess if the pandemic had any effect on the outcomes from pancreatic cancer for patients diagnosed within this timeframe.

Reviewer #1 (Public Review):

This research aimed to discern the pattern of methylation changes that occur during aging, distinguishing between a unified specific mechanism and stochastic changes. To date, no unified hypothesis exists to guide our understanding of the changes in chromatin geography observed during the aging of cells. This work analysed six different types of purified blood-borne white blood cells allowing comparison across different immune cell subsets to determine if similar patterns occurred in all cell populations. Intriguingly, each subset exhibited its own distinct differential methylation rather than a single program. However, a core set of gene changes close to age-associated CpGs was identified suggesting that a central program existed, but that individual cell type function and metabolism shaped the overall chromatin landscape for the population. These findings establish a new framework for considering the aging process and open new questions about how the individual clocks of different populations might be regulated. While circulating cells are readily accessible for evaluation in humans, the majority of immune cells that regulate immune homeostasis are found within the tissues of the body. Whether these cells exhibit a similar profile to circulating cells or are rather shaped by their tissue or organ-specific ecosystem remains to be determined. In this setting, these tissue-resident cells are exposed to very different oxygen tensions and metabolic substrates. Furthermore, genes identified have been associated with aging, they concurrently appear to be associated with inflammation, thus it is not clear whether aging and low-grade inflammation are inherently linked, or whether these two pathways can be segregated. Thus a number of questions remain warranting further investigation.

Reviewer #2 (Public Review):

The authors utilized publicly available datasets to investigate age-related DNA methylation changes in six immune cell types. They identified 350 differentially methylated sites that were changing in the same directions among all cell types, while most of the differentially methylated sites were cell type-specific during aging. Further analyses of enriched pathways and motifs indicate that these DNA methylation changes may be induced by the fluctuations in oxygen availability.

Analyzing cell type-specific DNA methylation data and comparing cross-sectional and longitudinal datasets, the authors are able to identify age-associated DNA methylation sites that may be regulated by a common mechanism in aging. However, sex differences should be considered, and the proposed mechanism could spur future studies to test it.

Reviewer #3 (Public Review):

In this study, titled "Epigenetic signature of human immune aging: the GESTALT study," the authors reanalysed data from five highly purified human immune cell types from 55 healthy volunteers across a wide age range to characterize age-related changes in DNA methylation status. Additionally, they performed some integrative analyses with chromatin state and transcriptional data. Findings support that age-related DNA methylation changes are predominantly cell type-specific. Out of thousands of age-associated sites, only 350 sites were differentially methylated in the same direction in all cell types and validated in an independent longitudinal cohort. Some conserved changes exist, which appear to be underpinned by alterations in the hypoxia response, with linked enrichment of transcription factor binding motifs related to ARNT and REST. The authors conclude that DNA methylation changes in healthy aging may represent adaptive responses to fluctuations in oxygen availability.

Strengths:

- The study utilised data from a large cohort of individuals (n=55), with participants ranging in age from their 20s to 80s, providing a comprehensive age-related analysis.

- The data set reanalysed was based on highly purified cells rather than unfractionated PBMCs. This revealed the largely cell-type-specific nature of these changes and demonstrated that conflicting directional changes can cancel each other out, going undetected at the PBMC level.

- The authors were able to verify the DNA methylation changes that were conserved across cell types longitudinally in PBMCs by reanalyzing published datasets from the InCHIANTI study, adding robustness to their findings.

Weaknesses:

- The authors make statements in the abstract and manuscript that overreach the study's findings. Specifically, they claim that "DNA methylation changes in healthy aging may represent adaptive responses to fluctuations in oxygen availability." In reality, the study shows that a small minority of conserved DNA methylation changes across hematopoietic cell types appear to be driven by hypoxia response processes. The study does not demonstrate that hypoxia response processes account for a large proportion of DNA methylation changes or that these processes apply to non-hematopoietic cell types. These statements should be put into context relative to the study findings.

- The authors should make it clear in the introduction and methods section that this current study is merely reanalysing a data set they published before. Also, the authors should describe in the introduction the key findings of the initial analysis as presented in their 2021 Immunity publication.

- In some instances, the manuscript lacks citations to support claims.

Reviewer #1 (Public Review):

The authors convincingly show in this study the effects of the fas5 gene on changes in the CHC profile and the importance of these changes toward sexual attractiveness.

The main strength of this study lies in its holistic approach (from genes to behaviour) showing a full and convincing picture of the stated conclusions. The authors succeeded in putting a very interdisciplinary set of experiments together to support the main claims of this manuscript.

The main weakness stems from the lack of transparency behind the statistical analyses conducted in the study. Detailed statistical results are never mentioned in the text, nor is it always clear what was compared to what. I also believe that some tests that were conducted are not adequate for the given data. I am therefore unable to properly assess the significance of the results from the presented information. Nevertheless, the graphical representations are convincing enough for me to believe that a revision of the statistics would not significantly affect the main conclusions of this manuscript.

The second major problem I had with the study was how it brushes over the somewhat contradicting results they found in males (Fig S2). These are only mentioned twice in the main text and in both cases as being "similarly affected", even though their own stats seem to indicate otherwise for many of the analysed compound groups. This also should affect the main conclusion concerning the effects of fas5 genes in the discussion, a more careful wording when interpreting the results is therefore necessary.

Reviewer #2 (Public Review):

Insects have long been known to use cuticular hydrocarbons for communication. While the general pathways for hydrocarbon synthesis have been worked out, their specificity and in particular the specificity of the different enzymes involved is surprisingly little understood. Here, the authors convincingly demonstrate that a single fatty acid synthase gene is responsible for a shift in the positions of methyl groups across the entire alkane spectrum of a wasp, and that the wasps males recognize females specifically based on these methyl group positions. The strength of the study is the combination of gene expression manipulations with behavioural observations evaluating the effect of the associated changes in the cuticular hydrocarbon profiles. The authors make sure that the behavioural effect is indeed due to the chemical changes by not only testing life animals, but also dead animals and corpses with manipulated cuticular hydrocarbons.

I find the evidence that the hydrocarbon changes do not affect survival and desiccation resistance less convincing (due to the limited set of conditions and relatively small sample size), but the data presented are certainly congruent with the idea that the methyl alkane changes do not have large effects on desiccation.

Reviewer #3 (Public Review):

In this manuscript, the authors are aiming to demonstrate that a fatty-acyl synthase gene (fas5) is involved in the composition of the blend of surface hydrocarbons of a parasitoid wasp and that it affects the sexual attractiveness of females for males. Overall, the manuscript reads very well, it is very streamlined, and the authors' claims are mostly supported by their experiments and observations. However, I find that some experiments, information and/or discussion are absent to assess how the effects they observe are, at least in part, not due to other factors than fas5 and the methyl-branched (MB) alkanes. I'm also wondering if what the authors observe is only a change in the sexual attractiveness of females and not related to species recognition as well.

The authors explore the function of cuticular hydrocarbons (CHCs) and a fatty-acyl synthase in Nasonia vitripennis, a parasitic wasp. Using RNAi, they successfully knockdown the expression of the fas5 gene in wasps. The authors do not justify their choice of fatty-acyl synthase candidate gene. It would have been interesting to know if that is one of many genes they studied or if there was some evidence that drove them to focus their interest in fas5. The authors observe large changes in the cuticular hydrocarbons (CHC) profile of male and females. These changes are mostly a reduction of some MB alkanes and an increase in others as well as an increase of n-alkene in fas5 knockdown females. For males fas5 knockdowns, the overall quantity of CHC is increased and consequently, multiple types of compounds are increased compared to wild-type, with only one compound appearing to decrease compared to wild-type. Insects are known to rely on ratios of compounds in blends to recognize odors. Authors address this by showing a plot of the relative ratios, but it seems to me that they do show statistical tests of those changes in the proportions of the different types of compounds. In the results section, the authors give percentages while referring to figures showing the absolute amount of CHCs. They should also test if the ratios are significantly different or not between experimental conditions. Similar data should be displayed for the males as well. Furthermore, the authors didn't use an internal standard to measure the quantity of CHCs in the extracts, which, to me, is the gold standard in the field. If I understood correctly, the authors check the abundance measured for known quantities of n-alkanes. I'm sure this method is fine, but I would have liked to be reassured that the quantities measured through this method are good by either testing some samples with an internal standard, or referring to work that demonstrates that this method is always accurate to assess the quantities of CHC in extracts of known volumes.

The authors provide a sensible control for their RNAi experiments: targeting an unrelated gene, absent in N. vitripennis (the GFP). This allows us to see if the injection of RNAi might affect CHC profiles, which it appears to do in some cases in males, but not in females. The authors also show to the reader that their RNAi experiments do reduce the expression of the target gene. However, one of the caveats of their experiments, is that the authors don't provide evidence or information to allow the (non-expert) reader to assess whether the fas5 RNAi experiments did affect the expression of other fatty-acyl synthase genes. I'm not an expert in RNAi, so maybe this suggestion is not relevant, but it should, at least, be addressed somewhere in the manuscript that such off-target effects are very unlikely or impossible, in that case, or more generally.

The authors observe that the modified CHCs profiles of RNAi females reduce courtship and copulation attempts, but not antennation, by males toward live and (dead) dummy females. They show that the MB alkanes of the CHC profile are sufficient to elicit sexual behaviors from males towards dummy females and that the same fraction from extracts of fas5 knockdown females does so significantly less. From the previous data, it seems that dummy females with fas5 female's MB alkanes profile elicit more antennation than CHC-cleared dummy females, but the authors do not display data for this type of target on the figure for MB alkane behavioral experiments. Unfortunately, the authors don't present experiments testing the effect of the non-MB alkanes fractions of the CHC extracts on male behavior toward females. As such, they are not able to (and didn't) conclude that the MB-alkane is necessary to trigger the sexual behaviors of males. I believe testing this would have significantly enhanced the significance of this work. I would also have found it interesting for the authors to comment on whether they observe aggressive behavior of males towards females (live or dead) and/or whether such behavior is expected or not in inter-individual interactions in parasitoids wasps.

CHCs are used by insects to signal and/or recognize various traits of targets of interest, including species or groups of origin, fertility, etc. The authors claim that their experiments show the sexual attractiveness of females can be encoded in the specific ratio of MB alkanes. While I understand how they come to this conclusion, I am somewhat concerned. The authors very quickly discuss their results in light of the literature about the role of CHCs (and notably MB alkanes) in various recognition behaviors in Hymenoptera, including conspecific recognition. Previous work (cited by the authors) has shown that males recognize males from females using an alkene (Z9C31). As such, it remains possible that the "sexual attractiveness" of N. vitripennis females for males relies on them not being males and being from the right species as well. The authors do not address the question of whether the CHCs (and the MB alkanes in particular) of females signal their sex or their species. While I acknowledge that responding to this question is beyond the scope of this work, I also strongly believe that it should be discussed in the manuscript. Otherwise, non-specialist readers would not be able to understand what I believe is one of the points that could temper the conclusions from this work.

Reviewer #1 (Public Review):

"Melanocortin 1 receptor regulates cholesterol and bile acid metabolism in the liver" by Thapa et al. extends previous findings that MC1R global knockout mice have dysregulated lipid metabolism in APOE KO mice. The authors generated a hepatocyte-specific MC1R KO mouse to assess the hepatic effects of MC1R on the regulation of lipid metabolism. Thapa et al. go on to show that hepatic MC1R deletion leads to dyslipidemia and hepatic steatosis. The authors subsequently show that altered cholesterol homeostasis disrupts bile acid metabolism in hepatic MC1R KO mice. Finally, the authors provide data to suggest a role for AMPK in mediating the effects of MSH on hepatic cholesterol metabolism. The authors designed rigorous experiments using multiple different models (in vivo and in vitro) as well as different approaches (genetic and pharmacological).

The work described herein would have an impact on the field in multiple ways. Firstly, it demonstrates a novel metabolic role for MSH in the regulation of hepatic cholesterol metabolism. This may prove to be a viable therapeutic strategy for the treatment of dyslipidemia. Furthermore, the authors demonstrate an alternative signaling cascade elicited by MSH independent of cAMP, but rather relying on AMPK. This novel interaction between AMPK and MC1R could have more widespread implications beyond the control of hepatic cholesterol metabolism.

For the most part, the conclusions offered by the authors are supported by the data that is presented. There are, however, a number of concerns in the current version of this manuscript detailed below:

1) The authors demonstrate the expression of MC1R in hepatocytes through IHC staining and western blot analysis. Furthermore, the authors show an alteration in systemic bile acid homeostasis in MC1R KO mice. However, no mention of MC1R expression or function in cholangiocytes is discussed. This is important to assess both experimentally and within the discussion given the profound role of the biliary epithelium in modulating bile acid homeostasis. Furthermore, in figure 1 the authors validate the MC1R knockdown only through mRNA expression. Given panels A and C of figure 1 shows there is clearly a functional antibody for MC1R, validation of protein knockdown is needed.

2) Figure 2 demonstrates a steatotic effect of MC1R knockdown in hepatocytes. The authors attempt to provide mechanistic insight into this phenomenon through assessing the mRNA expression of genes involved in cholesterol and fatty acid synthesis. The data provided is modest at the gene level and no protein validation was provided to demonstrate functional alterations of these proteins in MC1R KO mice. Key proteins proposed such as SREBP2 and HMGCR need to be validated via a western blot of IHC analysis.

4) The authors suggest the involvement of AMPK in mediating the cholesterol-lowering effects of MSH. However, MSH is still able to lower free cholesterol levels even in the presence of an AMPK inhibitor. This suggests that MSH does not in fact rely on the activation of AMPK to elicit these cholesterol-lowering effects. The authors' conclusions are stronger than the actual data support. Furthermore, the authors claim LD211 phenocopies the effects of MSH in the presence of an AMPK inhibitor. However, the authors only measured the phosphorylation of Akt as their outcome. This begs the question, does LD211 still lower total cholesterol in the presence of AMPK inhibitors? This experiment is essential to conclude whether or not LD211 phenocopies the effects of MSH.

5) The authors initiate the project by showing high-fat diet disrupts the expression of MC1R. However, all of the subsequent experiments in hepatic MC1R KO mice are performed under normal chow. This begs the question of what is the phenotype of the hepatic MC1R KO mice fed a high-fat diet. Does KO of MC1R in the liver exacerbate HFD-induced obesity, glucose intolerance, and dyslipidemia? Inversely, can WT mice challenged with an HFD be rescued metabolically by treatment with either MSH or LD211? Providing data along these lines of investigation will provide physiological/clinical relevance to their findings.

Reviewer #2 (Public Review):

Keshav Thapa et al. investigated the role of melanocortin 1 receptor (MC1-R) in cholesterol and bile acid metabolism in the liver. First, they observed that MC1-R is present in the mouse liver and that its expression is reduced in response to a cholesterol-rich diet. To determine the role of MC1-R in the liver, they generated hepatocyte-specific MC1-R KO mice (L-Mc1r-/-). These animals exhibited a significant increase in liver weight, lipid accumulation, triglycerides and cholesterol levels, and fibrosis in comparison with control mice. By performing liquid chromatography-mass spectrometry, the authors also found that L-Mc1r-/- mice also have fewer bile acids in the plasma and faeces, but not in the liver. In accordance with these findings, mRNA/protein expression of different genes involved in these processes were altered in L-Mc1r-/- animals.

Secondly, in an attempt to evaluate the underlying mechanisms, they measured the expression of MC1-R in HepG2 cells under different treatments (i.e., palmitic acid, LDL, and atorvastatin). Moreover, they stimulated these cells with the endogenous MC1-R agonist - MSH, where they show that this molecule decreases the free cholesterol content, whereas increasing LDL and HDL uptake, as well as recapitulates some previously observed phenotypes in the proportions of bile acids. These effects were also encountered when using a selective agonist for MC1-R (i.e., LD211), further supporting the specific role of MC1-R. Finally, some experiments indicated that -MSH evokes not one single, but multiple intracellular signalling cascades for which MC1-R activation effects might take place.

Overall, this work provides novel and interesting findings on the role of MC1-R in cholesterol and bile acid metabolism in the liver, which undoubtedly will have some crucial implications for future research. Nevertheless, some experimental details should be better explained for the correct interpretation of the data. Besides, discrepant results exist regarding the molecular mechanisms behind MC1-R action that requires additional experimentation to support the conclusions drawn.

Reviewer #1 (Public Review):

The authors aim to understand the role of clonal heterogeneity of tumors in immunogenicity of clonally expressed antigens. This is a significant problem with many basic as well as translational implications.

The strength of the manuscript lies in the novel demonstration that a poorly immunogenic tumor antigen, when paired with a stronger tumor antigen, begins to elicit significant immune response. The weakness lies in the fact that the actual mechanism of the key demonstration is never shown. There is a lot of speculation and tangential experimentation, but little actual evidence of a mechanism.

By making the key observation (mentioned in the strength section in the previous paragraph), the authors did achieve their objective albeit very partially. Their observation is based on excellent experimental tools and design. This study will stimulate further experiments in this important field.

Their key observation is somewhat reminiscent of the practice of conjugating small "non-immunogenic" antigens (such as some carbohydrates) to large protein carriers (such as serum albumin) in order to elicit strong antibody response to the weaker antigen. It is interesting to contemplate if the underlying mechanisms have any commonality.

Reviewer #1 (Public Review):

The manuscript described the mechanism of Spermidine modulation of Src kinase on IDO1, accelerating the kinetics of the reaction. Spermidine can act on the backside of the SH2 domain of Src, by the interaction of specific amino acids. Considering the important role of IDO1 in the immune response the results provide proof of principle for the development of molecules that can modulate the kinase activity and the nonenzymatic functions of Src and IDO1 at once. The conclusions of this paper are mostly well supported by data, but some aspects of figure construction and data analysis need to be improved for the sake of clarity.

Reviewer #2 (Public Review):

Src is a well-studied non-receptor protein tyrosine kinase (PTK) with broad impacts on many signal transduction pathways. In this manuscript titled, "A Back-Door Insights into the modulation of Src kinase activity by the polyamine spermidine" Rossini et al investigated the mechanism of spermidine, a natural polyamine, in regulating Src tyrosine kinase activity and complex formation with IDO1, a known Src substrate. These data show a direct binding, and an allosteric binding site in the SH2 domain of Src, for spermidine. Interestingly, the manuscript also shows spermidine bound to Src promotes binding to IDO1, as well as its phosphorylation.

Overall, the molecular glue-like property of spermidine is an interesting finding. That Src substrate binding and phosphorylation for Src substrate is regulated by natural metabolites like spermidine is also a new and interesting finding. These discoveries further strengthen the idea to develop potential allosteric modulators for Src/PTK-mediated pathways.

Reviewer #3 (Public Review):

The manuscript by Rossini et al suggests an interesting novel mechanism for the regulation of tyrosine kinase Src by spermidine. The idea is interesting and some of the data suggest that spermidine may regulate Src activity. However, the manuscript suffers from multiple major shortcomings. The mechanism proposed by the authors is not supported by their studies. Authors tend to overinterpret data and overlook critical information that is missing. Some of the data is insufficient to support the statements that the authors make. Authors tend to use confusing nomenclature without clarifications making it difficult to interpret the data. The extent of Src activation by spermidine should be carefully evaluated by comparing it to the maximum activity of constitutively active Src. Furthermore, the biological significance of this regulation is not demonstrated. Only a few overexpression data are shown.

Reviewer #1 (Public Review):

The authors examine the role of the K700E mutation in the Sf3B1 splicing factor in PDAC and report that this Sf3B1 mutation promotes PDAC by decreasing sensitivity to TGF-b resulting in decreased EMT and decreased apoptosis as a result. They propose that the Sf3b1 K700E mutant causes decreased expression of Map3K7, a known mediator of TGFb signaling and also known to be alternately spliced in other systems by the Sf3b1 K700E mutation. The role of splicing defects in cancer is relatively understudied and could identify novel targets for therapeutic intervention so this work is of potential significance. However, the data is over-interpreted in many instances and it is not clear the authors can make the claims they do based on the data shown. In particular, the data showing that decreased Map3k7 underlies the effects of the Sf3b1K700E mutant is very weak. Does over-expression of Map3k7 promote the EMT signature and induce apoptosis? Do the Map3k7 expressing organoids form tumors more effectively when transplanted into mice? Also, the novelty of the work is a concern since aberrant Map3k7 splicing due to SF3B1 mutation was seen previously in other systems. The authors also do not address the apparent conundrum of Sf3b1 K700E mutation promoting tumorigenesis despite there being less EMT which is also required for progression to metastasis in PDAC.

Major Concerns.<br /> 1. The analysis of the effect of Sf3b1K700E expression on normal pancreas and on PanINs in KC mice and PDAC in KPC mice is superficial and could be enhanced by staining for amylase, cytokeratin-19 and insulin. In particular, the data quantified in figure 1L should be accompanied by staining for CK19, Mucin5AC or some other marker of ductal transformation. Also, are any effects seen at older ages in normal mice?<br /> 2. The invasion assays used are limited and should be complemented by more routine quantification of cell migration and invasion including such assays as a scratch assay, Boyden chamber assays and use of the IncuCyte system to quantify. As it stands the image in Figure 3B is difficult to interpret since it is very poorly described in the figure legend. Additional evidence is needed to make the claims made by the authors.<br /> 3. The authors should show the actual CC3 staining quantified in Suppl. Figure 2G.<br /> 4. The graph in Figure 3L should show WT and Sf3b1K700E expressing organoids number both with and without TGF-b.

Reviewer #2 (Public Review):

The manuscript has several areas of strength; it functionally explores a mutant that is detected in a portion of pancreatic cancers; it conducts mechanistic investigation and it uses human cell lines to validate the findings based on mouse models. Some areas for improvement are described below.

1) TGF-b is known to act as a tumor suppressor early in carcinogenesis, and as a tumor promoter later. The authors should extend their analysis of mouse models to determine whether the effect of SF3B1K700E is specific to promoting initiation (e.g. more, early acinar ductal metaplasia) or faster progression of PanINs following their formation. Another way to address this could be acinar cultures, to determine whether an increased propensity to ADM exists.

2) Given that the effect of SF3B1K700E expression is more prominent in KC mice, rather than in KPC mice, the authors should explain the rationale for using the latter for RNA sequencing.

3) Given that this mutation is found in about 3% of human pancreatic cancer, it would be interesting to know whether these tumors have any unique feature, and specifically any characteristic that could be harnessed therapeutically.

4) It would be interesting to know whether this mutation mutually exclusive to other mutations affecting response to TGF-b. Further, while the data might not be widely available, it would be interesting to know whether in human patients the mutation occurs in precursor lesions (PanIN might be difficult to assess, but IPMN might be doable) or at later stages.

Reviewer #3 (Public Review):

Alternative splicing as a result of mutations in different components of the splicing machinery has been associated with a variety of cancer types, including hematological malignancies where this has been most extensively studied but also for solid tumors such as breast and pancreatic ductal adenocarcinoma (PDAC). Here the authors analyze genome sequencing data in human PDAC samples and identify a recurring mutation in the SF3B1 subunit that substitutes lysine for glutamate at residue 700 (SF3B1K700E) in PDACs. This mutation has been identified and its' molecular role in disease progression in other diseases has been studied, but the mechanism for promoting disease progression in pancreatic cancer has not been as well characterized.

To study how SF3B1K700E contributes to PDAC pathology, the authors generate a novel genetically modified mouse model of a pancreas specific SF3B1K700E mutation and explore its oncogenicity and tumor promoting potential. The authors find that SF3B1K700E is not oncogenic, but potentiates the oncogenic potential of Kras and p53 (KP) driver mutations commonly found in PDAC tumors. The authors then proceed to characterize the molecular mechanisms that might drive this phenotype. By transcriptomic analysis, the authors find KP-SF3B1K700E tumors have downregulation of epithelial-to-mesenchymal transition (EMT) genes compared to KP tumors. The cytokine TGFβ has previously been found to limit PDAC initiation and progression by causing lethal EMT in PDAC and PDAC precursor cells. Thus, the authors propose SF3B1K700E inhibition of EMT blocks the tumor suppressive activity of TGFβ and this underpins the tumor promoting role of SF3B1K700E mutation in PDAC. Consistent with this finding, SF3B1K700E mutation blocks TGFβ-induced toxicity in a variety of cell culture models of PDAC and PDAC precursor models.

Lastly, the authors seek to identify how altered splicing reduces EMT activity in PDAC cells. The authors identify misspliced genes consistent in both KP and human SF3B1K700E mutant cancer samples and find Map3k7 as one of 11 consistently misspliced genes. MAP3K7 has previously been identified as a positive regulator of EMT. Thus the authors speculated Map3k7 missplicing would lead to reduced MAP3K7 activity and a reduction EMT and that this underpins the TGFβ in SF3B1K700E mutant PDAC cells. Consistent with this, the authors find inhibition of MAP3K7 reduces TGFβ toxicity in SF3B1K700E WT cells and overexpression of MAP3K7 in SF3B1K700E mutant PDAC cells induces TGFβ toxicity. Altogether, this suggests activity of Map3k7 is responsible for altered EMT activity and TGFβ sensitivity in SF3B1K700E mutant PDAC.

Altogether, the authors generate a valuable model to study the role of a recurring splicing mutation in PDAC and provide compelling evidence that this mutation is accelerates disease. The authors then perform both: (1) an open-ended investigation of how this mutation alters PDAC cell biology where they identify altered EMT activity and (2) rigorous mechanistic studies showing suppressed EMT provides PDAC cells with resistance to TGFβ, which has previously been shown to be tumor suppressive in PDAC, suggesting a possible mechanism by which SF3B1K700E mutation is oncogenic in PDAC that future animal studies can confirm. This work generates valuable models and datasets to advance the understanding of how mutations in the splicing machinery can promote PDAC progression and suggests alternative splicing of MAP3K7 is one such possible mechanism that altered splicing promotes PDAC progression in vivo.

- One major concern about the manuscript is that the proposed mechanism by which SF3B1K700E mutation accelerates PDAC progression (MAP3K7 inhibition -> EMT inhibition -> reduced TGFb toxicity) is only tested in ex vivo culture models and there is very limited and correlative data to suggest that this is the operative mechanism by which SF3B1K700E mutant tumors are accelerated. This is especially important because of recent findings that IFNa signaling, which the authors also found to be high in SF3B1K700E mutant tumors, also promotes PDAC progression (https://www.biorxiv.org/content/10.1101/2022.06.29.497540v1). Thus, while thoroughly convinced by the rigorous ex vivo work that SF3B1K700E does lead to MAP3K7 inhibition -> EMT inhibition -> reduced TGFb toxicity, further experiments to confirm this mechanism is critical in vivo would be needed to convince me that this mechanism is critical to tumor progression in vivo. For example, would forced expression of MAP3K7 slow orthotopic KP-SF3B1K700E tumor growth while leaving IFNa signaling unperturbed?

Reviewer #1 (Public Review):

This is a nice and elegant genetic study on the role of the Sgs1 and Exo1 factors involved in long DNA resection in the mechanism of double-strand break (DSB) repair by homologous recombination (HR). Most studies have focused on the need for these two factors for the long resection of a DSB to allow efficient HR. Now, this study shows that a major role of the function of long resection mediated by Sgs1 and Exo1 is to activate the DNA damage checkpoint to allow the chromosomal mobility needed to allow the DNA ends to find a distant homologous sequence with which repair via homologous recombination.

Reviewer #2 (Public Review):

A new study by Kimble et al. examines the role of extensive resection in DNA double-strand break repair. Formation of ssDNA at DNA breaks is initiated by Mre11-Rad50-Xrs2 and followed by Exo1 or Sgs1/Dna2, which form longer ssDNA. This ssDNA is used to load recombination and DNA damage checkpoint proteins. Some studies suggested that very short ssDNA by MRX complex is sufficient for DSB repair. Here, the authors look carefully at the role of extensive resection in DSB repair by gene conversion. To address this question they have constructed a large number of new recombination assays. They find that sgs1 exo1 mutants that lack extensive resection are capable of DSB repair when recombining loci are present on a single DNA molecule and within 50 kb from each other. When the template for DSB repair is further away on the same molecule or present on a different chromosome, the repair is reduced by 5-10 folds in the absence of extensive resection. The authors present data suggesting that this defect relates to slower repair kinetics between more distant homologous sequences and the need for a Mec1-mediated DNA damage checkpoint that requires extensive resection. The role of the checkpoint response is likely not limited to simple cell cycle arrest but may also be necessary for the mobility of a broken molecule. Partial suppression of the sgs1 exo1 repair defect is accomplished by activating the checkpoint using an artificial system colocalizing checkpoint proteins on a separate chromosome. Altogether the manuscript addresses an important question, is well-written, and presents interesting data.

Reviewer #3 (Public Review):

This manuscript aims to define the importance of long-range resection for homologous recombination, a relevant and yet unanswered question in the field of genome maintenance. The data shows that long-range resection is required for interchromosomal, but not intrachromosomal, recombination is well-developed and convincing. The claim that the DNA damage checkpoint is crucial for promoting distal recombination is interesting and founded on logical rationale. However, some key points about the proposed role of checkpoint signaling and the presented results need further clarification, mainly regarding the issue of checkpoint activation status in exo1Δ sgs1Δ cells and the attempts of using forced Rad53 activation to rescue interchromosomal recombination defects. Additional experiments would help solidify the proposed model. Nonetheless, the paper establishes the importance of long-range resection for distal recombination and should be considered a significant contribution to the field.

Reviewer #3 (Public Review):

The present study presents a comprehensive exploration of the distinct impacts of Isoflurane and Ketamine on c-Fos expression throughout the brain. To understand the varying responses across individual brain regions to each anesthetic, the researchers employ principal component analysis (PCA) and c-Fos-based functional network analysis. The methodology employed in this research is both methodical and expansive. Notably, the utilization of a custom software package to align and analyze brain images for c-Fos positive cells stands out as an impressive addition to their approach. This innovative technique enables effective quantification of neural activity and enhances our understanding of how anesthetic drugs influence brain networks as a whole.

The primary novelty of this paper lies in the comparative analysis of two anesthetics, Ketamine and Isoflurane, and their respective impacts on brain-wide c-Fos expression. The study reveals the distinct pathways through which these anesthetics induce loss of consciousness. Ketamine primarily influences the cerebral cortex, while Isoflurane targets subcortical brain regions. This finding highlights the differing mechanisms of action employed by these two anesthetics-a top-down approach for Ketamine and a bottom-up mechanism for Isoflurane. Furthermore, this study uncovers commonly activated brain regions under both anesthetics, advancing our knowledge about the mechanisms underlying general anesthesia.

Reviewer #1 (Public Review):

The authors performed a comparative study of the effect of the anesthetics isoflurane and ketamine on whole-brain network activation by mapping whole-brain c-fos expression in mice. Principle component analysis on the normalized Fos density showed opposite effects of the 2 anesthetics, consistent with top-down functioning for ketamine and bottom-up functioning for isoflurane. Based on the network analysis the authors suggest that isoflurane mediates anesthesia through a bottom-up mechanism activating subcortical regions and inactivating cortical regions with the locus coeruleus being the most important region while ketamine produced anesthesia through a top-down mechanism activating the cortex and subcortical nuclei with the somatosensory cortex as the most important region. Overall they show that these two anesthetics have two opposite mechanisms to induce unconsciousness, although they also have overlapping coactivation of central sleep-wake, pain, and neuroendocrine regulating areas. This manuscript highlights some interesting findings through interesting analysis. The results are likely to have a significant impact on the field of anesthesia but also on the much larger field of neuropsychopharmacology as the tools and analyses used in this report will be useful for researchers investigating the effects of any psychoactive drugs on the brain. However, there are several issues that should be addressed to support their conclusions. The two main issues of this report are the lack of behavioral/physiological measures of the depth of anesthesia produced by ketamine/isoflurane and inadequate data analysis/interpretations for some of the results.

Strengths<br /> Comparison of two different anesthetics<br /> Use of single-cell whole-brain imaging<br /> Advanced network analysis

Weaknesses<br /> Lack of behavioral/physiological measures<br /> Interpretation of the data is sometimes confusing/unclear<br /> Some statistical tests are missing and others are not controlled for multiple comparisons

Major concerns<br /> 1. The lack of behavioral/physiological measures of the depth of anesthesia (ventilation, heart rate, blood pressure, temperature, O2, pain reflexes, etc...) combined with the lack of dose-response and the use of different routes of administration makes the data difficult to interpret. Sure, there is a clear difference in network activation between KET and ISO, but are those effects due to the depth of the anesthesia, the route of administration, and the dose used? The lack of behavioral/physiological measures prevents the identification of brain regions responsible for some of the physiological effects and different effects of anesthetics.<br /> 2. Under anesthesia there should be an overall reduction of activity, is that the case? There is no mention of significantly downregulated regions. The authors use multiple transformations of the data to interpret the results (%, PC1 values, logarithm) without much explanation or showing the full raw data in Fig 1. It would be helpful to interpret the data to compare the average fos+ neurons in each region between treatment and control for each drug.<br /> 3. I do not understand their interpretation of the PCA analyses. For instance, in Fig 2 they claim that KET is associated with PC1 while ISO is associated with PC2. Looking at the distribution of points it's clear that the KET animals are all grouped at around +2.5 on PC1 and -2.0 on PC2, this means that KET is associated with both PC1 and PC2 to a similar degree (2 to 2.5). Moreover, I'm confused about why they use PCA to represent the animals/group. PCA is a powerful technique to reduce dimensionality and identify groups of variables that may represent the same underlying construct; however, it is not the best way to identify clusters of individuals or groups.<br /> 4. The actual metric used for the first PCA is unclear, is it the FOS density in each of the regions (some of those regions are large and consist of many subregions, how does that affect the analysis) is it the %-fos, or normalized cells? The wording describing this is variable causing some confusion. How would looking at these different metrics influence the analysis?<br /> 5. Based on Fig 3 the authors concludes that ISO activates the hypothalamic regions and inhibits the cortex, however, Fig 1 shows neither an activation of the hypothalamus in the ISO nor an inhibition of the cortex when compared to home cage control. If anything it suggests the opposite.<br /> 6. Control for isoflurane should be air in the induction chamber rather than home cage. It is possible that Fos activation reflects handling/stress pre-anesthesia in the animals, which would increase Fos expression in the stress-related regions such as the BST, striatum (CeA), hypothalamus (PVH) and potentially the LC.<br /> 7. In the Ket network there are a few anticorrelated regions, most of which are amongst the list of the most activated regions, does this mean that the strong correlation results from an overall decreased activation? And if so, is it possible that the ketamine anesthesia was stronger than the isoflurane, causing a more general reduction in activity?<br /> 8. Since they have established networks it would be easy and useful to look at how the different regions identified (sleep, pain, neuroendocrine, motor-related, ...) work together to maintain analgesia, are they within the same module? Do they become functionally connected and is this core network of functional connections similar for KET and ISO?<br /> 9. The naming of the function of some of the regions is very much debatable. For instance, PL/ILA are named "sleep-wakefulness regulation" regions in the paper. I can think of many more important functions of the PL/IL including executive functions, behavioral flexibility, and emotional control. It is unclear how the functions of all the regions were attributed. I am not sure that this biased labeling of structure-function is useful to the reports, it may instead suggest wrong conclusions.<br /> 10. A point of concern and confusion is the number of brain regions analyzed. In the introduction, it is mentioned that 987 brain regions are considered, but this is reduced to 53 selected brain regions in Figure 2, then 201 brain regions in Figure 3, and reduced again to 63 for the network analysis. The rationale for selecting different brain regions is not clear.<br /> 11. The statistical analysis does not seem appropriate considering the high number of comparisons. They use simple t-tests without correction for multiple comparisons.<br /> 12. There is no statistical analysis in Fig 2C,

Reviewer #2 (Public Review):

In this paper the authors aim to investigate brain-wide activation patterns following administration of the anesthetics ketamine and isoflurane, and conduct comparative analysis of these patterns to understand shared and distinct mechanisms of these two anesthetics.

To this end, they perform Fos immunohistochemistry in perfused brain section to label active nuclei, use a custom pipeline to register images to the ABA framework and quantify Fos+ nuclei, and perform multiple complementary analyses to compare activation patterns across groups.

This is an interesting line of research and a tour de force in brain-wide Fos quantification. However, there are several issues with the analysis, and overall integration that dampen my enthusiasm for the article in its current form.

Major comments:

1- The authors report 987 brain regions in the introduction, but I cannot find any analysis that incorporates these or even which regions they are. Very little rationale is provided for the regions included in any of the analyses and numbers range from 53 in Figure 1, to 201 in Figure 3, to 63 in Figure 6. It would help if the authors could first survey Fos+ counts across all regions to identify a subset that is of interest (significantly changed by either condition compared to control) for follow up analysis.

2- Different data transformations are used for each analysis. One that is especially confusing is the 'normalization' of brain regions by % of total brain activation for each animal prior to PCA analysis in Figures 2 and 3. This would obscure any global differences in activation and make it unlikely to observe decreases in activation (which I think is likely here) that could be identified using the Fos+ counts after normalizing for region size (ie. Fos+ count / mm3) which is standard practice in such Fos-based activity mapping studies. While PCA can be powerful approach to identify global patterns, the purpose of the analysis in its current form is unclear. It would be more meaningful to show that regional activation patterns (measured as counts/mm3) are on separate PCs by group.

3- Critical problem: The authors include a control group for each anesthetic (ketamine vs. saline, isofluorane vs. homecage) but most analyses do not make use of the control groups or directly compare Fos+ counts across the groups. Strictly speaking, they should have compared relative levels of induction by ketamine versus induction by isoflurane using ANOVAs. Instead, each type of induction was separate from the other. This does not account for increased variability in the ketamine versus isoflurane groups. There is no mention in the Statistics section or in Results section that any multiple comparison corrections were used. It appears that the authors only used Students t-test for each region and did not perform any corrections.

4- Figures 4 and 5 show brain regions 'significantly activated' following KET or ISO respectively, but again a subset of regions are shown and the stats seem to be t-tests with no multiple comparisons correction. It would help to show these two figures side by side, include the same regions, and keep the y axis ranges similar so the reader can easily compare the 'activation patterns' across the two treatments. Indeed, it looks like KET/Saline induced activation is an order or magnitude or two higher than ISO/Homecage. I would also recommend that this be the first data figure before any other analyses and maybe further analysis could be restricted to regions that are significantly changed in following KET or ISO here.

5- Analyses in Figure 6 and 7 are interesting but again the choice of regions to include is unclear and makes interpreting the results impossible. For example, in Figure 7 it is unclear why the list of regions in bar graphs showing Degree and Betweenness Centrality are not the same even within a single row?

Reviewer #2 (Public Review):

This represents an important study that demonstrates a high degree of heterogeneity within trailblazer cells in clusters that participate in collective migration. Solid methods highlight this heterogeneity and show that in TNBC cancers, trailblazer cells are defined by vimentin (and not Keratin 14) and are dependent on both TGFbeta and EGFR signaling. Additional, single cell studies would further support this work.

Strengths:

The paper highlights that collective migration, and the nature of trailblazer cells can be highly heterogeneous. This is important as it suggests that the ability to move between states may supersede a singular phenotype.

The paper uses animal models and organoids and in several areas attempts to correlate findings to human tissues.

The experiments are logically described.

Reviewer #1 (Public Review):

The study investigates the nature of "trailblazer" cells in distinct tumor models, including luminal B (MMTV/PyMT) and triple negative (TNBC) tumors (C3-TAg). The authors note that the trailblazer phenotypes in the TNBC model are more complex relative to the Luminal B model and represent distinct EMT programs associated with the expression of distinct EMT-TFs (Zeb1, Zeb2 and Fra-1). They demonstrated that of numerous EMT-TFs, Zeb1 and Fra-1 were required for increased cancer cell migration and invasion. They reveal that TGF-beta and EGF-mediated signaling are required for the diverse EMT states that are required for trailblazer cell activity and increased cell migration/invasion. TGF-beta signaling engaged Zeb 1 and Zeb2 while EGF signaling activated Fra-1. Indeed, inhibitors of either TGF-beta or EGF signaling could impair cell migration/invasion. While both pathways contributed to trailblazer phenotypes, EGF signaling was shown to interfere with certain TGF-beta induced transcriptional response, including the expression of genes encoding extracellular matrix proteins.

One concern was the heavy reliance of the C3-TAg as the sole TNBC model in which the distinct trailblazer phenotypes were described. The data in Fig. 3 of the submission reveals that the phenotypes observed in the C3-TAg model could be recapitulated in a TNBC patient-derived xenograft model (PDX). Using this PDX, the authors were able to show vimentin expression in lung metastatic TNBC cells that were intravascular, those that had extravasated and clusters of cancer cells fully within the lung parenchyma. This was an important addition to the manuscript. The additional experiments to investigate the role of Zeb1 and Zeb1 more fully, beyond the focus on Fra-1 in the initial submission was an additional strength of the new submission. Additional clarifications to the discussion also clarified the concepts articulated in the study. The study employs multiple breast cancer models, utilizes numerous in vitro and in vivo assessments of the trailblazer phenotypes, and the experimental design is rigorous and the interpretation of the data is sound. The manuscript will be of general interest to the research community.

Reviewer #3 (Public Review):

Cancer is a disease of many faces and in particular, the ability of cancers cells to change their phenotypes and cell behaviors - cancer cell plasticity - is a major contributor to cancer lethality and therapeutic challenge of treating this disease. In this study, Nasir, Pearson et al., investigate tumor cell plasticity through the lens of invasive heterogeneity, and in particular in models of triple-negative breast cancer (TNBC), a subtype of breast cancer with particularly poor clinical prognosis and more limited treatment modalities. Using organoid models in a variety of matrix systems, microscopy, and signaling pathway inhibitors, they find that invading TNBC breast tumors, primarily in the C31-Tag genetically engineered mouse model of TNBC, are composed of heterogeneous invasive/"trailblazer" type tumor cells that in many cases express vimentin, a classical intermediate filament marker of epithelial-mesenchymal transition, and reduced keratin-14, another filament marker of basal epithelial cells associated with collective invasion in different breast cancer models. Supportive genetic and pharmacologic evidence is provided that generation of these cells is TGF-beta signaling pathway driven, likely in vivo from the surrounding tumor microenvironment, in accord with published studies in this space. Another important aspect of this study is the good transcriptional evidence for multiple migratory states showing differing degrees of partial overlap with canonical EMT programs, dependent on TGF-beta, and suggestive but at present incomplete understanding of a parallel program involving Egfr/Fra-1 mediated effects on invasion. When taken in context with other recent studies (Grasset et al. Science Translational Medicine 2022), these data are broadly supportive of concept of targeting vimentin-dependent invasion programs in TNBC tumors.

The core conclusions of this paper are generally supported by the data, but there are some conceptual and technical considerations that should be taken into account when interpreting this study. Specific comments:

1) The contribution of the different vimentin-positive trailblazer cells to distant metastasis was not directly confirmed in vivo in this study. Given the limited proliferative potential of many fully EMT'd cells and in light of recent studies indicating that invasion can be uncoupled from metastatic potential, it seems important to directly test whether the different C31-tag isolates, varying in invasive potential in this study, produce metastases and if so do metastases abundance correlate with the invasive potential in 3D culture. The collection of lungs at 34 days post injection described in methods is too short to evaluate metastatic frequency.

2) The invasion of cancer cells is dependent on 3D matrix composition. In other studies, collective cancer invasion is performed in exclusively collagen type 1 gels or in other instances entirely in 3D reconstituted basement membrane gel, e.g. lung cancer invasion studies. In this study, the authors use a mixture composed of both matrices. Given the invasion suppressive effects of matrigel, particularly for epithelial type cells, further studies would be important to determine whether the invasion phenotypes seen in this study are generalizable across matrix environments.

3) TGF-beta is well known to induce EMT. Although this study identifies potential transcriptional mediators of the invasion/trailblazer program, is this program reversible?

Reviewer #1 (Public Review):

The goal of the manuscript is a joint analysis of genetic variation, open chromatin, and gene expression in a genetically diverse population of mouse embryonic stem cells.

This is an important manuscript that links gene expression to genetic variants and regions of open chromatin. The mechanisms of genetic gene regulation are essential to understanding how standing genetic variation translates to function and phenotype. This data set has the ability to add substantial insight into the field. In particular, the authors show how the relationships between variants, chromatin, and genes are spatially constrained by topologically associated domains.

The description of the results is hard to follow, specific terms are not well-defined, and the methods section lacks detail. Several fundamental approaches cannot be understood easily without going to references (particularly #6, #15, and #33). The manuscript will benefit from efforts to improve readability.

In addition, the CTCF binding data (ChIP-seq) gets too little attention. The fundamental question of whether regulatory domains vary between individuals is not directly addressed.

Reviewer #2 (Public Review):

The experiments described in the manuscript are well designed and executed. Most of the data presented are of high quality, convincing, and in general support the conclusions made in the manuscript. This manuscript should be of great interest to the field of mammalian gene regulation and the approaches used here can have broader applications in studying genetic and epigenetic regulations of gene expression. The key finding reported here, the importance of 3D chromatin structure in controlling gene expression, although not unexpected, offers a better understanding of the physiological roles of TADs.

Given the complexity of the data and analysis, some clarification is needed to guide readers to better understand the results.

Reviewer #1 (Public Review):

In this manuscript, the authors are building on their previous work showing Delta-Notch regulates the entrance and exit from embryo-larval quiescence of neural stem cells of the central brain (called CB neuroblasts (NB) (PMID: 35112131)). Here they show that continuous depletion of Notch in NBs from early embryogenesis leads to cycling NBs in the adult. This - cycling NBs in the adult - is not seen in controls. The assumption here is that these Notch-RNAi NBs in adults are those that did not undergo terminal differentiation in pupal development. The authors show that Notch is activated by its ligand Delta which is expressed on the GMC daughter cell and on cortex glia. They determine that the temporal requirement for Notch activity is 0-72 hours after larval hatching (ALH) (i.e., 1st instar through mid-3rd instar at 25C). In NBs/GMCs depleted for Notch, early temporal markers were still expressed at time points when they should be off and late markers were delayed in expression. These effects were observed in ~20-40% of NBs (Figures 5 and 6). Through mining existing data sets, they found that the early temporal factor Imp - an RNA binding protein - can bind Delta mRNA. They state that Delta transcripts decrease over time (without any reference to a Figure or to published work), leading to the hypothesis that Delta mRNA is repressed by the late temporal factors. Over-expressing late factors Syp or E93 earlier in development leads to downregulation of a Delta::GFP protein trap. These results lead to a model in which Notch regulates expression of early temporal factors and early temporal factors regulate Notch activity through translation of Delta mRNA.

There are several strengths of this study. The authors report rigorous measurements and statistical analyses throughout the study. Their conclusions are appropriate for the results. Data mining revealed an important mechanism - that Imp binds Delta mRNA - supporting the model that early temporal factors promote Delta expression, which in turn promotes Notch signaling.

There are also several weaknesses:<br /> 1. The activation of Notch in NBs by Delta in GMCs was already shown by this group in their Dev 2022 paper, reducing some of the impact of this study.<br /> 2. The authors do not explain their current results in context of their prior paper (2022 Dev) until the Discussion, but this would be useful to read in the Introduction. Similarly, it would be good to mention that in the 2022 paper, they find a significant number of wor>Notch RNAi NBs at 2 AHL that are cycling. Are the adult Notch RNAi in this study descended from those NBs at 2 hours ALH in the 2022 study? In other words, how does the early requirement for Notch between 0-72 hours ALH reported in the current study relate to the Notch-depleted NBs identified in the 2022 paper?<br /> 3. Most of the experiments rely upon continuous depletion of Notch from embryonic stage 8 until adulthood using the wor-GAL4 driver. There is no lineage tracing of this driver and there is no citation about the published expression pattern of this driver. The inclusion of these details is important for a broad audience journal.<br /> 4. Most of the experiments utilize a single RNAi transgene for Notch, Delta, Imp, Syp, E93. There are no experiments demonstrating the efficacy of the RNAi lines and no references to prior use and/or efficacy of these lines.

An appraisal: The authors use temperature shifts with Gal80TS to show that Notch is required between 0-72 hours ALH. They show with the use of known markers of the temporal factors and Delta protein trap, that Imp promotes Delta protein expression and the later temporal factors reduce Delta, although the molecular mechanisms are not clearly delineated. Overall, these data support their model that the reduction of Delta expression during larval development leads to a loss of Notch activity.

As noted in the Discussion, this study raises many questions about what Notch does in larval CB NBs. For example, does it inhibit Castor or Imp? Is Notch required in certain neural lineages and not others. These studies will be of interest in the community of developmental neurobiologists.

Reviewer #2 (Public Review):

Embryonic stem cells extensively proliferate to generate the necessary number of cells that are required for organogenesis, and their proliferation must be timely terminated to allow for proper patterning. Thus, timely termination of stem cell proliferation is critical for proper development. Numerous studies have suggested that cell-extrinsic changes in the surrounding niche environment drive the termination of stem cell proliferation. By contrast, cell-intrinsic mechanisms that terminate stem cell proliferation remain poorly understood. Fruit fly larval brain neuroblasts provide an excellent model for mechanistic investigation of intrinsic control of stem cell proliferation due to the wealth of information on molecular marks, gene functions and lineage hierarchy. Sood et al. conducted a genetic screen to identify genes that are required for the termination of neuroblast proliferation in metamorphosis and found that Notch and its ligand Delta contribute to their exit from cell cycle. They showed that knocking down Notch or delta function in larval neuroblasts allows them to persist into adulthood and remain proliferative when no neuroblasts can be detected in wild-type adult brains. By carrying out a well-designed temperature-shift experiment, the authors showed that Notch is required early during larval development to promote timely exit from cell cycle in metamorphosis. The authors went on to show that attenuating Notch signaling prolongs the expression of temporal identity genes castor and seven-up perturbing the switch from Imp to Syp/E93. Finally, they showed that knocking down Imp function or overexpressing E93 can restore the elimination of neuroblasts in Notch/delta mutant brains.

Overall, the experiments are well conceived and executed, and the data are clear. However, the data reported in this study represent incremental progress in improving our mechanistic understanding of the termination of neuroblast proliferation. Some of the data seem to represent more careful analyses of previously published observations described in the Zacharioudaki et al., Development 2016 paper while others seem to contradict to the results in this study. Gaultier et al., Sci. Adv. 2022 suggested that Grainyhead is required for the termination of neuroblast proliferation in a neuroblast tumor model, and grainyhead is a direct target of Notch signaling. Thus, Grainyhead should be a key downstream effector of Notch signaling in terminating castor and seven-up expression. Identical to Notch signaling, Grainyhead is also expressed through larval development. Grainyhead can function as a classical transcription factor as well as a pioneer factor raising the possibility that temporal regulation of neurogenic enhancer accessibility might be at play in allowing Notch signaling in early larval development to set up termination of castor and seven-up expression in metamorphosis. Diving deeper into how dynamic changes in chromatin in neurogenic enhancers affect the termination of neuroblast proliferation will significantly improve our understanding of termination of stem cell proliferation in diverse developing tissue.

Reviewer #3 (Public Review):

In this study, the authors investigate the effects of Notch pathway inactivation on the termination of Drosophila neuroblasts at the end of development. They find that termination is delayed, while temporal patterning progression is slowed down. Forcing temporal patterning progression in a Notch pathway mutant restores the correct timing of neuroblast elimination. Finally, they show that Imp, an early temporal patterning factor promotes Delta expression in neuroblast lineages. This indicates that feedback loops between temporal patterning and lineage-intrinsic Notch activity fine tunes timing of early to late temporal transitions and is important to schedule NB termination at the end of development.<br /> The study adds another layer of regulation that finetunes temporal progression in Drosophila neural stem cells. This mechanism appears to be mainly lineage intrinsic - Delta being expressed from NBs and their progeny, but also partly niche-mediated - Delta being also expressed in glia but with a minor influence. Together with a recent study (PMID: 36040415), this work suggests that Notch signaling is a key player in promoting temporal progression in various temporal patterning system. As such it is of broad interest for the neuro-developmental community.

Strengths<br /> The data are based on genetic experiments which are clearly described and mostly convincing. The study is interesting, adding another layer of regulation that finetunes temporal progression in Drosophila neural stem cells. This mechanism appears to be mainly lineage intrinsic - Delta being expressed from NBs and their progeny, but also partly niche-mediated - Delta being also expressed in glia but with a minor influence. A similar mechanism has been recently described, although in a different temporal patterning system (medulla neuroblasts of the optic lobe - PMID: 36040415). It is overall of broad interest for the neuro-developmental community.

Weaknesses<br /> The mechanisms by which Notch signaling regulates temporal patterning progression are not investigated in details. For example, it is not clear whether Notch signaling directly regulates temporal patterning genes, or whether the phenotypes observed are indirect (for example through the regulation of the cell-cycle speed). The authors could have investigated whether temporal patterning genes are directly regulated by the Notch pathway via ChIP-seq of Su(H) or the identification of potential binding sites for Su(H) in enhancers. A similar approach has been recently undertaken by the lab of Dr Xin Li, to show that Notch signaling regulates sequential expression of temporal patterning factors in optic lobes neuroblasts (PMID: 36040415), which exhibit a different temporal patterning system than central brain neuroblasts in the present study. As such, the mechanistic insights of the study are limited.

Reviewer #1 (Public Review):

The authors set out to investigate the hypothesis that mirror neurons in ventral premotor area F5 code actions in a common motor representation framework. To achieve this, they trained a linear discriminant classifier on the neural discharge of three types of action trials and test whether the thus trained classifier could decode the same categories of actions when observed. They showed that codes were fully matched for a small subset of neurons during the action epoch, while a wider set of "mirror neurons" showed only poorly matched codes for different epochs.

The authors controlled for potential visual object confounds by having identical objects be manipulated in three different ways and by having the animal carry out the motor execution in the dark. The main strength of the study lies in the clever decoding approach testing the matched tuning to behavioural categories in a model-free way. The central result is in the identification of the small sub-group of mirror neurons that show true matching during the execution epoch, which can dissociate the three types of action almost perfectly. This aligns well with some previous work while offering a novel avenue to identify and investigate those neurons.

The underlying neuronal mechanism and behavioural relevance of these neurons remain an open question. It would have been interesting to understand better whether the specific motor representations at a recording site, for instance identified through microstimulation prior to recording (see Methods), the reaction times on individual trials or the specific gaze targets (object/hand) had a bearing on the decoding performance for a neuron/trial. Ultimately, the uncovered matched mirror representations should in future experiments be tested with causal interventions and linked trial-by-trial to action selection performance.

The authors put the focus of their discussion on the wider, less well-matched neuronal pool to support an action selection framework, which is of course a valid view and well established in motor representations. From a sensory perspective, sparse coding, as suggested by the small group of "true" mirror neurons identified with the decoding approach, should also be considered as the basis for a possible neuronal mechanism. A particular strength of the paper is that it could give new data and impetus to the important discussion about how motor and sensory coding frameworks come together in cortical processing.

Reviewer #2 (Public Review):

The paper by Pomper and coworkers is an elegant neurophysiological study, generally sound from a methodological point of view, which presents extremely relevant data of considerable interest for a broad audience of neuroscientists. Indeed, they shed new light on the mirror mechanism in the primate brain, trying to approach its study with a novel paradigm that successfully controls for some important factors that are known to impact mirror neuron response, particularly the target object. In this work, a rotating device is used to present the very same object to the monkey or the experimenter, in different trials, and neurons are recorded while the monkey (motor response) or the experimenter (visual response) performed a different action (twist, shift, lift) cued by a colored LED.

The results show that there is a small set of neurons with congruent visual and motor selectivity for the observed actions, in line with classical mirror neuron studies, whereas many more cells showed temporally unstable matched or even completely non-matched tuning for the observed and executed actions. Importantly, the population codes allow to accurately decode both executed and observed actions and, to some extent, even to cross-decode observed actions based on the coding principles of the executed ones.

In my view, however, the original hypothesis that an observer understands the actions of others by the activation of his/her motor representations of the observed actions constitutes circular reasoning that cannot be challenged or falsified, as the author may want to claim. Indeed, 1) there is no causal evidence in the paper favoring or ruling out this hypothesis (and there couldn't be), 2) there is no independent definition (neither in this paper nor in the literature) of what "action understanding" should mean (or how it should be measured). Instead, the findings provide important and compelling evidence to the recently proposed hypothesis that observed actions are remapped onto (rather than matched with) motor substrates, and this recruitment may primarily serve, as coherently hypothesized by the authors, to select behavioral responses to others (at least in monkeys).

1) One of the main problems of this manuscript is, in my view, a theoretical one. The authors follow a misleading, though very influential, proposal, advanced since the discovery of mirror neurons: if there are (mirror) neurons in the brain of a subject with an action tuning that is matched between observation and execution contexts, then the subject "understands" the observed action. This is clearly circular reasoning because the "understanding" hypothesis uniquely derives from the neuron firing features, which are what the hypothesis should explain. In fact, there is no independent, operational definition of the term "understanding". Not surprisingly there is no causal evidence about the role of mirror neurons in the monkey, and the human studies that have claimed to provide causal evidence of "action understanding" ended up using, practically, operational definitions of "recognition", "match-to-sample", "categorization", etc. Thus, "action understanding" is a theoretical flaw, and there is no way "to challenge" a theoretical flaw with any methodologically sound experiment, especially when the flaw consists of circular reasoning. It cannot be falsified, by definition: it must simply be abandoned.<br /> On these bases, I strongly encourage the authors to rework the manuscript, from the title to the discussion, by removing any useless attempt to falsify or challenge a circular concept and, instead, constructively shed new light on how mirror neurons may work and which may be their functional role.

2) An important point to be stressed, strictly related to the previous one, concerns the definition of "mirror neuron". I premise that I am perfectly fine with the definition used by the authors, which is in line with the very permissive one adopted in most studies of the last 20 years in this field. However, it does not at all fulfill the very restrictive original criteria of the study in which "action understanding" concept was proposed (see Gallese et al. 1996 Brain): no response to object, no response to pantomimed action or tool actions, activation during execution in the dark and during the observation of another's action. If the idea (which I strongly disagree with) was to simply challenge a (very restrictive) definition of mirroring (a very out-of-date one, indeed, and different from the additional implication of "action understanding"), the original definition of this concept should be at least rigorously applied. In the absence of additional control conditions, only the example neuron in Figure 2A could be considered a mirror neuron according to Gallese et al. 1996. Permissive criteria implies that more "non-mirror" neurons are accepted as "mirror": simply because they are permissively named "mirror", does not imply they are mirroring anything as initially hypothesized (Example neuron in Fig 2B, for example, could be related to mouth, rather than hand, movements, since it responds strongly and similarly around the reward delivery also during the observation task, when the monkey should be otherwise still). Clearly, these concerns impact all the action preference analyses. To practically clarify what I mean, it should be sufficient to note that 74% (reported in this study) is the highest percentage ever reported so far in a study of neurons with "mirror" properties in F5 (see Kilner and Lemon 2013, Curr Biol) and it is similar to the 68% recently reported by these same authors (Pomper et al. 2020 J Neurophysiol) with very similar criteria. Clearly, there is a bias in the classification criteria relative to the original studies: again, no surprise if by rendering most of the recorded neurons "mirror by definition" then they don't "mirror" so much. I suggest keeping the authors' definition but removing the pervasive idea to challenge the (misleading) concept of understanding.

3) It would be useful to provide more information on the task. Panel B in Figure 1 is the unique information concerning the type of actions performed by the monkey and the experimenter. Although I am quite convinced of the generally low visuomotor congruence, there are no kinematics data nor any other evidence of the statement "the experimental monkey was asked to pay attention to the same actions carried out by a human actor". First, although the objects were the same, the same object cannot be grasped or manipulated in the same way by a human and a macaque, even just because of the considerable difference in the size of their hands; this certainly changes the way in which monkeys' and experimenter's hands interact with the same object, and this is a quantifiable (but not quantified) source of visuomotor difference between observed and executed actions and a potential source of reduced congruency. Second, there is little information about monkey's oculomotor behavior in the two conditions, which is known to affect mirror neuron activity when exploratory eye movements are allowed (Maranesi et al. 2013 Eur J Neurosci), potentially influencing the present findings: a {plus minus}7 (vertical) and {plus minus}5 (horizontal) window at 49 cm implies that the monkey could explore a space larger than 10 cm horizontally and 14 cm vertically, which is fine, but certainly leaves considerable freedom to perform different exploratory eye movements, potentially different among observed actions and hence capable to account for different "attention" paid by the monkey to different conditions and hence a source of neural variability, in addition to action tuning.

4) Information about error trials and their relationship with action planning. The monkey cannot really "make errors" because, despite the cue, each object can be handled in a unique way. The monkey may not pay attention to the cue and adjust the movement based on what the object permits once grasped, depending on online object feedback. From the behavioral events and the times reported in Table 1, I initially thought that "shift" action was certainly planned in advance, whereas "lift" and "twist" could in principle be obtained by online adjustments based on object feedback; nonetheless, from the Methods section it appears that these times are not at all informative because they seem to depend on an explicit constraint imposed by the experimenters (in a totally unpredictable way). Indeed, it is stated that "to motivate the monkey even more to use the LED in the execution task, another timeout was active in 30% (rarely up to 100%) of trials for the time period between touch of object to start moving the object: 0.15 (rarely 0.1) for a twist and shift, 0.35 (rarely 0.3s) for a lift". This is totally confusing to me; I don't understand 1) why the monkey needed to be motivated, 2) how can the authors be sure/evaluate that the monkeys were actually "motivated" in this way, and 3) what kind of motor errors the monkey could actually do if any. If there is any doubt that the monkeys did actually select and plan the action in advance based on the cue, there is no way to study whether the activity during action execution truly reflects the planned action goal or a variety of other undetermined factors, that may potentially change during the trials. Please clarify.

5) Classification analysis. There seems to be no statistical criterion to establish where and when the decoding is significantly higher than chance: the classifier performance should be formally analyzed statistically. I would expect that, in this way, both the exe-obs and the obs-exe decoding may be significant. Together with the considerations of the previous point 2 about the permissive inclusion criteria for mirror neurons, this is a remarkable (even quite unexpected) result, which would prove somehow contrary to what the authors claim in the title of the paper. The fact that in any classification the "within task" performance is significantly better than the "between task" performance does not appear in any way surprising, considering both the inclusive selection criteria for "mirror neurons" and the unavoidably huge different sources of input (e.g. proprioceptive, tactile, top-down, etc. afferences) between execution and observation. So, please add a statistical criterion to establish and show in the figures when and where the classifications are significantly above chance.

6) "As the concept of a mirror mechanism posits that the observation performance can be led back to an activation of a motor representation, we restricted this analytical step to a comparison of the exe-obs and the obs-obs discrimination performance". I don't understand the rationale of this choice. The so-called "concept" of mirror mechanism in classical terms posits that mirror neurons have a motor nature and hence their functioning during observation should follow the same principle as during action execution. But this logical consideration has never been demonstrated directly (it is indeed costated by several papers), and when motor neurons are concerned (e.g. pyramidal tract neurons, see Kraskov et al. 2009) their behavior during action observation is by far more complex (e.g. suppression vs facilitation) than that hypothesized for classical "mirror neurons". Furthermore, when across-task decoding for execution and observation code has been used, both in neurophysiological (e.g. Livi et al. 2019, PNAS) and neuroimaging (Fiave et al. 2018 Neuroimage) data, the visual-to-motor direction typical produce better performance than the opposite one. Thus, I don't see any good reason not to show also (if not even just) the obs-exe results. Furthermore, I wonder whether it is considered the possible impact of a rescaling in the single neuron firing rate across contexts, as the observation response is typically less strong than the execution response in basically all brain areas hosting neurons with mirror properties, and this should not impact on the matching if the tuning for the three actions remains the same (e.g. see Lanzilotto et al. 2020 PNAS). The analysis shown in Figures 4 and 5 is, for the rest, elegant and very convincing - somehow surprising to me, as the total number of "congruent" neurons (7.5%) is even greater than in the original study by Gallese et al. (5.4%).

7) The discussion may need quite deep revision depending on the authors' responses and changes following the comments; for sure it should consider more extensively the numerous recent papers on mirror neurons that are relevant to frame this work and are not even mentioned.

Reviewer #3 (Public Review):

Mirror neurons are a big deal in the neuroscience literature and have been for thirty years. I (and many others) remain skeptical of whether they serve the functions often attributed to them - specifically, whether they are motor planning neurons that contribute to understanding the actions of others. Testing their functions, therefore, is of great interest and importance. The present study, however, is not a cogent or convincing test. I do not think this study helps to answer the questions surrounding mirror neurons. It purports to provide a crucial test, that comes out mostly against the mirror neuron hypothesis, but the test has too many weaknesses to be convincing.

First, consider that the motor tuning and the visual tuning match "poorly." How poor or good must the match be before the mirror neuron hypothesis is rejected? I do not know, and the study does not help here. Even a "poor" match could contribute significantly to a social perception function.

Second, the results remind me in some ways of other multi-modal responses in the brain. For example, in the visual area MST, neurons are tuned to optic flow fields that imply specific directions of self-motion. Many of the same neurons are tuned to vestibular signals that also imply specific directions of self-motion. But the optic flow tuning and the vestibular tuning are not perfectly matched. There is considerable slop and complexity in how the two tunings compare within individual neurons. That complexity is not evidenced against multi-modal tuning. Instead, it suggests a hidden-layer complexity that is simply not fully understood yet. Just so here, the fact that the apparent motor tuning and apparent visual tuning match "poorly" is not evidence against both a motor planning and a visual encoding function.

Third, the animals are massively over-trained in three actions. They perform these actions and see them performed thousands of times toward the same object. Surely, if I were in the place of the monkey, every time I saw the object, I'd mentally imagine all three actions. As I saw a person act on the object, I'd mentally imagine the alternative two actions at the same time. Even if the mirror neuron hypothesis is strictly correct, this experiment might still find a confusion of signals, in which neurons that normally might respond mainly to one action begin to respond in a less predictable way during all three trial types.

Fourth, the experiment relies on a colored LED that acts as an instructional cue, telling the monkey which action to perform. What is to stop the neurons from developing a cue-sensitive response, as in classic studies from Steve Wise and others in the premotor cortex? Perhaps the neuronal signal that the experimenters are trying to measure is partly obscured by other, complex responses influenced in some manner by the instructional cue?

Fifth, finally, and most importantly, the fundamental problem with this study is that it is correlational. Studies that purport to test the function of a set of neurons, and do so by use of correlational measurements, cannot provide strong answers. There are always half a dozen different interpretations and caveats, such as the ones I raised here. Both sides of a debate can always spin the results, and the arguments are never resolved. To test the mirror neuron hypothesis properly would require a causal study. For example, lesion area F5 and test if the monkey is less able to discriminate the actions of others. Or, electrically microstimulate in area F5 and test if the stimulation interferes (either constructively or destructively) with the task of discriminating the actions of others. Only in this way will it be possible to answer the question: do mirror neurons functionally participate in understanding the actions of others? The present study does not answer that question.

Reviewer #1 (Public Review):

Cedillo et al. address the critically important question of how biguanides exert their positive effects on longevity using the powerful C. elegans model. Biguanides metformin and phenformin have been widely prescribed in the clinic to address metabolic challenges of diabetes; more recently the value of metformin in addressing specific cancers has emerged, and testing for impact on healthy human aging is getting underway. The need to understand the mechanism of biguanide action and the metabolic consequences of biguanide administration is clear.

The authors report that three genes that suppress longevity associated with metformin or phenformin treatment affect a common pathway for ether lipid biosynthesis; this ether lipid biosynthesis pathway is required for mitochondrial lifespan extension, eat-2 mediated dietary restriction longevity, and TOR inhibition-associated longevity, but not insulin pathway mediated longevity. Authors document with lipid profiling how ether lipids and some other lipids are impacted by phenformin vs. genetic disruption of ether lipid biosynthesis, define the tissue primarily responsible for the ether lipid biosynthesis, show that over-expression of enzyme fard-1 is sufficient to confer most of the phenformin effect, and implicate conserved stress transcription factor SKN-1 as a downstream outcome of the ether lipid change.

Strengths include the exploitation of the nematode model to address requirements not readily discerned in other models, the rigor of genetic documentation, the inclusion of metabolic profiling, the testing of multiple potential pathways that have been in the general discourse regarding metformin action, and the elaboration of a reasonably supported model that ether lipid biosynthesis is required for phenformin to activate longevity-promoting metabolic defenses downstream of conserved stress-responsive transcription factor SKN-1/NRF2. The novelty includes that ether lipids are directly linked to lifespan, ether lipid biosynthesis is needed for specific longevity pathways, and that ether lipids might play a role in a shift to pro-longevity metabolism.

There are some points that require clarification and could benefit from additional study, some wording and presentation issues, and a few missing points of potential discussion.

Overall, the data reported in this paper contribute a highly valuable advance in the biguanide field and adds stimulating hypotheses to the scientific community for moving forward in this biomedically important area.

Reviewer #2 (Public Review):

This manuscript pulls together a series of integrated genetic and metabolomic data sets to examine the molecular basis for biguanide action in C. elegans. Biguanides such as Metformin are important anti-diabetic drugs as well as being explored as a therapeutic mechanism for increasing human longevity. Understanding the molecular basis of biguanide action is of general interest to those in the ageing and age-related health fields as well as to those studying metabolism and obesity. The work here has been carried out in C. elegans but the work can be picked up by those working in mammalian systems. More could be done to highlight the conserved aspects of the mechanisms involved to assist with this translatability.

The methodology used is in general standard in the field and experiments are reported in detail. The successful use of metabolomics in C. elegans and its associated protocols is helpful as more labs expand to do this type of work.

Strengths: In general all the experiments presented are logical and well executed with the conclusions supported by the data. I am convinced that: 1) Metformin and Phenformin extend C. elegans lifespan (although that has previously been shown), 2) biguanides induce changes in ether lipids, 3) genes required for ether lipid biogenesis are required for the lifespan incurred with biguanide treatment and, in the case of fard-1 oe, can also promote longevity when levels are increased, 4) ether lipid biogenesis is also needed for other specific key longevity processes to extend lifespan, and 5) that some key ageing regulators (skn-1, aak-2 and daf-16) are required for fard-1 oe to extend lifespan.

Weaknesses: I was less convinced by the fat accumulation data and felt that the link between skn-1 gain of function and ether lipid genes was not clear and that the results were more correlative than mechanistic. If age-associated somatic depletion of fat is important for the lifespans seen here then this is interesting and important and identifying an epistatic, genetic link between the implicated genes and fat levels is desirable. Additionally, biguanides are reported to have major effects on the metabolism and growth of bacteria. As C. elegans grows on and eats E. coli, it is important that the biguanides in question do not alter the worm's food source. If bacterial growth is restricted or metabolically altered this would have a major impact on fat metabolism and the other outputs examined here (see Cabreiro et al 2013). Therefore the impact of these biguanide treatments on the C. elegans foods used here should be clearly addressed. Additionally, biguanide treatment is subject to dose dependence. Different concentrations of biguanide are used for different types of experiments to make correlative points e.g. growth inhibition at 160mM metformin, and metformin uptake measured in C. elegans treated with 50mM. It is not clear why, or whether this could impact the results. Can the authors be sure that these different doses do not alter metformin action and/or uptake either by the worms or the way the bacteria metabolise it? I appreciate that it is interesting and important to understand what biguanides are doing in the organism irrespective of whether this is a direct or indirect effect but knowing how the effects are achieved could be important for treatment strategies moving forwards.

Reviewer #1 (Public Review):

The authors expand upon prior findings and show that basolateral amygdala (BLA) activity is necessary for defensive responses elicited by both innate and learned threats. The authors also show that a projection from the auditory thalamus (MGM thalamic nucleus) mediates these effects.

Learned threats were modelled with auditory fear conditioning. The authors finding showing that the MGM-BLA pathway is required for auditory fear learning is largely a replication of prior results.

The novelty in this paper is that the authors show that the auditory MGM-BLA pathway is involved in defense evoked by a visual looming stimulus.

Overall, this is a reasonably designed study. The main weakness is that the loss of function manipulations use either caspase-induced lesions or contralateral chemogenetic disconnection studies, which lack temporal resolution.

Reviewer #2 (Public Review):

Khalil et al. aimed to gain insights into similarities and differences between circuits processing innate and learned threats. For this, they investigated a circuit that is well established to have a critical role in auditory associative threat learning, the projection from the medial geniculate nucleus (MGN) to the basolateral amygdala (BLA), and carried out a side-by-side comparison of its role in conditioned and innate threat.

Although the MGN is part of the main auditory stream, the neurons that project to BLA are multimodal. Khalil et al. took advantage of this to use visual looming stimuli to evoke innate threat. The authors showed that the MGN-BLA pathway processes both innate freezing responses to looming black circles and threat-conditioned freezing responses to tones. The disruption of the pathway impairs freezing in both cases, and the pathway is activated mostly in the presence of freezing. This suggests that the MGN-BLA processes threat independently of the sensory modality and of whether the threat is learnt or not. This further suggests that these different forms of threat may share similar mechanisms.

Nonetheless, the fact that MGN-BLA circuit disruptions were done during the conditioning phase of associative threat learning, and not during the recall phase only, complicates the side-by-side comparison: it could be argued that in this case what is disturbed is the processing of the unconditioned innately aversive stimulus in the task, the foot shock, instead of the learnt threat of the sound. Still, this would go in hand with one of the main conclusions of the study, which is that the MGN-BLA processes innate threats.

There are alternative interpretations of the results though, which are beyond the scope of the study: the circuit might be relevant for processing salient stimuli beyond threatening stimuli, for instance for positive valence stimuli as well; or this circuit might be relevant for processing the freezing response to threat in particular. To target the MGN-BLA circuit, the authors employ viral-vector mediated expression of proteins in mice. This way they delete, inhibit, or image either the activity of the neurons (or the axons) that project from MGN to BLA, or the BLA neurons themselves. They combine this with fiber-photometry and behavioural quantifications. Targeting these small and deep nuclei in the mouse brain bilaterally is challenging, which increases the value of the presented data. Conversely, it is important that the authors support more explicitly the specificity of their targeting methods and quantifications throughout the manuscript.

Overall, the main conclusions of this paper are mostly supported by data, but important methodological aspects need to be clarified, data analysis extended and the interpretation of results discussed further. The question of whether innate and learnt responses to stimuli share common mechanisms is timely. This study places the MGN-BLA pathway as a suitable model circuit to investigate this and paves the way for future work to dig into the implicated mechanisms.

Specific comments (strengths):<br /> a) The authors use two methods to interrupt the MGN-BLA pathway, a reversible one (chemogenetics) and an irreversible one (neuronal deletion via caspase 3 expression), obtaining consistent results that strengthen the evidence supporting their conclusions.<br /> b) The authors demonstrate the efficacy of their MGN-BLA pathway interruption methods with in vivo recordings.<br /> c) The approach of addressing the same behavioural output (freezing) in the two conditions (innate and learnt threat) helps the interpretability of results.

Specific comments (weaknesses):<br /> e) There are not enough analysis and method descriptions to demonstrate the specificity of the targeting approach, which is in some cases neither reflected in the pictures of the main figures. These include quantifications of the extension of expression/deletions in the brain and placement of viral-vector injections. In particular, these should show that i) protein expression does not extend beyond the BLA or MGN; ii) the MGN cells projecting to the striatum (right above the BLA) are not implicated, iii) that neurons in the visual thalamus are not affected by the manipulations. These are critical points that need to be addressed.<br /> f) There is a lack of digging into the mechanisms that could be enhanced with further analysis and discussion. For example, to start addressing this question, the authors administer blockers of beta-adrenergic receptors systemically. This reveals differences between MGN-BLA projecting neurons, BLA neurons, and innate and learnt threat, but the mechanistic implications are not clear and should be discussed. Also, the interpretation of the pathway's role in behaviour and its relation to neuronal activity could be deepened with further analysis.

Reviewer #3 (Public Review):

Khalil et al. investigated the role of medial geniculate nuclei -> basolateral amygdala pathway in the processing of innate and learned threats. Using looming stimuli and cued fear conditioning the authors show that both the BLA and MGN projections to the BLA respond to learned and innately threatening stimuli and that their activation is necessary to generate adequate fear responses. Lastly, Khalil et al. highlight a possible role of adrenergic signaling in modulating threat-induced BLA (but not MGN) activity. The manuscript is well conceived, the statistical analysis is solid, and the methodology is appropriate. The strength of this paper is that the hypothesis is tested using multiple experimental strategies that all nicely converge to demonstrate the involvement of the MGN-BLA pathway in threat processing. However, a more detailed analysis of fiber photometry data in relation to the presented stimuli and to behavioral responses would help to clarify whether this MGN-BLA pathway is involved in processing sensory stimuli per se or directly generates behavioral responses.

Reviewer #1 (Public Review):

It has been shown previously that there are relationships between a transdiagnostic construct of anxious-depression (AD), and average confidence rating in a perceptual decision task. This study sought to investigate these results, which have been replicated several times but only in cross-sectional studies. This work applies a perceptual decision-making task with confidence ratings and a transdiagnostic psychometric questionnaire battery to participants before and after an iCBT course. The iCBT course reduced AD scores in participants, and their mean confidence ratings increased without a change in performance. Participants with larger AD changes had larger confidence changes. These results were also shown in a separate smaller group receiving antidepressant medication. A similar sized control group with no intervention did not show changes.

The major strength of the study is the elegant and well-powered data set. Longitudinal data on this scale is very difficult to collect, especially with patient cohorts, so this approach represents an exciting breakthrough. Analysis is straightforward and clearly presented. However, no multiple comparison correction is applied despite many different tests. While in general I am not convinced of the argument in the citation provided to justify this, I think in this case the key results are not borderline (p<0.001) and many of the key effects are replications, so there are not so many novel/exploratory hypothesis and in my opinion the results are convincing and robust as they are. The supplemental material is a comprehensive description of the data set, which is a useful resource.

The authors achieved their aims, and the results clearly support the conclusion that the AD and mean confidence in a perceptual task covary longitudinally.

I think this study provides an important impact to the project of computational psychiatry.Sspecifically, it shows that the relationship between transdiagnostic symptom dimensions and behaviour is meaningful within as well as across individuals.

Reviewer #2 (Public Review):

The authors of this study investigated the relationship between (under)confidence and the anxious-depressive symptom dimension in a longitudinal intervention design. The aim was to determine whether confidence bias improves in a state-like manner when symptoms improve. The primary focus was on patients receiving internet-based CBT (iCBT; n=649), while secondary aims compared these changes to patients receiving antidepressants (n=82) and a control group (n=88).

The results support the authors' conclusions, and the authors convincingly demonstrated a weak link between changes in confidence bias and anxious-depressive symptoms (not specific to the intervention arm)

The major strength and contribution of this study is the use of a longitudinal intervention design, allowing the investigation of how the well-established link between underconfidence and anxious-depressive symptoms changes after treatment. Furthermore, the large sample size of the iCBT group is commendable. The authors employed well-established measures of metacognition and clinical symptoms, used appropriate analyses, and thoroughly examined the specificity of the observed effects.

However, due to the small effect sizes, the antidepressant and control groups were underpowered, reducing comparability between interventions and the generalizability of the results. The lack of interaction effect with treatment makes it harder to interpret the observed differences in confidence, and practice effects could conceivably account for part of the difference. Finally, it was not completely clear to me why, in the exploratory analyses, the authors looked at the interaction of time and symptom change (and group), since time is already included in the symptom change index.

This longitudinal study informs the field of metacognition in mental health about the changeability of biases in confidence. It advances our understanding of the link between anxiety-depression and underconfidence consistently found in cross-sectional studies. The small effects, however, call the clinical relevance of the findings into question. I would have found it useful to read more in the discussion about the implications of the findings (e.g., why is it important to know that the confidence bias is state-dependent; given the effect size of the association between changes in confidence and symptoms, is the state-trait dichotomy the right framework for interpreting these results; suggestions for follow-up studies to better understand the association).

Reviewer #3 (Public Review):

This study reports data collected across time and treatment modalities (internet CBT (iCBT), pharmacological intervention, and control), with a particularly large sample in the iCBT group. This study addresses the question of whether metacognitive confidence is related to mental health symptoms in a trait-like manner, or whether it shows state-dependency. The authors report an increase in metacognitive confidence as anxious-depression symptoms improve with iCBT (and the extent to which confidence increases is related to the magnitude of symptom improvement), a finding that is largely mirrored in those who receive antidepressants (without the correlation between symptom change and confidence change). I think these findings are exciting because they directly relate to one of the big assumptions when relating cognition to mental health - are we measuring something that changes with treatment (is malleable), so might be mechanistically relevant, or even useful as a biomarker?

This work is also useful in that it replicates a finding of heightened confidence in those with compulsivity, and lowered confidence in those with elevated anxious-depression.

One caveat to the interest of this work is that it doesn't allow any causal conclusions to be drawn, and only measures two timepoints, so it's hard to tell if changes in confidence might drive treatment effects (but this would be another study). The authors do mention this in the limitations section of the paper.

Another caveat is the small sample in the antidepressant group.

Some thoughts I had whilst reading this paper: to what extent should we be confident that the changes are not purely due to practice? I appreciate there is a relationship between improvement in symptoms and confidence in the iCBT group, but this doesn't completely rule out a practice effect (for instance, you can imagine a scenario in which those whose symptoms have improved are more likely to benefit from previously having practiced the task).

Relatedly, to what extent is there a role for general task engagement in these findings? The paper might be strengthened by some kind of control analysis, perhaps using (as a proxy for engagement) the data collected about those who missed catch questions in the questionnaires.

I was also unclear what the findings about task difficulty might mean. Are confidence changes purely secondary to improvements in task performance generally - so confidence might not actually be 'interesting' as a construct in itself? The authors could have commented more on this issue in the discussion.

To make code more reproducible, the authors could have produced an R notebook that could be opened in the browser without someone downloading the data, so they could get a sense of the analyses without fully reproducing them.

Rather than reporting full study details in another publication I would have found it useful if all relevant information was included in a supplement (though it seems much of it is). This avoids situations where the other publication is inaccessible (due to different access regimes) and minimises barriers for people to fully understand the reported data.

Reviewer #1 (Public Review):

The authors consider data by the Heisenberg group on rheological properties of non-confluent tissue in zebrafish embryos. These data had shown a steep increase and subsequent saturation in viscosity with cell density. The authors introduce a physical agent-based model of such tissues that accounts for the dispersion in cell size and the softness of the cells. The model is inspired by previous models to study glassy dynamics and reveals essential physical features that can explain the observed behavior. It goes beyond previous studies that had analysed the observations in terms of a percolation problem. The numerics are thoroughly done and could have a deep impact on how we describe non-confluent tissues.

A major weakness of the manuscript is the way it is written, which gives the impression to have been done rather carelessly. Several quantities are not properly introduced and at places physical jargon is used that makes the work difficult to access for readers without a background in soft matter.

Reviewer #2 (Public Review):

This paper explores how minimal active matter simulations can model tissue rheology, with applications to the in vivo situation of zebrafish morphogenesis. The authors explore the idea of active noise, particle softness and size heterogeneity cooperating to give rise to surprising features of experimental tissue rheologies (in particular an increase and then a plateau in viscosity with fluid fraction). In general, the paper is interesting from a theoretical standpoint, by providing a bridge between concepts from jamming of particulate systems and experiments in developmental biology. The idea of exploring a free space picture in this context is also interesting.

However, I'm still unsure right now though of how much it can be applied to the specific system that the authors refer to - which could be fixed either by considering other experimental systems/models reported in the recent literature or by doing the following theoretical checks:

- Take your current simulations and smoothly change the ratio of polydispersity from 8 to 0 to see exactly how much dispersity is needed to explain viscosity plateauing, and at which point the transition occurs.

- Cellular self-propulsion does not seem to play a role in zebrafish blastoderm, see Ref. [14]. Active noise has been proposed to play key roles in other systems and you could check whether such active noise could replace self-propulsion in your model, see for example Kim & Campas, Nat Phys, 2021.

- Could you simulate realistic rheological deformations to see how much they match both your expectation and the data?

Reviewer #3 (Public Review):

The authors successfully explain the sharp rise and subsequent saturation of the viscosity in dependence of cell packing fraction in zebrafish blastoderm with the help of a 2d model of soft deformable, polydisperse and self-propelled (active) disks. The main experimental observations can be reproduced and the unusual dependence of the viscosity on packing fraction can be explained by the available free area and the emergent motility of small sized cells facilitating multi-cell rearrangement in a highly jammed environment.

The paper is very well written, the results (experimental as well theoretical) are original and scientifically valid. This is an important contribution to understand rheological properties of non-confluent tissues linking equilibrium and transport properties.

Reviewer #1 (Public Review):

Many drugs have off-target effects on the gut microbiota but the downstream consequences for drug efficacy and side effect profiles remain unclear. Herein, Wang et al. use a mouse model of liver injury coupled to antibiotic and microbiota transplantation experiments. Their results suggest that metformin-induced shifts in gut microbial community structure and metabolite levels may contribute to drug efficacy. This study provides valuable mechanistic insights that could be dissected further in future studies, including efforts to identify which specific bacterial species, genes, and metabolites play a causal role in drug response. Importantly, although some pilot data from human subjects is shown, the clinical relevance of these findings for liver disease remain to be determined.

The major strength of this work is its scope, including detailed mouse phenotyping, inter-disciplinary methods, and numerous complementary experiments. The antibiotic depletion and FMT experiments provide support for a role of the gut microbiota in this mouse model.

A major limitation is the lack of studies narrowing down which microbes are responsible. Sequencing data is shown, but no follow-up studies are done with bacterial isolates or defined communities.

The link to GABA is also somewhat tenuous. While it does match the phenotypic data, there are no targeted experiments in which GABA producing microbial communities/strains are compared to a control community/strain. As such, it seems difficult to know how much of the effects in this model are due to GABA vs. other metabolites.

My major recommendation would be to revise the title, abstract, and discussion to provide more qualification and to consider alternative interpretations.

Some key controls are also missing, which could be addressed by repeat experiments in the mouse model. The antibiotic depletion experiment would be improved by testing the effect of antibiotics in the absence of metformin, to see if the effect is just driven by the model itself as opposed to an interaction between metformin and antibiotics. The FMT experiment lacks a control group and suffers from pseudoreplication: multiple donors from metformin treated and untreated mice could be used to colonize separate groups of recipient mice.

Reviewer #2 (Public Review):

The authors examine the use of metformin in the treatment of hepatic ischemia/reperfusion injury (HIRI) and suggest the mechanism of action is mediated in part by the gut microbiota and changes in hepatic ferroptosis. While the concept is intriguing, the experimental approaches are inadequate to support these conclusions.

The histological and imaging studies were considered a strength and reveal a significant impact of metformin post-HIRI.

Weaknesses largely stem from the experimental design. First, use of the iron chelator DFO would be strengthened using the ferroptosis inhibitor, liproxstatin. Second, the impact of metformin on the microbiota is profound resulting in changes in bile acid, lipid, and glucose homeostasis. Throughout the manuscript no comparisons are made with metformin alone which would better capture the metformin-specific effects. Lastly, the absence of proper controls including germ free mice, metformin treated mice, FMT treated mice, etc make it difficult to understand the outcomes and to properly reproduce the findings in other labs.

Overall, while the concept is interesting and has the potential to better understand the pleiotropic functions of metformin, the limitations with the experimental design and lack of key controls make it challenging to support the conclusions.

Reviewer #3 (Public Review):

The study presented in this paper explores the role of gut microbiota in the therapeutic effect of metformin on HIRI, as supported by fecal microbiota transplantation (FMT) experiments. Through high throughput sequencing and HPLC-MS/MS, the authors have successfully demonstrated that metformin administration leads to an increase in GABA-producing bacteria. Moreover, the study provides compelling evidence for the beneficial impact of GABA on HIRI.

Reviewer #1 (Public Review):

This manuscript provides important evidence on the association between sleep regularity and mortality in the UK Biobank, which is a popular topic in recent sleep and circadian research in population-based studies. The analysis reported robust associations between sleep irregularity and increased total, CVD and cancer mortality, and provided evidence to support the role of sleep and circadian health in disease progression and longevity in human populations. The Sleep Regularity Index (SRI) used in this study is a novel metric that quantifies the consistency in rest-activity rhythms over consecutive 24 hour periods, thus providing objective assessment of potential circadian disruption. The study is based on a large accelerometer study with validated follow-up of incident diseases and deaths. The data quality and large sample size strengthen the credibility of the conclusion. Overall, the analyses are appropriately done and the manuscript is clearly written. Additional justification for the assessment of nonlinearity and further subgroup analyses would further improve the manuscript.

Reviewer #2 (Public Review):

This interesting research commendably revealed the association between sleep regularity and mortality. However, as authors acknowledged, the analysis can not accurately identify the cause and effect. In my opinion, the causality is important for this topic, cuz, sleep regularity and health (e.g. chronic disease) were long-term simultaneous status, especially given the participants are older. I suggest that the author could utilize MR analysis to find out for more evidence.

Joint Public Review

In the presence of predators, animals display attenuated foraging responses and increased defensive behaviors that serve to protect them from potential predatory attacks. Previous studies have shown that the basolateral nucleus of the amygdala (BLA) and the periaqueductal gray matter (PAG) are necessary for the acquisition and expression of conditioned fear responses. However, it remains unclear how BLA and PAG neurons respond to predatory threats when animals are foraging for food. The authors employed single-unit recording of BLA and PAG neurons and optogenetic tools to address this question in an 'approach food-avoid predator' paradigm.

The authors observed that rats exhibited a significant increase in the latency to obtain the food pellets and a reduction in the pellet success rate when the predator robot was activated. A subpopulation of PAG neurons showing increased firing rate in response to the robot activation did not change its activity in response to food pellet retrieval during the pre- or post-robot sessions. Optogenetic stimulation of PAG neurons increased the latency to procure the food pellet in a frequency- and intensity-dependent manner, similar to what was observed during the robot test. Combining optogenetics with single-unit recordings, the authors demonstrated that photoactivation of PAG neurons increased the firing rate of 10% of BLA cells. A subsequent behavioral test in three of these same rats demonstrated that BLA neurons responsive to PAG stimulation displayed higher firing rates to the robot than BLA neurons nonresponsive to PAG stimulation. Next, because the PAG does not project monosynaptically to the BLA, the authors used a combination of retrograde and anterograde neural tracing to identify possible regions that could convey robot-related information from PAG to the BLA. They observed that neurons in specific areas of the paraventricular nucleus of the thalamus (PVT) that are innervated by PAG fibers contained neurons that were retrogradely labeled by the injection of CTB in the BLA. In addition, PVT neurons showed increased expression of the neural activity marker cFos after the robot test, suggesting that PVT may be a mediator of PAG signals to the BLA.

Strengths

Overall, the idea that the PAG interacts with the BLA via the midline thalamus during a predator vs. foraging test is new and quite interesting. The authors have used appropriate tools to address their questions. The major impact in the field would be to add evidence to claims that the BLA can be downstream of the dPAG to evoke defensive behaviors. The study also adds to a body of evidence that the PAG mediates primal fear responses.

Weaknesses

The two most significant weaknesses relate to a) anatomical concerns related to the subregions of the BLA and PAG that were targeted by manipulations and analyses and b) the correlational nature of the PVT measures and the lack of any causal role demonstrated. Other concerns are also detailed below.

Anatomical concerns:

1. The authors claim that the recordings were performed in the dorsal PAG (dPAG), but the histological images in Fig. 1B and Supplementary S2 for example show the tip of the electrode in a different subregion of PAG (ventral/lateral). They should perform a more careful histological analysis of the recording sites and explain the histological inclusion and exclusion criteria. Diagrams showing the sites of all PAG and BLA recordings, as well as all fiber optics, would be helpful.<br /> 2. Prior studies investigating the role of BLA neurons during a foraging vs. robot test similar to the one used in this study should be also cited and discussed (e.g., Amir et al 2019, PMID: 30840520; Amir et al 2015, PMID: 26400931). These two studies demonstrated that most neurons in the basal portion of the BLA exhibit inhibitory activity during foraging behavior and only a small fraction of neurons (~4%) display excitatory activity in response to the robot (in contrast to the 25% reported in the present study). A very accurate histological analysis of BLA recording sites should be performed to clarify whether distinct subregions of the BLA encode foraging and predator-related information, as previously shown in the two described studies.<br /> 3. An important claim of this study that the PAG sends predator-related signals to BLA via the PVT (Fig. 4). The authors stated that PVT neurons labeled by intra-BLA injection of the retrograde tracer CTB were activated by the predator, but a proper immunohistochemical quantification with a control group was not provided to support this claim. To provide better support for their claim, the authors should quantify the double-labeled PVT neurons (cFos plus CTB positive neurons) during the robot test.<br /> 4. The AVV anterograde tracer deposit spread to a large part of the PAG, including dorsolateral and lateral PAG, and supraoculomotor regions (Fig. 4B). Is the projection to the PVT from the dPAG or other regions of the PAG?

Concerns about the strength of the evidence supporting a role for the PVT:

5. The authors conclude in the discussion section that the dPAG-amygdala pathway is involved in generating antipredatory defensive behavior. However, the current results are entirely based on correlational analyses of neural firing rate and there is no direct demonstration that the PAG provides information about the robot to the BLA. Therefore, the authors should tone down their interpretation or provide more evidence to support it by performing experiments applying inhibitory tools in the dPAG > PVT > BLA pathway and examining the impact on behavior and downstream neural firing.

Other concerns:

6. One of the main findings of this study is the observation that BLA neurons that are responsive to PAG photostimulation are preferentially recruited during the foraging vs. robot test (Fig. 3). However, the experimental design used to address this question is problematic because the laser photostimulation of PAG neurons preceded the foraging vs. robot test. Prior photoactivation of PAG may have caused indirect short-term synaptic plasticity in BLA cells, which would favor the response of these cells to the robot. Please see Oishi et al, 2019 PMID: 30621738, which demonstrated that 10 trains of 20Hz photoactivation (300 pulses each) was sufficient to induce LTP in brain slices.<br /> 7. The authors should perform a longitudinal analysis of the behavioral responses of the rats across the trials to clarify whether the animals habituate to the robot or not. In Figure 1E, it appears that PAG neurons fire less across the trials, which could be associated with behavioral habituation to the predator robot. If that is the case, the activity of many other PAG and BLA neurons will also most likely vary according to the trial number, which would impact the current interpretation of the results.<br /> 8. In Figure 1, it is unclear why the authors compared the activity of neurons that respond to the robot activation against the activity of the neurons during the retrieval of the food pellets in the pre-robot and post-robot sessions. The best comparison would be aligning the cells that were responsive to the activation of the robot with the moment in which the animals run back to the nest after consuming the pellets during the pre-robot or post-robot sessions. This would enable the authors to demonstrate that the PAG responses are directly associated with the expression of escaping behavior in the presence of the robot rather than associated with the onset of goal-directed movement in direction to the next during the pre- and post-robot sessions. A graphic showing the correlation between PAG firing rate and escape response would be also informative.

Reviewer #1 (Public Review):

This EEG study probes the prediction of a mechanistic account of P300 generation through the presence of underlying (alpha) oscillations with a non-zero mean. In this model, the P300 can be explained by a baseline shift mechanism. That is, the non-zero mean alpha oscillations induce asymmetries in the trial-averaged amplitudes of the EEG signal, and the associated baseline shifts can lead to apparent positive (or negative) deflections as alpha becomes desynchronized at around P300 latency. The present paper examines the predictions of this model in a substantial data set (using the typical P300-generating oddball paradigm and careful analyses). The results show that all predictions are fulfilled: the two electrophysiological events (P300, alpha desynchronization) share a common time course, anatomical sources (from inverse solutions), and covariations with behaviour; plus relate (negatively) in amplitude, while the direction of this relationship is determined by the non-zero-mean deviation of alpha oscillations pre-stimulus (baseline shift index, BSI). This is indicative of a tight link of the P300 with underlying alpha oscillations through a baseline shift account, at least in older adults, and hence that the P300 can be explained in large parts by non-zero mean brain oscillations as they undergo post-stimulus changes.

Reviewer #2 (Public Review):

The authors attempt to show that event-related changes in the alpha band, namely a decrease in alpha power over parieto/occipital areas, explain the P300 during an auditory target detection task. The proposed mechanism by which this happens is a baseline-shift, where ongoing oscillations which have a non-zero mean undergo an event-related modulation in amplitude which then mimics a low frequency event-related potential. In this specific case, it is a negative-mean alpha-band oscillation that decreases in power post-stimulus and thus mimics a positivity over parieto-occipital areas, i.e. the P300. The authors lay out 4 criteria that should hold if indeed alpha modulation generates the P300, which they then go about providing evidence for.

Strengths:<br /> - The authors do go about showing evidence for each prediction rigorously, which is very clearly laid out. In particular, I found the 3rd section connecting resting-state alpha BSI to the P300 quite compelling.<br /> - The study is obviously very well-powered.<br /> - Very well-written and clearly laid out. Also, the EEG analysis is thorough overall, with sensible analysis choices made.<br /> - I also enjoyed the discussion of the literature, albeit with certain strands of P300 research missing.

Weaknesses:<br /> In general, if one were to be trying to show the potential overlap and confound of alpha-related baseline shift and the P300, as something for future researchers to consider in their experimental design and analysis choices, the four predictions hold well enough. However, if one were to assert that the P300 is "generated" via alpha baseline shift, even partially, then the predictions either do not hold, or if they do, they are not sufficient to support that hypothesis. This general issue is to be found throughout the review. I will briefly go through each of the predictions in turn:

1. The matching temporal course of alpha and P300 is not as clear as it could be. Really, for such a strong statement as the P300 being generated by alpha modulation, one would need to show a very tight link between the signals temporally. There are many neural and ocular signals which occur over the course of target detection paradigms: P300, alpha decrease, motor-related beta decrease, the LRP, the CNV, microsaccade rate suppression etc. To specifically go above and beyond this general set of signals and show a tighter link between alpha and P300 requires a deeper comparison. To start, it would be a good idea to show the signals overlapping on the same plot to really get an idea of temporal similarity. Also, with the P300-alpha correlation, how much of this correlation is down to EEG-related issues such as skull thickness, cortical folding, or cognitive issues such as task engagement? One could perhaps find another slow wave ERP, e.g. the Lateralised Readiness Potential, and see if there is a similar strength correlation. If there is not, that would make the P300 relationship stand out.

In Figure 3, it is clear that alpha binning does not account for even 50% of the variance of P300 amplitude. Again, if there is such a tight link between the two signals, one would expect the majority of P300 variance to be accounted for by alpha binning. As an aside, the alpha binning clearly creates the discrepancy in the baseline period, with all alpha hitting an amplitude baseline at approx. 500ms. I wonder if could you NOT, in fact, baseline your slow wave ERP signal, instead using an appropriate high pass filter (see "EEG is better left alone", Arnaud Delorme, 2023) and show that the alpha binning creates the difference in ERP at the baseline which then is reinterpreted as a P300 peak difference after baselining.

2. The topographies are somewhat similar in Figure 4, but not overwhelmingly so. There is a parieto-occipital focus in both, but to support the main thesis, I feel one would want to show an exact focus on the same electrode. Showing a general overlap in spatial distribution is not enough for the main thesis of the paper, referring to the point I make in the first paragraph re Weaknesses. Obviously, the low density montage here is a limitation. Nevertheless, one could use a CSD transform to get more focused topographies (see https://psychophysiology.cpmc.columbia.edu/software/csdtoolbox/), which apparently does still work for lower-density electrode setups (see Kayser and Tenke, 2006).

3. Very nice analysis in Figure 6, probably the most convincing result comparing BSI in steady state to P300, thus at least eliminating task-related confounds.

4. Also a good analysis here, wherein there seem to be similar correlation profiles across P300 and alpha modulation. One analysis that would really nail this down would be a mediation analysis (Baron and Kenny, 1986; https://davidakenny.net/cm/mediate.htm), where one could investigate if e.g. the relationship between P300 amplitude and CERAD score is either entirely or partially mediated by alpha amplitude. One could do this for each of the relationships. To show complete mediation of P300 relationship with a cog task via alpha would be quite strong.

One last point, from the methods it appears that the task was done with eyes closed? That is an extremely important point when considering the potential impact of alpha amplitude modulation on any other EEG component due to the well-known substantial increase in alpha amplitude with eyes closed versus open. I wonder, would we see any of these effects with eyes opened?

Overall, there is a mix here of strengths of claims throughout the paper. For example, the first paragraph of the discussion starts out with "In the current study, we provided comprehensive evidence for the hypothesis that the baseline-shift mechanism (BSM) is accountable for the generation of P300 via the modulation of alpha oscillations." and ends with "Therefore, P300, at least to a certain extent, is generated as a consequence of stimulus-triggered modulation of alpha oscillations with a non-zero mean." In the limitations section, it says the current study speaks for a partial rather than exhausting explanation of the P300's origin. I would agree with the first part of that statement, that it is only partial. I do not agree, however, that it speaks to the ORIGIN of the P300, unless by origin one simply means the set of signals that go to make up the ERP component at the scalp-level (as opposed to neural origin).

Again, I can only make these hopefully helpful criticisms and suggestions because the paper is very clearly written and well analysed. Also, the fact that alpha amplitude modulation potentially confounds with P300 amplitude via baseline shift is a valuable finding.

Reviewer #1 (Public Review):

The present study by Berger et al. analyzes to what extent memory formation is dependent on available energy reserves. This has been dealt with extensively in the case of aversive memory formation, but only very sparsely in the case of appetitive memory formation. It has long been known that an appetitive memory in flies can only be formed by starvation. However, the authors here additionally show that not only the duration of starvation plays a role, but also determines which form of memory (short- or long-term memory) is formed. The authors demonstrated that internal glycogen stores play a role in this process and that this is achieved through insulin-like signaling in octopaminergic reward neurons that integrates internal energy stores into memory formation. Here, the authors suggest that octopamine plays a role as a negative regulator of different forms of memory.

The study sheds light on an old question, to what extent the octopaminergic neuronal system plays a role in the formation of appetitive memory, since in recent years only the dopaminergic system has been in focus. Furthermore, the data are an interesting contribution to the ongoing debate whether insulin receptors play a role in neurons themselves or in glial cells. The experiments are very well designed and the authors used a variety of behavioural experiments, genetic tools to manipulate neuronal activity and state-of-the-art imaging techniques. In addition, they not only clearly demonstrated that octopamine is a negative regulator of appetitive memory formation, but also proposed a mechanism by which the insulin receptor in octopaminergic neurons senses the internal energy status and then controls the activity of those neurons. The conclusions are mostly supported by the data, but some aspects related to the experimental design, some explanations and literature references need more clarification and revision.

1. Usually, long-term memory (LTM) is tested 24 hours after training. Here, the authors usually refer to LTM as a memory that is tested 6 hours after training. The addition of a control experiment to show that LTM that the authors observe here lasts longer would increase the power of this study immensely.

2. The authors define here another consolidated memory component as ARM, when they applied a cold-shock 2 hours after training. However, some publications showed that LTM is formed after only one training cycle (Krashes et al 2008, Tempel et al 1983). This makes it difficult to determine, whether appetitive ARM can be formed. Furthermore, one study showed that appetitive ARM is absent after massed training (Colomb et al 2009). Therefore, the conclusion could be also, that different starvation protocols, would lead to different stabilities of LTM. Therefore, additional experiments could help to clarify this opposing explanation. From these results, it can then be concluded either that different stable forms of LTM are formed depending on the starvation state, or that two differently consolidated memory phases (LTM, ARM) are formed, as has already been shown for aversive memory. This is also important for other statements in the manuscript, and therefore the authors should address this. For example, the findings about the insulin receptor (is it two opposing memories or different stabilities of LTM).

Reviewer #2 (Public Review):

How organism physiological state modulates establishment and perdurance of memories is a timely question that the authors aimed at addressing by studying the interplay between energy homeostasis and food-related conditioning in Drosophila. Specifically, they studied how starvation modulates the establishment of short-term vs long-term memories and clarified the role of the monoamine Octopamine in food-related conditioning, showing that it is not per se involved in formation of appetitive short-term memories but rather gates memory formation by suppressing LTM when energy levels are high. This work clarifies previously described phenotypes and provides insight about interconnections between energy levels, feeding and formation of short-term and long-term food-related memories. In the absence of population-specific manipulation of octopamine signaling, it however does not reach a circuit-level understanding of how these different processes are integrated.

Strengths<br /> - Previous studies have documented the impact of Octopamine on different aspects of food-related behaviors (regulation of energy homeostasis, feeding, sugar sensing, appetitive memory...), but we currently lack a clear understanding of how these different functions are interconnected. The authors have used a variety of experimental approaches to systematically test the impact of internal energy levels in establishment of appetitive memory and the role of Octopamine in this process.

- The authors have used a range of approaches, performed carefully controlled experiments and produced high quality data.

Weaknesses<br /> 1- In the tbh mutant flies, Tyramine -to- Octopamine conversion is inhibited, resulting not only in a lack of Octopamine, but also in elevated levels of Tyramine. If and how elevated levels of Tyramine contributes to the described phenotypes is unclear. In the current version of the manuscript, only one set of experiments (Figure 2) has been performed using Octopamine agonist. This is particularly important in light of recent published data showing that starvation modifies Tyramine levels.

2- Octopamine (and its precursor Tyramine) have been implicated in numerous processes, complicating the analysis of the phenotypes resulting from a general inhibition of tbh.

3- The manuscript explores various aspects of the impact of energy levels on food-related behaviors and the underlying sensing and effector mechanism, both in wild-type and tbh mutants, making it difficult to follow the flow of the results.

Reviewer #3 (Public Review):

In this manuscript, Berger et al. study how internal energy storage influence learning and memory. Since in Drosophila melanogaster, octopamine (OA) is involved in the regulation of energy homeostasis they focus on the roles of OA. To do so they use the tyramine-β-hydroxylase (Tbh) mutant that is lacking the neurotransmitter OA and study short term memory (STM), long-term memory (LTM) and anesthesia-resistant memory (ARM). They show that the duration of starvation affects the magnitude of both short- and long-term memory. In addition, they show that OA has a suppressive effect on learning and memory. In terms of energy storage, they show that internal glycogen storage influences how long sucrose is remembered and high glycogen suppresses memory. Finally, they show that insulin-like signaling in octopaminergic neurons, which is also related to internal energy storage, suppresses learning and memory.

This is an important study that extends our knowledge on OA activity in learning and memory and the effects the metabolic state has on learning and memory. The authors nicely use the genetic tools available in flies to try and unravel the complex circuitry of metabolic state level, OA activity and learning and memory.<br /> Nevertheless, I do have some comments that I think require attention:

1. The authors use RNAi to reduce the level of glycogen synthase or glycogen phosphorylase. These manipulations are expected to affect the level of glycogen. Using specific drivers the authors attempt to manipulate glycogen level at the muscles and fat bodies and examine how this affects learning and memory. The conclusions of the authors arise solely from the manipulation intended (i.e. the genetics). However, the authors also directly measured glycogen levels at these organs and those do not follow the manipulation intended, i.e. the RNAi had very limited effect on the glycogen level. Nevertheless, these results are ignored.

2. The authors claim in the summary that OA is not required for STM. However, according to one experiment OA is required for STM as Tbh mutants cannot form STM. In another experiment OA is suppressive to STM as wt flies fed with OA cannot form STM. Therefore, it is very difficult to appreciate the actual role of OA on STM.

3. The authors use t-test and ANOVA for most of the statistics, however, they did not perform normality tests. While I am quite sure that most datasets will pass normality test, nevertheless, this is required.

4. While it is logical to assume that OA neurons are upstream to R15A04 DA neurons, I am not sure this really arises from the experiment that is presented here. It is well established that without activity in R15A04 DA neurons there is no LTM. Since OA acts to decrease LTM, can one really conclude anything about the location of OA effect when there is no learning?

5. It is unclear how expression of a dominant negative form of insulin receptor (InR) in OA neurons can rescue the lack of OA due to the Tbh mutation. If OA neurons cannot release anything to the presumably downstream DA neurons, how can changing their internal signaling has any effect?

While I stressed some comments that need to be addressed, the overall take-home message of the manuscript is supported and the authors do show that the metabolic state of the animal affects learning and memory. I do think though, that some more caution is required for some of the conclusions.

Reviewer #1 (Public Review):

She et al studied the evolution of gene expression reaction norms when individuals colonise a new environment that exposes them to physiologically challenging conditions. Their objective was to test the "plasticity first" hypothesis, which suggest that traits that are already plastic (their value changes when facing a new environment compared to the original environment) facilitates the colonisation of novel environments, which, if true, would be predicted to result in the evolution of gene expression values that are similar in the population that colonised the new environment and evolved under these particular selection pressures. To test this prediction, they studied gene expression in cardiac and muscle tissues in individuals originating from three conditions: lowland individuals in their natural environment (ancestral state), lowland individuals exposed to hypoxia (the plastic response state), and a highland population facing hypoxia for several generations (the coloniser state). They classified gene expression patterns as maladaptive or adaptive in lowland individuals responding to short term hypoxia by classifying gene expression patterns using genes that differed between the ancestral state (lowland) and colonised state (highland). Genes expressed in the same direction in lowland individuals facing hypoxia (the plastic state) as what is found in the colonised state are defined as adaptative, while genes with the opposite expression pattern were labelled as maladaptive, using the assumption that the colonised state must represent the result of natural selection. Furthermore, genes could be classified as representing reversion plasticity when the expression pattern differed between the plasticity and colonised states and as reinforcement when they were in the same direction (for example more expressed in the plastic state and the colonised state than in the ancestral state). They found that more genes had a plastic expression pattern that was labelled as maladaptive than adaptive. Therefore, some of the genes have an expression pattern in accordance with what would be predicted based on the plasticity-first hypothesis, while others do not.

As pointed out by the authors themselves, the fact that temperature was not included as a variable, which would make the experimental design much more complex, misses the opportunity to more accurately reflect the environmental conditions that the colonizer individuals face at high altitude. Also pointed out by the authors, the acclimation experiment in hypoxia lasted 4 weeks. It is possible that longer term effects would be identifiable in gene expression in the lowland individuals facing hypoxia on a longer time scale. Furthermore, a sample size of 3 or 4 individuals per group depending on the tissue for wild individuals may miss some of the natural variation present in these populations. Stating that they have a n=7 for the plastic stage and n= 14 for the ancestral and colonized stages refers to the total number of tissue samples and not the number of individuals, according to supplementary table 1.

Impact of the work:

There has been work showing that populations adapted to high altitude environments show changes in their hypoxia response that differs from the short-term acclimation response of lowland population of the same species. For example, in humans, see Erzurum et al. 2007 and Peng et al. 2017, where they show that the hypoxia response cascade, which starts with the gene HIF (Hypoxia-Inducible Factor) and includes the EPO gene, which codes for erythropoietin, which in turns activates the production of red blood cell, is LESS activated in high altitude individuals compared to the activation level in lowland individuals (which gives it its name). The present work adds to this body of knowledge showing that the short-term response to hypoxia and the long term one can affect different pathways and that acclimation/plasticity does not always predict what physiological traits will evolve in populations that colonize these environments over many generations and additional selection pressure (UV exposure, temperature, nutriment availability).

Altogether, this work provides new information on the evolution of reaction norms of genes associated with the physiological response to one of the main environmental variables that affects almost all animals, oxygen availability. It also provides an interesting model system to study this type of question further in a natural population of homeotherms.

Erzurum, S. C., S. Ghosh, A. J. Janocha, W. Xu, S. Bauer, N. S. Bryan, J. Tejero et al. "Higher blood flow and circulating NO products offset high-altitude hypoxia among Tibetans." Proceedings of the National Academy of Sciences 104, no. 45 (2007): 17593-17598.

Peng, Y., C. Cui, Y. He, Ouzhuluobu, H. Zhang, D. Yang, Q. Zhang, Bianbazhuoma, L. Yang, Y. He, et al. 2017. Down-regulation of EPAS1 transcription and genetic adaptation of Tibetans to high-altitude hypoxia. Molecular biology and evolution 34:818-830.

Reviewer #2 (Public Review):

This is a well-written paper using gene expression in tree sparrow as model traits to distinguish between genetic effects that either reinforce or reverse initial plastic response to environmental changes. Tree sparrow tissues (cardiac and flight muscle) collected in lowland and highland populations subject to hypoxia treatment were profiled for gene expression and compared in 1) highland birds; 2) lowland birds under normal conditions to test for differences in directions of changes between initial plastic response and subsequent colonized response.

The authors clarified several points and made revisions according to my comments. It is good to know that the highland and lowland samples were collected and processed at the same time and the previous publication reported part of the data. My concerns regarding the conclusions about reversal versus reinforcement remain even after the additional analyses. Further studies are needed to confirm these results.

Reviewer #1 (Public Review):

The authors were seeking to improve understanding of how wind and wave action affect the use of energetically demanding wing flapping and running by albatross engaged in takeoff flight. To accomplish this in the complex and challenging environment in which albatross live, the authors sought to use accelerometry and geographic positioning to infer patterns of locomotion, flight orientation relative to the prevailing wind, and wave height during takeoff.

The major strength of the methods and results is that the use of accelerometry and novel interpretations of data from a geographic positioning system provides new insight into the use of waves by albatross and how the effects of wave magnitude interact with wind to modulate energy demands during takeoff. Weaknesses of the approach are due to the challenging environmental conditions in which albatross live. The interpretation of accelerometry data was not validated using a subset of the sample synchronized with video (prior validation was cited for shearwaters). The interpretation of wind direction relative to flight path is based on the behavior of the bird without concurrent measures of local wind velocity.

The authors achieved their aims, and their results support their conclusions.

Although it is generally understood that albatross and many other birds choose to takeoff into the wind to reduce energetic costs, the authors provide novel quantitative data on this behavior. Their results on the effects of wave height and the interactions between wave height and wind provide novel insight into how albatross harvest energy from their complicated and dynamic environment to reduce the energy they must output to get into the air. In particular, the new insight into the effects of wave height should revise understanding among ornithologists, ocean ecologists and those who study the mechanics of animal locomotion. The use of accelerometry and geographic positioning systems to measure flight behavior and ocean ecology should inspire other researchers to adopt similar methods.

Albatross live in a complex and poorly understood environment that is likely to be threatened by climate change. This research provides worthwhile new insight into how wind and wave action affect takeoff in albatross, and can therefore improve insight into how changes in these variables with climate change may affect the distribution of albatross populations.

Reviewer #2 (Public Review):

The authors used cutting-edge bio-telemetry technology to decipher the roles of wind speed and wave height on the take-off of albatrosses from the water surface. They revealed that each of these factors contributes to take-off in a unique way with interesting interactions of the two factors. The authors achieved their objectives and their results support their conclusions. This work will set new standards in integrating information about bird movement and environmental conditions experienced by the bird in a comprehensive, integrative and hypothesis-driven framework. The approach of the authors is highly advanced, providing heuristic insights for many additional systems where organisms are influenced by, and respond to small-scale environmental conditions.

Reviewer #3 (Public Review):

The present study used novel data logging devices to record the foraging behavior of wandering albatrosses. Specifically, the authors showed how localized winds and wave heights influence their ability to take off from the sea surface, which is the most expensive behavior they engage in while foraging. There is no better platform for this initial work because these birds are so large, the equipment they can carry without creating significant impact is tremendous.

The results were impressive, presented well, and the paper generally written in an accessible way to readers with less knowledge. The authors provide a convincing set of results that support the aims and conclusions. The theory and application could be used to inform our understanding of flight behavior in other seabirds.

Although the idea of taking off from the sea surface may sound trivial, it is essential to understand that albatrosses and other soaring seabirds have wings that are adapted for soaring (i.e. long and narrow). The trade off however, is that powered flight through wing flapping is energetically expensive because the wings have a shallow amplitude and generate less power compared to a shorter, wider wing. Thus, wind is everything and this study shows how wind facilitates the ability of the birds to gain flight using wind and waves. Awesome!

Reviewer #1 (Public Review):

The manuscript provides analyses on a very complete dataset on weight and length growth, as well as several physiological markers related to growth, in bonobos. Moreover, there is a good overview of the presence of adolescent growth spurts in non-human primates, by reviewing published data, in comparison to their own dataset. They discuss the need to consider scaling laws when interpreting and comparing growth curves of different species and variables.

The manuscript is very well written, the sample is large, and the methods are well explained. It seems they have analyzed a very complete dataset. Also, the discussion and the references supporting the findings are complete.

The main weakness of this manuscript is that they do not provide a direct comparison with previously analyzed datasets in other species, using their own method (in part maybe because there is not available data, but just published figures).

On the other side, conclusions are well supported by the results, and the previously published datasets are discussed in the manuscript, although not in detail.

Reviewer #2 (Public Review):

This work sheds new light on the growth trajectory of Bonobo and contributes heavily to the discussion of the exclusivity of certain aspects of growth in modern humans. These results are also interesting as long as they are based on the study of the largest sample ever considered in the study of the growth of this species by including morphometric measurements as well as endocrinological factors.

The authors approach the study of the presence of growth spurs (GS) in Bonobo on the basis that GS are exclusive to the growth in modern humans. This idea is fairly widespread, however studies on non-human primates have shown an acceleration of growth during adolescence in several species, these works are recalled, presented and discussed by the authors. The originality of this work lies in highlighting the importance of scaling in studies of growth trajectories. The absence of GS in Bonobo but also in other primate species may result from not considering the conjunction of weight and height in the analysis of growth, because the pronounced changes in the speed of the height are in relation to the speed of changes in weight and this is modified according to the size/age. The authors apply scaling corrections to their results and the GS become evident (or more obvious) in Bonobo. Thus, the exclusivity of GS in growth in modern humans may in fact result only by the application of analytical approach not very appropriate in non-human primates.

Reviewer #1 (Public Review):

This paper describes the discovery, functional analysis and structure of TcaP, a protein encoded by the Vibrio phage satellite PLE that forms a size-determining scaffold around PLE procapsids made from helper phage ICP1 structural proteins. The system displays a fascinating similarity to the P2/P4 system, which had previously been unique in its use of a size-determining external scaffolding protein, Sid. The work is interesting, comprehensive and of high quality. The presentation could be improved as listed in the suggestions below.

An interesting observation is that PLE appears to be dependent on small capsids for efficient transduction. This is not completely surprising if the element uses a cos site type mechanism for packaging, since this requires an integer number of genomes to be packaged when the capsid is full, and this might be more difficult to accomplish when the helper capsid is much larger than the satellite, as is the case with ICP1. The authors mention in a few places that this is the first known satellite to have this requirement. However, this is not quite correct: a similar defect was seen in phi12/SaPIbov5, where the large phi12 capsid was not quite the right size for either two or three copies of the wild-type ("unevolved") SaPIbov5 (Carpena et al. 2016).

The authors present several micrographs showing capsids formed in the presence or absence of wildtype or mutant TcaP and CP (Fig. 1, Fig 2., Fig 3). However, each micrograph shows only a handful of particles of the "correct" size, in addition to a few shells that are aberrant or of a different size. I miss a more statistically rigorous enumeration of shells of different size (PLE or ICP1 sized, or different), empty vs. full, aberrant shells etc. This could be presented as a size distribution graph, a histogram or in table form.

In the abstract, the term "divergent satellite P4" is vague and unclear. Divergent from what? Probably they mean distinct from or unrelated to PLE. Please clarify.

How do they know that gp123 is a decoration protein? Was this previously determined, does it have (sequence) similarity to other known decoration proteins, or is it simply the most likely designation based on its position in the genome?

Although the reconstruction and modeling statistics are good, it is difficult to assess the quality of the map and the model from the presented figures. Details of the density and FSC curves (half-map and model-to-map) should be shown. It is also difficult to see the TcaP structure and how it compares to Sid from the figures presented.

Introduction, Paragraph 3: "...which is the number of coat proteins divided by 60" is not strictly speaking the definition of T number. The T number corresponds to the number of subtriangles that one triangular face of the icosahedron is divided into. It corresponds to the number of coat proteins divided by 60 in the canonical case, but in tailed phages, 5 copies are removed to make way for the portal protein. (Other viruses could be described as having architecture corresponding to a specific T number, but with divergent numbers of subunits, e.g. adenoviruses or polyomaviruses.)

Reviewer #2 (Public Review):

Phage satellites are fascinating elements that have evolved to hijack phages for induction, packaging, and transfer, promoting their widespread dissemination in nature. It is remarkable how different satellites use conserved strategies of parasitism, utilising unrelated proteins that perform similar roles in their cognate elements. In the current manuscript, Dr. Seed and coworkers elucidated the mechanism used by one family of satellites, the PLEs, to produce small capsids, a process that inhibits phage reproduction while increasing PLE transmission. The work is presented beautifully, and the results are astonishing. The authors identified the gene responsible for generating the small capsids, characterised its role in the PLE transfer and phage inhibition, and determined the structure of the PLE-sized small capsids. It is a truly impressive piece of work.

Reviewer #3 (Public Review):

The manuscript by Boyd and co-authors "A Vibrio cholerae viral satellite maximizes its spread and inhibits phage by remodelling hijacked phage coat proteins into small capsids" reports important results related to self-defending mechanisms that bacteria are used against phages that infect them. It has been shown previously that bacteria produce phage-inducible chromosomal island-like elements (PLE) that encode proteins that are integrated into bacterial genome. These proteins are used by bacteria to amend the phage capsids and to create phage-like particles (satellites) that move between cells and transfer the genetic material of PLE to another bacteria. That study highlights the interactions between a PLE-encoded protein, TcaP, and capsid proteins of the phage ICP1.

The manuscript is well written, provides a lot of new information and the results are supported by biochemical analysis.

Reviewer #1 (Public Review):

This is a paper describing in detail the seasonal movements of a vole-eating raptor, the rough-legged buzzard, from their Arctic breeding areas to the temperate wintering areas and back, in an annual cycle perspective. The basis of the descriptions (using satellite tags) is state of the art, and so are the analyses on aspects of time and space. Of particular relevance is the degree in which this study successfully pinpoints the ecological shaping factors, food availability of course, in this case strongly affected by snow cover (which can be remotely sensed over large areas). The authors claim a new migration pattern called 'foxtrot' with phases with rapid and phases with slower migration movements.

My concern with this paper is the framing. A story on the how and why of these continental movements in response to snow and other habitat features would be a grand contribution.

Reviewer #2 (Public Review):

This preprint by Pokrovsky and coworkers is a descriptive study reporting on non-breeding itinerant behaviour of an intrapalearctic migratory raptor, the rough-legged buzzard, and relating such non-breeding movements to snow cover across the European non-breeding range. The article is based on long-term GPS tracking data from a relatively large sample of individuals (n=43) that were equipped with state-of-the-art tracking devices in the Russian Arctic during 2013-2019. The results show that, upon breeding, buzzards migrated rapidly to southern non-breeding areas, located in open areas north of the Black and Caspian seas, where they perform continuous directional movements at a slower pace, initially moving SW (Oct to Jan) and then progressively moving NE (Feb to Apr) before embarking on rapid spring migration. It is suggested that such itinerant behaviour follows variation (expansion and retreat) of snow cover across the non-breeding range.

The results are definitely useful for researchers investigating the ecological drivers of bird movement patterns. The paper is generally well-written and the analytical framework is solid. However, there are significant weaknesses in the theoretical framework, unwarranted claiming of novelty, and interpretation of the data. Below are key points that the authors may wish to consider.

1) The authors underemphasize the fact that what they term 'fox-trot' migration is actually a well-known pattern for many other migratory species, both in the Nearctic and in the Afro-Palearctic migration systems. Such behaviour has previously been identified as 'itinerant', involving an alternation of stopovers and movements between different short-term non-breeding residency areas, and it seems that the pattern the authors report for this particular species is perfectly in line with such previous evidence. For instance, this is well-documented among migratory raptors, such as the Montagu's harrier, a lesser kestrel or black kite, that exploit Sahelian savannahs, where large spatio-temporal variation in greenness and hence resource availability occurs. And, besides the mentioned cuckoos and nightingales, there are studies of red-backed shrikes suggesting the same, as well as of tree swallows in the Nearctic. Therefore, the authors should avoid claiming novelty for this study and introducing unnecessary and confusing new terms in the literature (i.e. the 'fox-trot' migration patterns) when these are definitely not strictly needed as they have been previously observed and defined otherwise. Reference to all this previous body of literature is only hinted at and should be considerably expanded. The final sentence of the abstract, involving a general recommendation for future work, is definitely not warranted. Sentences such as 'We used the rough-legged buzzard as a model..." are also similarly unwarranted. This is simply a descriptive study reporting on such behaviour in yet another migratory species. The predictions paragraph is also overlong and could be considerably condensed.

2) The term 'migration' associated to so-called 'fox-trot' movements (see Fig. 1) is also highly confusing and possibly incorrect, as it is not in line with the commonly accepted definition of 'migration' (i.e. mass back and forth movements from the same areas). Apparently, the authors do not provide any evidence that the birds are moving back and forth from the same areas during the non-breeding period (i.e., there is no mention of site fidelity between early and late wintering areas, but judging from fall and spring migration distances it seems this is definitely not the case). 'Non-breeding itinerancy' is clearly a more appropriate term to describe this behaviour. More generally, the reference to 'winter migration', which is often mentioned in the manuscript, is not correct and should be amended.

3) The current title is unnecessarily general (it may recall rather a review or meta-analysis) and not adequately describing the content of the manuscript. It is not at all clear how the terms 'Conservation' and 'Anthropocene' are related to the content of the study (unless one believes that this is because any study of wildlife is aimed at its conservation, which is of course untrue, and that the study has been performed in the Anthropocene, which is the case for all wildlife studies carried out after 1950-1960). In order to be informative, the title should more tightly reflect the content of the article. A valid alternative would be 'Itinerant non-breeding behaviour of an intra-Palaearctic migratory raptor', far more adequate and informative. Although it might be worthwhile mentioning the association between movements and snow cover (or ecological conditions more generally) already in the title, perhaps that link is too indirect as currently reported in the manuscript. There are several possibilities to provide a more direct link between movements and snow cover, such as e.g. performing habitat selection analysis with respect to snow cover. Plotting temporal progression of snow cover (average) against movements (e.g. by showing monthly home ranges against snow cover) would help visualizing the association between snow cover and movement patterns.

4) The text, particularly the Introduction and (even more so) the Discussion, would benefit from profound reframing in light of the above comments. Any link to conservation is too weak and should be removed or considerably toned down. Moreover, the species is not of conservation interest (IUCN = Least Concern), as it has an extremely large range and population size, with largely fluctuating and non-declining populations (whose dynamics are related to Arctic small rodent cycles). Unless the authors are able to make prediction on how these movements will be affected by climate change (e.g. by using species distribution models or similar approaches), the link to the Anthropocene and to conservation is mostly unwarranted. In general, reference to 'winter' should be avoided and replaced with 'non-breeding season', which is a more general term.

Reviewer #1 (Public Review):

The authors Wang et al. present a study of a mouse model K74R that they claim can extend the life span of mice, and also has some anti-cancer properties. Importantly, this mechanism seems to be mediated by the hematopoietic system, and protective effects can be transferred with bone marrow transplantation.

The authors need to be more specific in the title and abstract as to what is actually novel in this manuscript (a single tumor model), and what relies on previously published data (lifespan). Because many of these claims derive from previously published data, and the current manuscript is an extension of previously published work. The authors need to be more specific as to the actual data they present (they only use the B16 melanoma model) and the actual novelty of this manuscript.

Especially experiments on life span are published and not sufficiently addressed in this actual paper, as the title would suggest.

Reviewer #2 (Public Review):

The manuscript by Wang et al. follows up on the group's previous publication on KLF1 (EKLF) K47R mice and reduced susceptibility to tumorigenesis and increased life span (Shyu et al., Adv Sci (Weinh). Sep 2022;9(25):e2201409. doi:10.1002/advs.202201409). In the current manuscript, the authors have described the dependence of these phenotypes on age, gender, genetic background, and hematopoietic translation of bone marrow mononuclear cells. Considering the current study is centered on the phenotypes described in the previous study, the novelty is diminished. Further, there are significant conceptual concerns in the study that make the inferences in the manuscript far less convincing. Major concerns are listed below:

1. The authors mention more than once in the manuscript that KLF1 is expressed in range of blood cells including hematopoietic stem cells, megakaryocytes, T cells and NK cells. In the case of megakaryocytes, studies from multiple labs have shown that while EKLF is expressed megakaryocyte-erythroid progenitors, EKLF is important for the bipotential lineage decision of these progenitors, and its high expression promotes erythropoiesis, while its expression is antagonized during megakaryopoiesis. In the case of HSCs, the authors reference to their previous publication for KLF1's expression in these cells- however, in this study nor in the current study, there is no western blot documented to convincingly show that KLF1 protein is expressed at detectable levels in these cells. For T cells, the authors have referenced a study which is based on ectopic expression of KLF1. For NK cells, the authors reference bioGPS: however, upon inspection, this is also questionable.

2. The current study rests on the premise that KLF1 is expressed in HSCs, NK cells and leukocytes, and the references cited are not sufficient to make this assumption, for the reasons mentioned in the first point. Therefore, the authors will have to show both KLF1 mRNA and protein levels in these cells, and also compare them to the expression levels seen in KLF1 wild type erythroid cells along with knockout erythroid cells as controls, for context and specificity.

3. To get to the mechanism driving the reduced susceptibility to tumorigenesis and increased life span phenotypes in EKLF K74R mice, the authors report some observations- However, how these observations are connected to the phenotypes is unclear.<br /> a. For example, in Figure S3, they report that the frequency of NK1.1+ cells is higher in the mutant mice. The significance of this in relation to EKLF expression in these cells and the tumorigenesis and life span related phenotypes are not described. Again, as mentioned in the second point, KLF1 protein levels are not shown in these cells.<br /> b. In Figure 4, the authors show mRNA levels of immune check point genes, PD-1 and PD-l1 are lower in EKLF K74R mice in PB, CD3+ T cells and B220+ B cells. Again, the questions remain on how these genes are regulated by EKLF, and whether and at what levels EKLF protein is expressed in T cells and B cells relative to erythroid cells. Further, while the study they reference for EKLF's role in T cells is based on ectopic expression of EKLF in CD4+ T cells, in the current study, CD3+ T cells are used. Also, there are no references for the status of EKLF in B cells. These details are not discussed in the manuscript.

4. The authors perform comparative proteomics in the leukocytes of EKLF K74R and WT mice as shown in Figure S5. What is the status of EKLF levels in the mutant lysate vs wild type lysates based on this analysis? More clarity needs to be provided on what cells were used for this analysis and how they were isolated since leukocytes is a very broad term.

5. In the discussion the authors make broad inferences that go beyond the data shown in the manuscript. They mention that the tumorigenesis resistance and long lifespan is most likely due to changes in transcription regulatory properties and changes in global gene expression profile of the mutant protein relative to WT leukocytes. And based on reduced mRNA levels of Pd-1 Pd-l1 genes in the CD3+ T cells and B220+ B cells from mutant mice, they "assert" that EKLF is an upstream regulator of these genes and regulates the transcriptomes of a diverse range of hematopoietic cells. The lack of a ChIP assay to show binding of WT EKLF on genes in these cells and whether this binding is reduced or abolished in the mutant cells, make the above statements unsubstantiated.

6. Where westerns are shown, the authors need to show the molecular weight ladder, and where qPCR data are shown for EKLF, it will be helpful to show the absolute levels and compare these levels to those in erythroid cells, along the corresponding EKLF knock out cells as controls.

7. Figure S1D does not have a figure legend. Therefore, it is unclear what the blot in this figure is showing. In the text of the manuscript where they reference this figure, they mention that the levels of the mutant EKLF vs WT EKLF does not change in peripheral blood, while in the figure they have labeled WBCs for the blot, and the mRNA levels shown do seem to decrease in the mutant compared to WT peripheral blood.

Reviewer #3 (Public Review):

Hung et al provide a well-written manuscript focused on understanding how Eklf mutation confers anticancer and longevity advantages in vivo. The work is fundamental and the data is convincing although several details remain incompletely elucidated. The major strengths of the manuscript include the clarity of the effect and the appropriate controls. For instance, the authors query whether Eklf (K74R) imparts these advantages in a background, age, and gender dependent manner, demonstrating that the findings are independent. In addition, the authors demonstrate that the effect is not the consequence of the specific amino acid substitution, with a similar effect on anticancer activity. Furthermore, the authors provide some evidence that PD-1 and PDL-1 are altered in Eklf (K74R) mice.

Finally, they demonstrate that the effects are transferrable with BMT. Several weaknesses are also evidence. For instance, only melanoma is tested as a model of cancer such that a broad claim of "anti-cancer activity" may be somewhat of an overreach. It is also unclear why a homozygous mutation is needed when only a small fraction of cells during BMT can confer benefit. It is also difficult to explain how transplanted donor Eklf (K74R) HSCs confer anti-melanoma effect 7 and 14 days after BMT. Furthermore, it would be useful to see whether there are virulence marker alterations in the melanoma loci in WT vs Eklf (K74R) mice. Finally, the data in Fig 4c is difficult to interpret as decreased PD-1 and PDL-1 after knockdown of EKLF in vitro is not a useful experiment to corroborate how mutation without changing EKLF expression impacts immune cells. The work is impactful as it provides evidence that healthspan and lifespan may be modulated by specific hematological mutation but the mechanism by which this occurs is not completely elucidated by this work.

Reviewer #1 (Public Review):

In this manuscript, Bockorny, Muthuswamy, and Huang et al. performed proteomics analysis of plasma extracellular vesicles (EVs) from pancreatic ductal adenocarcinoma (PDAC) patients and patients with benign pancreatic diseases (chronic pancreatitis and intraductal papillary mucinous neoplasm, IPMN) to develop a 7-EV protein signature that predicts PDAC. Moveover, the authors identified PSMB4, RUVBL2, and ANKAR as being associated with metastasis. These studies provide important insight into alterations of EVs during PDAC progression and the data supporting predict PDAC with EV protein signatures are solid. However, there are certain concerns regarding the rigor and novelty of the data analysis and interpretation, as well as the clinical implications, as detailed below.

1. Plasma EVs were characterized by transmission electron microscopy and nanoparticle tracking analysis to confirm their morphology and size. The authors should also include an analysis of putative EV markers (e.g., tetraspanins, syntenin, ALIX, etc.) to confirm that the analyzed particles are EVs.

2. The authors identified multiple over-expressed proteins in PDAC based on their fold change and p-value; however, due to the heterogeneity of PDAC, it is necessary to show a heatmap displaying their abundance in all samples. High fold change does not necessarily indicate consistently high abundance in all PDAC samples.

3. PSMB4, RUVBL2, and ANKAR were identified as being associated with metastasis. The authors state that they intended to distinguish early and late-stage cancer samples, but it is unclear why they chose to compare metastatic and non-metastatic samples, as the non-metastatic group also includes late-stage cancer samples. This sentence should be rephrased to more accurately reflect the sample types profiled.

4. Non-metastatic and metastatic patients were separated based on global protein abundance. The samples within each group display significant heterogeneity with, some samples displaying similar patterns although they were classified into different groups (Figure 3A), and the samples within the same group, particularly the metastasis group, did not consistently exhibit similar patterns of protein abundance. The authors should clarify this point.

5. The authors performed the survival analysis on a set of EV proteins but did not specify the origin of these markers or how many markers were examined. The authors should show their abundances across different groups, such as different stages and metastasis status.

6. The classification model yielded a 100% accuracy, which may refer to AUC, in their discovery cohort, but it decreased to 89% in the independent cohort. This suggests that the authors have encountered overfitting issues with their model, where it performed well on the discovery cohort but did not generalize well to the independent cohort. The authors should clarify this point. The AUC score of the 7-EV signature is 0.89 and is not equivalent to prediction accuracy. In order to demonstrate prediction accuracy, the authors should show the confusion matrix of training and testing data as well as other evaluation metrics, such as accuracy, precision, and recall.

7. The authors should include more details of their model and the process of selection of signatures to enhance the reproducibility and transparency of their methods.

Reviewer #2 (Public Review):

The authors intended to identify a protein signature in extracellular vesicles of serum to distinguish pancreatic ductal adenocarcinoma from benign pancreatic diseases.

A major strength of the work presented is the valuable profiling of a significant number of patient samples, with a rich cohort of patients with pancreatic cancer, benign pancreatic diseases, and healthy controls. However, despite the strong cohorts presented, the numbers of patient samples for benign pancreatic diseases as well as controls were very limited.

Also, the method used to isolate vesicles, EVTrap, recognizes double bilayers, which means that it can detect cellular debris and apoptotic bodies, which are very common in the circulation of patients that are undergoing chemotherapy. It would be important to identify the patients that are therapy naïve and the ones that are not because of this possible bias. Additionally, the transmission electron microscopy data reflect this heterogeneity of the samples, also with little identification of double bilayered vesicles. It would be important to identify some extracellular vesicles markers in those preparations to strengthen the quality of the samples analysed. What is more, previously published work with this same methodology identifies around 2000 proteins per sample. It would be important to explain why in this study there seems to be a reduction in more than 50% of the amount of proteins identified in the vesicles.

One of the proteins that constantly surges on the analysis is KRT20. It would be important to proceed with the analysis by first filtering out possible contaminants of the proteomics, of which keratins are the most common ones. Finally, none of the 7-extracellular vesicle protein signatures has been validated by other techniques, such as western blot, in extracellular vesicles isolated by other, standard, methods, such as size exclusion chromatography.

A distinct technique for protein analysis was done but not a different method of isolation of these vesicles. This would strengthen the results and the origin of the proteins.

The conclusions that are reached do not fully meet the proposed aims of the identification of a protein signature in circulating extracellular vesicles that could improve early detection of the disease. The authors did not demonstrate the superiority of detection of these proteins in extracellular vesicles versus simply performing an ELISA, nor their superiority with respect to the current standard procedure for diagnosis.

The authors also suggest that profiling of circulating extracellular vesicles provides unique insights into systemic immune changes during pancreatic cancer development. How is this better than a regular hemogram is not clear.

Finally, it would be important to determine how this signature compares with many others described in the literature that have the exact same aim. Why and how would this one be better?

Reviewer #3 (Public Review):

This work investigates the use of extracellular vesicles (EVs) in blood as a noninvasive 'liquid biopsy' to aid in the differentiation of patients with pancreatic cancer (PDAC) from those with benign pancreatic disease and healthy controls, an important clinical question where biopsies are frequently non-diagnostic. The use of extracellular vesicles as biomarkers of disease has been gaining interest in recent history, with a variety of published methods and techniques, looking at a variety of different compositions ('the molecular cargo') of EVs particularly in cancer diagnosis (Shah R, et al, N Engl J Med 2018; 379:958-966).

This study adds to the growing body of evidence in using EVs for earlier detection of pancreatic cancer, identifying both new and known proteins of interest. Limitations in studying EVs, in general, include dealing with low concentrations in circulation and identifying the most relevant molecular cargo. This study provides validation of assaying EVs using the novel EVtrap method (Extracellular Vesicles Total Recovery And Purification), which the authors show to be more efficient than current standard techniques and potentially more scalable for larger clinical studies.

The strength of this study is in its numbers - the authors worked with a cohort of 124 cases, 93 of them which were PDAC samples, which are considered large for an EV study (Jia, E et al. BMC Cancer 22, 573 (2022)). The benign disease group (n=20, between chronic pancreatitis and IPMNs) and healthy control groups (n=11) were relatively small, but the authors were not only able to identify candidate biomarkers for diagnosis that clearly stood out in the PDAC cohort, but also validate it in an independent cohort of 36 new subjects.

Proteins they have identified as associated with pancreatic cancer over benign disease included PDCD6IP, SERPINA12, and RUVBL2. They were even able to identify a set of EV proteins associated with metastasis and poorer prognosis, which include the proteins PSMB4, RUVBL2 and ANKAR and CRP, RALB and CD55. Their 7-EV protein signature yielded an 89% prediction accuracy for the diagnosis of PDAC against a background of benign pancreatic diseases that is compelling and comparable to other studies in the literature (Jia, E. et al. BMC Cancer 22, 573 (2022)).

The limitations of this study are its containment within a single institution - further studies are warranted to apply the authors' 7-EV protein PRAC panel to multiple other cases at other institutions in a larger cohort.

Reviewer #2 (Public Review):

This manuscript identified a long noncoding RNA, PITAR (p53 Inactivating TRIM28 associated RNA), as an inhibitor of p53. PITAR is highly expressed in glioblastoma (GBM) and glioma stem-like cells (GSC). The authors found that TRIM28 mRNA, which encodes a p53-specific E3 ubiquitin ligase, is a direct target of PITAR. PITAR interaction with TRIM28 RNA stabilized TRIM28 mRNA, which resulted in increased TRIM28 protein levels, enhanced p53 ubiquitination, and attenuated DNA damage response. While PITAR silencing inhibited the growth of WT p53 containing GSCs in vitro and reduced glioma tumor growth in vivo, its overexpression enhanced the tumor growth and promoted resistance to Temozolomide. DNA damage also activated PITAR, in addition to p53, thus creating an incoherent feedforward loop. Together, this study established an alternate way of p53 inactivation and proposed PITAR as a potential therapeutic target.

P53 is a well-established tumor suppressor gene contributing to cancer progression in many human cancers. It plays a vital role in preserving genome integrity and inhibiting malignant transformation. p53 is mutated in more than 50% of human cancers. In cancers that do not carry mutations in p53, the inactivation occurs through other genetic or epigenetic alterations. Therefore, further study of the mechanism of regulation of wt-p53 remains vital in cancer research. This study identified a novel LncRNA PITAR, which is highly expressed in glioblastoma (GBM) and glioma stem-like cells (GSCs) and interacts with and stabilizes TRIM28 mRNA, which encodes a p53-specific E3 ubiquitin ligase. TRIM28 can inhibit p53 through HDAC1-mediated deacetylation and direct ubiquitination in an MDM2-dependent manner. Thus, the overall impact of this study is high because of the identification of a novel mechanism in regulating wt-p53.

The other significant strengths of this manuscript included an apparent research strategy design and a clearly outlined and logically organized research approach. They provided both the in vitro and in vivo studies to evaluate the effect of PITAR. They offered reasonable control of the study by validating the results in cells with mutant p53. They also performed a rescue experiment to confirm the PITAR and TRIM28 relationship regulating p53. The conclusions were all supported by solid results. The overall data presentation is clear and convincing.

Reviewer #1 (Public Review):

In this manuscript by Wu et al., the authors present the high-resolution cryoEM structures of the WT Kv1.2 voltage-gated potassium channel. Along with this structure, the authors have solved several structures of mutants or experimental conditions relevant to the slow inactivation process that these channels undergo and which is not yet completely understood.

One of the main findings is the determination of the structure of a mutant (W366F) that is thought to correspond to the slow inactivated state. These experiments confirm results in similar mutants in different channels from Kv1.2 that indicate that inactivation is associated with an enlarged selectivity filter.

Another interesting structure is the complex of Kv1.2 with the pore-blocking toxin Dendrotoxin 1. The results show that the mechanism of the block is different from similar toxins, in which a lysine residue penetrates the pore deep enough to empty most external potassium binding sites.

The quality of the structural data presented in this manuscript is very high and allows for the unambiguous assignment of side chains. The conclusions are supported by the data. This is an important contribution that should further our understanding of voltage-dependent potassium channel gating. Specific comments are appended below.

1) In the mains text's reference to Figure 2d residues W18' and S22' are mentioned but are not labeled in the insets.

2) On page 8 there is a discussion of how the two remaining K+ ions in binding sites S3 and S4 prevent permeation K+ in molecular dynamics. However, in Shaker, inactivated W434F channels can sporadically allow K+ permeation with normal single-channel conductance but very reduced open times and open probability at not very high voltages.

3) The structures of WT in the absence of K+ show a narrower selectivity filter, however, Figure 4 does not convey this finding. In fact, the structure in Figure 4B is constructed at such an angle that it looks as if the carbonyl distances are increased, perhaps this should be fixed. Also, it is not clear how the distances between carbonyls given in the text on page 12 are measured. Is it between adjacent or kitty-corner subunits?

4) It would be really interesting to know the authors' opinions on the driving forces behind slow inactivation. For example, potassium flux seems to be necessary for channels to inactivate, which might indicate a local conformational change is the trigger for the main twisting events proposed here.

Reviewer #2 (Public Review):

There are four Kv1.2 channel structures reported: the open state, the C-type inactivated state, a dendrotoxin-bound state, and a structure in Na+.

A high-resolution crystal structure of the open state for a chimeric Kv1.2 channel was reported in 2007 and there is no new information provided by the cryoEM structure reported in this study.

The cryo-EM structure of the C-type inactivated state of the Kv1.2 channel was determined for a channel with the W to F substitution in the pore helix. A cryo-EM structure of the Shaker channel and a crystal structure of a chimeric Kv1.2 channel with an equivalent W to F mutation were reported in 2022. Cryo-EM structures of the C-type inactivated Kv1.3 channel are also available. All these previous structures have provided a relatively consistent structural view of the C-type inactivated state and there is no significant new information that is provided by the structure reported in this study.

A structure of the Kv1.2 channel blocked by dendrotoxin is reported. A crystal structure of charybdotoxin and the chimeric Kv1.2 channel was reported in 2013. Density for dendrotoxin could not be clearly resolved due to symmetry issues and so the definitive information from the structure is that dendrotoxin binds, similarly to charybdotoxin, at the mouth of the pore. A potential new finding is that there is a deeper penetration of the blocking Lys residue in dendrotoxin compared to charybdotoxin. It will however be necessary to use approaches to break the symmetry and resolve the electron density for the dendrotoxin molecule to support this claim and to make this structure significant.

The final structure reported is the structure of the Kv1.2 channel in K+ free conditions and with Na+ present. The structure of the KcsA channel by the MacKinnon group in 2001 showed a constricted filter and since then it has been falsely assumed by the K channel community that the lowering of K concentration leads to a construction of the selectivity filter. There have been structural studies on the MthK and the NaK2K channels showing a lack of constriction in the selectivity filter in the absence of K+. These results have been generally ignored and the misconception of filter constriction/collapse in the absence of K+ still persists. The structure of the Kv1.2 channel in Na+ provided a clear example that loss of K+ does not necessarily lead to filter constriction.<br /> The structure in Na+ is significant while the other structures are either merely reproductions of previous reports or are not resolved well enough to make any substantial claims.

Reviewer #3 (Public Review):

Wu et al. present cryo-EM structures of the potassium channel Kv1.2 in open, C-type inactivated, toxin-blocked and presumably sodium-bound states at 3.2 Å, 2.5 Å, 2.8 Å, and 2.9 Å. The work builds on a large body of structural work on Kv1.2 and related voltage-gated potassium channels. The manuscript presents a large quantity of structural work on the Kv1.2 channel, and the authors should be commended on the breadth of the studies. The structural studies seem well-executed (this is hard to fully evaluate because the current manuscript is missing a data collection and refinement statistics table). The findings are mostly confirmatory, but they do add to the body of work on this and related channels. Notably, the authors present structures of DTX-bound Kv1.2 and of Kv1.2 in a low concentration of potassium (with presumably sodium ions bound within the selectivity filter). These two structures add new information, but the studies seem somewhat underdeveloped - they would be strengthened by accompanying functional studies and further structural analyses. Overall, the manuscript is well-written and a nice addition to the field.

Reviewer #1 (Public Review):

The authors have previously employed micrococcal nuclease tethered to various Mcm subunits to the cut DNA to which the Mcm2-7 double hexamers (DH) bind. Using this assay, they found that Mcm2-7 DH are located on many more sites in the S. cerevisiae genome than previously shown. They then demonstrated that these sites have characteristics consistent with origins of DNA replication, including the presence of ARS consensus sequences, location of very inefficient sites of initiation of DNA replication in vivo, are free of nucleosomes, they contain a G-C skew and they locate to intergenic regions of the genome. The authors suggest, consistent with published single molecule results, that there are many more potential origins in the S. cerevisiae genome than previously annotated.

The results are convincing and are consistent with prior observations. The analysis of the origin associated features is informative.

Reviewer #2 (Public Review):

By mapping the sites of the Mcm2-7 replicative helicase loading across the budding yeast genome using high-resolution chromatin endogenous cleavage or ChEC, Bedalov and colleagues find that these markers for origins of DNA replication are much more broadly distributed than previously appreciated. Interestingly, this is consistent with early reconstituted biochemical studies that showed that the ACS was not essential for helicase loading in vitro (e.g. Remus et al., 2009, PMID: 19896182). To accomplish this, they combined the results of 12 independent assays to gain exceptionally deep coverage of Mcm2-7 binding sites. By comparing these sites to previous studies mapping ssDNA generated during replication initiation, they provide evidence that at least a fraction of the 1600 most robustly Mcm2-7-bound sequences act as origins. A weakness of the paper is that the group-based (as opposed to analyzing individual Mcm2-7 binding sites) nature of the analysis prevents the authors from concluding that all of the 1,600 sites mentioned in the title act as origins. The authors also show that the location of Mcm2-7 location after loading are highly similar in the top 500 binding sites, although the mobile nature of loaded Mcm2-7 double hexamers prevents any conclusions about the location of initial loading. Interestingly, by comparing subsets of the Mcm2-7 binding sites, they find that there is a propensity of at least a subset of these sites to be nucleosome depleted, to overlap with at least a partial match to the ACS sequence (found at all of the most well-characterized budding yeast origins), and a GC-skew. Each of which is a characteristic of previously characterized origins of replication.

Overall, this manuscript greatly broadens the number of sites that are capable of loading Mcm2-7 in budding yeast cells and shows that a subset of these additional sites act as replication origins. Although these sites do have a propensity to include a match to the ACS, these studies suggest that the mechanism of helicase loading in yeast and multicellular organisms is more similar than previously thought.

Reviewer #1 (Public Review):

The authors investigated the function of BATF in hepatic lipid metabolism. They found BATF alleviated high-fat diet (HFD)-induced hepatic steatosis. In addition, BATF could inhibit programmed cell death protein (PD)1 expression induced by HFD. By using over expression and transcriptional activity analysis, this study confirmed that BATF regulates fat accumulation by inhibiting PD1 expression and promoting energy metabolism. Then, they found PD1 antibodies alleviated hepatic lipid deposition. These data identified the regulatory role of BATF in hepatic lipid metabolism and that PD1 is a target for alleviation of NAFLD.

The conclusions of this manuscript are supported by data, but some remaining concerns need to be addressed.

1. There are different cells in liver tissue, in which BATF protein is expressed most.<br /> 2. The statistical data should be provided to support the liver specific over-expression of BATF.<br /> 3. For in vivo study, food intake is key data to exclude the change of energy intake.<br /> 4. For Fig.6 Since PD1 are also highly expressed in heart and spleen, how to exclude the effect of PD1 antibody on these tissues?

Reviewer #2 (Public Review):

In this manuscript, authors firstly investigated the role of a transcriptional factor BATF in hepatic lipid metabolism both in vivo and in vitro. By using a AAV transfection to overexpress BATF in liver, the mice with overexpression of BATF resisted the high fat diets induced obesity and attenuated the hepatic steatosis. Mechanically, the PD1 mediated its effect on lipid accumulation in hepatocyte and IL-27 mediated its effect on adiposity reduction in vivo.

Strength<br /> 1) This work found the transcription factor BATF was positive to reduce hepatic lipid accumulation and offered a potential target to treat NAFLD.<br /> 2) PD1 antibody is always used to treat cancer, authors here have developed its new function in metabolic disease. PD1 antibody could help mice to combat obesity and hepatic steatosis induced by high fat diets.<br /> 3) Overexpression of BATF in the liver not only decreased the lipid accumulation in the liver but also reduced the fat mass. IL-27 secretion in the liver was enhanced to affect the adipose tissue. The cross talk in liver and adipose tissue was also validated in this paper.

Weakness<br /> 1) BATF protein is also abundantly expressed in control hepatocyte, but the knockdown of BATF had no effect on lipid accumulation. Besides, the expression of BATF was elevated by high fat diets. So it will be interesting to investigate its role in the liver by using its hepatic conditional knockout mice.<br /> 2) The data for the direct regulation of BATF on PD1 and IL-27 is not enough, it is better to carry out CHIP experiment to further confirm it.

Reviewer #1 (Public Review):

This study delves into the impact of imidacloprid, an insecticide documented for its toxicity towards honeybees, on the development of bee larvae. The investigation involved exposing bee larvae to various concentrations of imidacloprid, and observing the resultant effects.

The findings of this study revealed that imidacloprid exerted a dose-dependent delay in the development of bee larvae, marked by reductions in body mass, width, and an overall decline in the growth index. Moreover, at elevated concentrations, imidacloprid was observed to impair neural transmission, induce oxidative stress, inflict damage to the gut, and inhibit hormones and genes essential for development. The larvae were found to engage antioxidant defense systems and deploy detoxification mechanisms to mitigate these effects.

However, the manuscript could be significantly enhanced through several improvements. Firstly, the structure of the manuscript warrants refinement to foster coherence and clarity. Additionally, there is a need for careful reevaluation of the concentrations of imidacloprid employed in the study, to ensure their relevance and applicability. In terms of references, greater attention to accuracy in citation is imperative.

Furthermore, while the authors have provided an overview of the general effects of imidacloprid on both vertebrates and invertebrates, the inclusion of a more exhaustive literature review with a specific focus on honey bees and other insects would bolster the context and significance of this research. This would be particularly beneficial in the introduction section, which should be subjected to a major revision.

In summary, this study offers preliminary evidence of the detrimental effects of imidacloprid on the development of bee larvae by interfering with molting and metabolism. This research holds potential as a valuable resource for assessing the risks posed by pesticides to juvenile stages of various animal species.

Reviewer #2 (Public Review):

This study provides evidence on the ability of sublethal imidacloprid doses to affect growth and development of honeybee larva. While checking the effect of doses that do not impact survival or food intake, the authors found changes in the expression of genes related to energy metabolism, antioxidant response, and P450 metabolism. The authors also identified cell death in the alimentary canal, and disturbances in levels of ROS markers, molting hormones, weight and growth ratio. The study strengths come from applying these different approaches to investigate the impacts of imidacloprid exposure. The study weaknesses are not providing an in-depth investigation of the mechanisms behind the impacts observed and not bringing the results in light of the current literature. For instance, the authors' hypothesis is based on two main points, the generation of ROS that leads to gut cell death and energy dysfunction, and the increased P450 expression. They propose this increases P450 expression which in turn increases energy consumption and could contribute to developmental retardation. There is however no investigation on the mechanisms of ROS generation (it could be through mitochondrial damage, Nox/ Duox activity, NOS activity, P450s activity, etc). A link between higher P450 expression and increased energy consumption leading to energy deprivation is also missing. It would also be important for the authors to provide a more complete literature review as previous works have investigated imidacloprid sublethal dose impacts in larval stages for bees and other insect models.

Reviewer #1 (Public Review):

This is a straightforward paper that uses TraDIS (high-density TnSeq) with Klebsiella pneumoniae to infer essential genes, and genes required for survival under various infection-relevant conditions. The gene sets identified, together with the raw sequence data, will be valuable resources for the Klebsiella research community. The evidence to support the lists of essential and conditionally-important genes is solid, although a few additional follow-up experiments would strengthen some of the claims made based on the TraDIS data.

1. The data strongly suggest that iron depletion in urine leads to conditional essentiality of some genes. It would be informative to test the single gene deletions (Figure 3G) for growth in urine supplemented with iron, to determine how many of those genes support growth in urine due to iron limitation.<br /> 2. Line 641. The authors raise the intriguing possibility that some mutants can "cheat" by benefitting from the surrounding cells that are phenotypically wild-type. Growing a fepA deletion strain in urine, either alone or mixed with wild-type cells, would address this question. Given that other mutants may be similarly "masked", it is important to know whether this phenomenon occurs.<br /> 3. In cases where there are disparities between studies, e.g., for genes inferred to be essential for serum resistance, it would be informative to test individual deletions for genes described as essential in only one study.

Reviewer #2 (Public Review):

This study presents a useful inventory of essential genes from an antibiotic-resistant K. pneumoniae strain to grow in a rich medium. The study also includes a catalogue of genes required to grow/survive in urine and in serum. The former is particularly interesting. The data is analyzed using adequate tools.

The authors leveraged TraDIS to identify essential genes of K. pneumoniae in LB, and those required to survive in urine, and serum. TraDIS is a well-established approach to investigate these aspects, and in fact, has also been already exploited in the case of K. pneumoniae to identify essential genes and those required for serum resistance. The strain used by the team is not probed by many other laboratories, making it difficult to assess the relevance in the context of K. pneumoniae population biology. Nonetheless, the authors have tried to compare their results against other published studies.

The descriptions of the method and analysis of the data are quite detailed; however considering that this work is mostly a bioinformatics one, it would have been interesting to go beyond the Ecl8 strain and make a detailed comparison against the other published data sets as well as consider the genes identified in the wider population structure of K. pneumonaie and other Enterobactericease (particularly E. coli and Salmonella).

The catalogue of genes may spark additional research to provide mechanistic insights into the contribution of the loci to the phenotypes (either urine and/or serum survival). These experiments are not included in the manuscript beyond the validation level achieved by constructing additional mutants using the Red system.

Reviewer #3 (Public Review):

In this study, Gray and coworkers use a transposon mutant library in order to define: (i) essential genes for K. pneumoniae growth in LB medium, (ii) genes required for growth in urine, (iii) genes required for resistance to serum, and complement-mediated killing. Although there are previous studies, using a similar strategy, to describe essential genes for K. pneumoniae growth and genes required for serum resistance, this is the first work to perform such a study in urine. This is important because these types of pathogens can cause urinary tract infections. Moreover, the authors performed the work using a highly saturated library of mutants, which makes the results more robust, and use a clinically relevant strain from a pathotype for which similar studies have not been performed yet. Besides applying the transposon mutant library coupled with high-throughput sequencing, the authors validate some of the most relevant genes required for each condition using targeted mutagenesis. This is clearly an important step to confirm that the results obtained from the library are reliable. Moreover, in vitro experiments involving complementation of urine with iron provide additional support to the results obtained with the mutants suggesting the importance of genes required for iron acquisition in a limiting-iron environment such as urine. Overall, the study is well-designed and written, and the methodology and analysis performed are adequate. The study would have benefited from in vivo experiments, including a mouse model of bacterial sepsis or urinary tract infections which could have demonstrated the role of the identified genes in the infection process. Nevertheless, the results obtained are informative for the scientific community in order to understand which genes are potentially more relevant in infections caused by K. pneumoniae. The identified genes could represent future targets for developing new therapies against a type of pathogen that is acquiring resistance to all available antibiotics. Below I include several comments regarding potential weaknesses in the methodology used:

- The study was done with biological duplicates. In vitro studies usually require 3 samples for performing statistical robust analysis. Thus, are two duplicates enough to reach reproducible results? This is important because many genes are analyzed which could lead to false positives. That said, I acknowledge that genes that were confirmed through targeted mutagenesis led to similar phenotypic results. However, what about all those genes with higher p and q values that were not confirmed? Will those differences be real or represent false positives? Could this explain the differences obtained between this and other studies?

- Two approaches are performed to investigate genes required for K.pneumoniae resistance to serum. In the first approach, the resistance to complement in serum is investigated. And here a total of 356 genes were identified to be relevant. In contrast, when genes required for overall resistance to serum are studied, only 52 genes seem to be involved. In principle, one would expect to see more genes required for overall resistance to serum and within them identify the genes required for resistance to complement. So this result is unexpected. In addition, it seems unlikely that 356 genes are involved in resistance to complement. Thus, is it possible false positives account for some of the results obtained?

Reviewer #1 (Public Review):

The present study combines quantitative histomorphometry, live cell imaging and tracking, functional analyses, and computational modeling to define potentially pathologic interactions between lung CD8 T cells and fibrocytes in human COPD. The authors use multiple technical approaches to establish the close proximity of CD8 T cells with fibrocytes in peri-bronchial tissue in COPD subjects that notably correlate with functional disease parameters (FEV1/FEV). Their follow-on studies identify specific chemokine pathways and inflammatory consequences of these interactions. Collectively, these seminal data acquired in a unified experimental context, provide support for pathogenic interactions between lung CD8 T cells and fibrocytes and now offer the consideration of mediators and pathways that may be amenable to therapeutic targeting. The strength of the study is the integration of the multi-modality approach, the quality of the quantitative data, and the creation of a tenable model for the interaction role in COPD of CD8 T cells and fibrocytes. While both have been previously implicated in COPD, this new study is more definitive by using this integrated approach.

Reviewer #2 (Public Review):

The authors use a series of elegant methods to describe the nature of the interrelationship among CD8+ T cells and fibrocytes in the airways of COPD patients. They find an increased presence of these interactions in COPD and show that CXCL8-CXCR2 interactions are crucial for this interaction, leading to increased CD8+ T cell proliferation.

Major strengths of the work include the detailed functional experiments used to describe the nature of the CD8+ T cell - fibrocyte interaction. Another key strength is the translational approach of the work, building on clinical data and connecting back to these same clinical data. The conclusions of the authors are supported by the data. The impact of the work is significant and key to our understanding of the interrelationship between inflammation and tissue remodeling in COPD. Understanding this relationship holds strong potential for the identification of new drug targets and for the identification of patients at risk.

Reviewer #3 (Public Review):

Eyraud and colleagues examine how fibrocytes and CD8 cells can interact with each other to promote COPD. The key findings include that CD8 cells and fibrocytes are found to exist in close proximity to each other in COPD lungs using histopathological analysis of patient samples. The authors leverage pre-existing transcriptomic data on CD8 cells to focus on chemokine release by CD8 cells as a potential pathogenic mechanism by which they could affect fibrocyte migration. In vitro studies using peripheral blood-derived CD8 cells and fibrocytes confirm increased fibrocyte migration in the presence of CD8 cells. as drivers of COPD progression. Conversely, in vitro studies show that fibrocytes exert a pro-proliferative effect on CD8 cells. The authors also use a computational model to assess how these interactions could promote the development of fibrocyte-CD8 clusters as COPD progresses over the course of 20 years.

The strengths of the study include:

1. The multi-faceted research approach that integrates histopathology from clinical COPD lung sections, in vitro co-culture studies, and computational modeling.

2. Applying computational modeling to determine how cell-cell interactions of migration and proliferation can result in distribution patterns within the lung that approximate what is found in actual clinical samples

3. Propose a feedback loop of CD8 cells and fibrocytes that could become a potential therapeutic target to interrupt a vicious cycle that promotes COPD

However, there are also some weaknesses:

1. Specificity of the role of CD8 cells: While much of the focus is on the proximity of and interactions between CD8 cells and fibrocytes, it is not clear whether other cells similarly interact with fibrocytes. For example, CD4 cells, dendritic cells, or interstitial macrophages may similarly interact with fibrocytes as several of these also release chemokines. In the absence of a more comprehensive assessment, it becomes difficult to parse out how specific and relevant the fibrocyte-CD8 cell interactions are for COPD progression when compared to other putative interactions.

2. The transcriptomic analysis which in many ways sets the stage for the chemokine studies uses a pre-existing dataset of COPD and non-COPD samples with only n=2. The robustness of such a sample size is limited and the narrow focus on chemokines or adhesion receptors of CD8 cells in this limited sample size does not provide a more comprehensive analysis that would require larger samples sizes, studying the transcriptomes of other cell types and a broader analysis of which pathways are the most likely to be dysregulated in the cells that surround fibrocytes.

3. Specificity of the findings for COPD: The in vitro studies use circulating cells which are different from lung cells and this is appropriately acknowledged by the authors. However, it appears from the description that the cells are all from COPD patients. It is therefore not clear whether these interactions between fibrocytes and CD8 cells are unique to COPD, whether they also occur between control CD8 and fibrocytes, or only in cells obtained from patients with inflammatory/pulmonary diseases. This limitation is appropriately acknowledged in the manuscript.

Reviewer #1 (Public Review):

The cerebral cortex, or surface of the brain, is where humans do most of their conscious thinking. In humans, the grooves (sulci) and bumps (convolutions) have a particular pattern in a region of the frontal lobe called Broca's area, which is important for language. Specialists study features imprinted on the internal surfaces of braincases in early hominins by casting their interiors, which produces so-called endocasts. A major question about hominin brain evolution concerns when, where, and in which fossils a humanlike Broca's area first emerged, the answer to which may have implications for the emergence of language. The researchers used advanced imaging technology to study the endocast of a hominin (KNM-ER 3732) that lived about 1.9 million years ago (Ma) in Kenya to test a recently published hypothesis that Broca's remained primitive (apelike) prior to around 1.5 Ma. The results are consistent with the hypothesis and raise new questions about whether endocasts can be used to identify the genus and/or species of fossils.

Reviewer #2 (Public Review):

The authors tried to support the hypothesis that early Homo still had a primitive condition of Broca's cap (the region in fossil endocasts corresponding to Broca's area in the brain), being more similar to the condition in chimpanzees than in humans. The evidence from the described individual points to this direction but there are some flaws in the argumentation.

First, only one human and one chimpanzee were used for comparison, although we know that patterns of brain convolutions (and in addition how they leave imprints in the endocranial bones) are very variable.

Second, the evidence from this fossil specimen adds to the evidence of previously describe individuals but still not yet fully prove the hypothesis.

Third, there is a vicious circle in using primitive and derived features to define a fossil species and then using (the same or different) features to argue that one feature is primitive or derived in a given species. In this case, we expect members of early Homo to be derived compared to their predecessors of the genus Australopithecus and that's why it seems intriguing and/or surprising to argue that early Homo has primitive features. However, we should expect that there is some kind of continuum or mosaic in a time in which a genus "evolves into" another genus. This discussion requires far more discussions about the concepts we use, maybe less discussion about what is different between the two groups but more discussion about the evolutionary processes behind them.

Fourth, the data of convolutional imprints presented are rather subjective when identifying which impressions represent which brain convolutions. Not seeing an impression does not necessarily mean that the corresponding brain feature did not exist. Interestingly, the manuscript does not mention and discuss at all the frontoorbital sulcus. This is a sulcus that usually runs from the orbital surface of the frontal lobe up to divide the inferior frontal gyrus in chimpanzees, a condition totally different than in humans who do not have a frontoorbital sulcus. Could such a sulcus be identified, this would provide a far more convincing argument for a primitive condition in this specimen. In Australopithecus sediba, e.g., the condition in this region seems to be a mosaic in which some aspects of the morphology seem to be more modern while one of the sulcual impressions can well be interpreted as a short frontoorbital sulcus. For this specimen, by the way, I would come back to my third point above: some experts in the field might argue that this specimen could belong to Homo rather than Australopithecus...

According to my arguments above, I think that this manuscript might revive interesting discussions about this topic but it is not likely to settle them because the data presented are not strong enough to fully support the hypothesis.

Reviewer #3 (Public Review):

The authors provide a detailed analysis of the sulcal and sutural imprints preserved on the natural endocast and associated cranial vault fragments of the KNM-ER3732 early Homo specimen. The analyses indicate a primitive ape-like organization of this specimen's frontal cortex. Given the geological age of around 1.9 million years, this is the earliest well-documented evidence of a primitive brain organization in African Homo.

In the discussion, the authors re-assess one of the central questions regarding the evolution of early Homo: was there species diversity, and if yes, how can we ascertain it? The specimen KNM-ER1470 has assumed a central role in this debate because it purportedly shows a more advanced organization of the frontal cortex compared to other largely coeval specimens (Falk, 1983). However, as outlined in Ponce de León et al. 2021 (Supplementary Materials), the imprints on the ER1470 endocranium are unlikely to represent sulcal structures and are more likely to reflect taphonomic fracturing and distortion. Dean Falk, the author of the 1983 study, basically shares this view (personal communication). Overall, I agree with the authors that the hypothesis to be tested is the following: did early Homo populations with primitive versus derived frontal lobe organizations coexist in Africa, and did they represent distinct species?

I greatly appreciate that the authors make available the 3D surface data of this interesting endocast.

Reviewer #1 (Public Review):

Recent works have documented the observation that transcription factors (TFs) and other transcriptional machinery proteins, e.g., Pol2 and mediator, can form high-concentration clusters at target genes within the nucleus and such behavior plays an important role in transcriptional activation. It is also well-established that the intrinsically disordered regions (IDRs) within many of the transcriptional regulators can undergo multivalent protein-protein interactions, which can lead to phase separation under certain conditions. It is thus thought that the IDRs are essential drivers of the clustering behaviors of transcriptional regulators. However, direct proof of this hypothesis remains missing. To fill this gap, Hannon and Eisen conducted a survey of the subnuclear localization of 75 IDRs derived from Drosophila TFs. They found that many full-length TFs but not IDRs alone form subnuclear clusters. They also did not detect a change in the clustering of TFs after deleting IDRs. Based on these data, they concluded that IDRs are unlikely to be the primary molecular drivers of the clustering phenomenon observed during transcription.

This study tackles an interesting question related to transcriptional regulation and IDR behaviors. The subnuclear distribution of many Drosophila TFs and TF IDRs measured in this work provides a valuable resource for future studies of these TFs and IDRs. The authors' finding that the distribution of an IDR alone is distinct from a full-length TF containing the IDR is new and informative though not surprising. Protein-chromatin binding is known to be stoichiometric with a clear structural basis, which is likely stronger than IDR-IDR interactions that are known to be weaker and more transient. Thus, adding a chromatin-binding capability to an IDR of interest indeed likely significantly affects the distribution of the IDR. Despite being a natural hypothesis based on existing knowledge, it was not previously verified until this current work that systematically compared TF and TF IDR distributions. However, the authors' other conclusion that deleting the IDR from a TF does not affect the TF's clustering behavior is not fully supported. This is because the change of TF's clustering behavior due to IDR deletion, if any, is likely quantitative (decreasing) instead of qualitative (completely disappearing), due to the fact that protein-chromatin binding is stronger than IDR-IDR interactions. This work lacks quantitative characterization of TF clusters before and after IDR deletion. The spinning disk confocal microscopy used here likely does not provide the necessary spatial resolution to quantitatively characterize TF clusters, which often have dimensions near or below the diffraction limit of light.

Reviewer #2 (Public Review):

This work by Hannon and Eisen focuses on the sequence and structural features of transcription factors (TFs) that dictate their sub-nuclear localization. The authors test the hypothesis that intrinsically disordered regions (IDRs) in TFs are drivers of subnuclear localization and clustering by first identifying IDRs in the drosophila proteome using a novel approach and then expressing a subset of IDRs from TFs important during the development of an early embryo. The authors then perform an extensive and high-throughput imaging screen in S2 cells and drosophila embryos and find that subnuclear clustering does not occur when IDRs are expressed alone but happens frequently in full-length TFs, even sometimes without the IDRs. A significant strength of the study is the extensive amount of imaging data that support well the conclusions in the paper. A potential weakness is that the conclusions are based on qualitative analysis only; the work would be strengthened considerably if the authors could provide quantification that allows the reader to distinguish clearly between a homogenous distribution and clustering of TFs. The work tackles an important functional question regarding IDRs in TFs and is of high relevance to the field. There is an impressive amount of data that generally support the conclusion of the paper, which is that IDRs are insufficient to drive TF clustering in the nucleus. The manuscript is very well written, pleasing to read, and easy to follow. This work advances the field considerably, providing valuable mechanistic insights into transcription.

Reviewer #1 (Public Review):

The expression and localization of Foxc2 strongly suggest that its role is mainly confined to As undifferentiated spermatogonia (uSPGs). Lineage tracing demonstrated that all germ cells were derived from the FOXC2+ uSPGs. Specific ablation of the FOXC2+ uSPGs led to the depletion of all uSPG populations. Full spermatogenesis can be achieved through the transplantation of Foxc2+ uSPGs. Male germ cell-specific ablation of Foxc2 caused Sertoli-only testes in mice. CUT&Tag sequencing revealed that FOXC2 regulates the factors that inhibit the mitotic cell cycle, consistent with its potential role in maintaining a quiescent state in As spermatogonia. These data made the authors conclude that the FOXC2+ uSPG may be the true SSCs, essential for maintaining spermatogenesis. The conclusion is supported by the data presented.

Reviewer #2 (Public Review):

The authors found FOXC2 is mainly expressed in As of mouse undifferentiated spermatogonia (uSPG). About 60% of As uSPG were FOXC2+ MKI67-, indicating that FOXC2 uSPG were quiescent. Similar spermatogonia (ZBTB16+ FOXC2+ MKI67-) were also found in human testis.

The lineage tracing experiment using Foxc2CRE/+;R26T/Gf/f mice demonstrated that all germ cells were derived from the FOXC2+ uSPG. Furthermore, specific ablation of the FOXC2+ uSPGs using Foxc2Cre/+;R26DTA/+ mice resulted in the depletion of all uSPG population. In the regenerative condition created by busulfan injection, all FOXC2+ uSPG survived and began to proliferate at around 30 days after busulfan injection. The survived FOXC2+ uSPGs generated all germ cells eventually. To examine the role of FOXC2 in the adult testis, spermatogenesis of Foxc2f/-;Ddx4-cre mice was analyzed. From a 2-month-old, the degenerative seminiferous tubules were increased and became Sertoli cell-only seminiferous tubules, indicating FOXC2 is required to maintain normal spermatogenesis in adult testes. To get insight into the role of FOXC2 in the uSPG, CUT&Tag sequencing was performed in sorted FOXC2+ uSPG from Foxc2CRE/+;R26T/Gf/f mice 3 days after TAM diet feeding. The results showed some unique biological processes, including negative regulation of the mitotic cell cycle, were enriched, suggesting the FOXC2 maintains a quiescent state in spermatogonia.

Lineage tracing experiments using transgenic mice of the TAM-inducing system was well-designed and demonstrated interesting results. Based on all data presented, the authors concluded that the FOXC2+ uSPG are primitive SSCs, an indispensable subpopulation to maintain adult spermatogenesis. The conclusion of the mouse study is supported by the data presented.

Reviewer #3 (Public Review):

By popular single-cell RNA-seq, the authors identified FOXC2 as an undifferentiated spermatogonia-specific expressed gene. The FOXC2+-SSCs can sufficiently initiate and sustain spermatogenesis, the ablation of this subgroup results in the depletion of the uSPG pool. The authors provide further evidence to show that this gene is essential for SSCs maintenance by negatively regulating the cell cycle in adult mice, thus well-established FOXC2 as a key regulator of SSCs quiescent state.

The experiments are well-designed and conducted, the overall conclusions are convincing. This work will be of interest to stem cell and reproductive biologists.

Joint Public Review:

The study has main limitations which need to be addressed and there is lack of functional explanation of carriage. These limitations are: a) the lack of inclusion of non-Black patients; and b) the lack of appropriate explanation if results are false-positive since APOL1 provides risk for chronic renal disease (CRD) and patients with CRD are predisposed to sepsis. Sepsis occurred in 565 Black subjects, of whom 105 (29% ) had APOL1 high-risk genotype and 460 had-low risk genotype. Importantly, the risk for sepsis associated with APOL1 HR variants was no longer significant after adjusting for subjects pre-existing severe renal disease or after excluding these subjects. Thus, the susceptibility pathway seems to be: APOL1 variants > CKD > sepsis diathesis.

Suggestions to the authors:<br /> • The authors need to provide analysis of patients of non-Black origin.<br /> • The Table of demographics needs to include the type of infections and the underlying pathogen.<br /> • The authors need to provide convincing analysis if results are false-positive since APOL1 provides risk for chronic renal disease (CRD) and patients with CRD are predisposed to sepsis. For this purpose, they have to provide evidence if the sepsis causes (both type of infection and implicated pathogens) in patients with CRD who are carriers of APOL1 variants are different than in patients with CRD who are not carriers of APOL1 variants.<br /> • Why concentrations of APOL1 were not measured in the plasma of patients?<br /> • Why analysis towards risk for death is not done?<br /> • The authors need to explain why functional information is not provided.<br /> • n 162-172: too many assumptions have been used for the trial; thus, progression to sepsis is difficult to define. According to Sepsis-3 sepsis is no more a continuum from infection to sepsis and septic shock. Some patients presented with sepsis (-1, 0, 1 days considered by the authors) and when electronic health records are used, we are not able to detect the exact timepoint of SOFA score turning to a 2-point increase. This is a major limitation of the methodology presented.<br /> Same applies for all comorbidities and data extracted from electronic health records.<br /> • P value significance thresholds were set at 0.05, except for the PWAS where the threshold was set at 0.05/5 (p13). It would be helpful to list at this point what the 5 outcomes were that led to this adjusted threshold.<br /> "Risk of sepsis was significantly increased among patients with high-risk genotypes (OR 1.29, 1.0 to 1.67, P1.29, CI 1.00-1.67, P<0.47)." Some would argue that a confidence interval that includes 1.0 indicates non-significance.<br /> • The Discussion is too long and should be shortened.

Reviewer #1 (Public Review):

In this manuscript Budinska and colleagues aim to align morphologically distinct areas of colorectal cancers with the gene expression profiles and published signatures. They observe that distinct morphotypes such as serrated or mucinous align with certain subtypes but that these contradict the bulk subtype assignment. Although these data are of interest they may not be as novel as suggested by the authors and lack clarity in terms of patient selection and subtype definition.

1. Patient selection and tumor area selection are crucial for this study but not very carefully defined. Why are some core and others not? Figure referral is an issue here (sup figure 6 where all core and non-core samples are supposed to be according to the legend of Fig 4 is likely sup fig 7 but this is then a complete copy paste of Figure 4). In the methods it is stated that the core samples are based on limited contamination of additional morphotypes (<20%) but Fig 4 suggests that all tumours listed have multiple morphotypes.

2. CMS subtype should be performed with single sample predictor rather than CMScaller.

3. A couple of surprising observations need specification. MUC2 is a strong CMS3 reporter gene yet Mucinous tumours appear to end up in CMS4 rather than 3. Can the authors show that indeed stroma cells are very evident in these samples?

4. The SE PP and CT are assigned to CMS2, but in Figure 4 this appears a lot more variable than the authors would make the reader believe. The full data are not completely clear (see point 1)

5. The tumor response rates are rather weird as this is likely dependent on the complete tumour and not so much the subareas. It is not very well described what we see in this analysis.

6. Serrated adenomas have previously been aligned with CMS4. Is this different from serrated areas in cancers?

7. The fact that iCMS2 and iCMS3 align rather well with the current analysis of the distinct regions suggests that the analysis that was reported last year is the proper way to view tumor intrinsic signatures. The authors now propose a rather similar outcome to this issue which does take away a lot of the novelty of the findings of this study.

Reviewer #2 (Public Review):

In this paper, Budinská et al. consider whether morphological heterogeneity in colorectal cancer (CRC) might impact gene-expression based classifiers typically applied to bulk CRC tissues. To investigate this, the authors generated and analysed whole transcriptome microarrray profiling data from macro-dissected morphotype-specific tumour regions, bulk tumor and surrounding normal and stromal tissues.

The authors make a number of claims based on their analyses. Namely that<br /> (1) morphotype-specific gene expression profiles and active molecular pathways can be identified and that (2) most gene expression-based classifiers make different predictions when applied to different morphotypes within the same tumour and when applied to morphotype-specific tumor regions versus bulk tumor tissue.

Overall, the manuscript provides an interesting histological/morphological framework through which we can consider heterogeneity in colorectal carcinoma and an approach by which we might improve the performance of gene expression-based classifiers in predicting clinical behaviour and/or responses to therapy. Exploration of CRC morphotypes and their differences was quite interesting. However, more work is needed to support the claims made by the authors. While I appreciate that the authors themselves identify limitations of their study within the manuscript, I believe awareness of these limitations is not reflected in some of the claims made in the abstract and at points in the main text when discussing the use of expression-based classifiers.

Reviewer #1 (Public Review):

This is an interesting, timely and informative article. The authors used publicly available data (made available by a funding agency) to examine some of the academic characteristics of the individuals recipients of the National Institutes of Health (NIH) k99/R00 award program during the entire history of this funding mechanism (17 years, total ~ 4 billion US dollars (annual investment of ~230 million USD)). The analysis focuses on the pedigree and the NIH funding portfolio of the institutions hosting the k99 awardees as postdoctoral researchers and the institutions hiring these individuals. The authors also analyze the data by gender, by whether the R00 portion of the awards eventually gets activated and based on whether the awardees stayed/were hired as faculty at their k99 (postdoctoral) host institution or moved elsewhere. The authors further sought to examine the rates of funding for those in systematically marginalized groups by analyzing the patterns of receiving k99 awards and hiring k99 awardees at historically black colleges and universities.

The goals and analysis are reasonable and the limitations of the data are described adequately. It is worth noting that some of the observed funding and hiring traits are in line with the Matthew effect in science (https://www.science.org/doi/10.1126/science.159.3810.56) and in science funding (https://www.pnas.org/doi/10.1073/pnas.1719557115). Overall, the article is a valuable addition to the research culture literature examining the academic funding and hiring traits in the United States. The findings can provide further insights for the leadership at funding and hiring institutions and science policy makers for individual and large-scale improvements that can benefit the scientific community.

Reviewer #2 (Public Review):

Early career funding success has an immense impact on later funding success and faculty persistence, as evidenced by well-documented "rich-get-richer" or "Matthew effect" phenomena in science (e.g., Bol et al. 2018, PNAS). Woitowich et al. examined publicly available data on the distribution of the National Institutes of Health's K99/R00 awards - an early career postdoc-to-faculty transition funding mechanism - and showed that although 85% of K99 awardees successfully transitioned into faculty, disparities in subsequent R01 grant obtainment emerged along three characteristics: researcher mobility, gender, and institution. Men who moved to a top-25 NIH funded institution in their postdoc-to-faculty transition experienced the shortest median time to receiving a R01 award, 4.6 years, in contrast to the median 7.4 years for women working at less well-funded schools who remained at their postdoc institutions. This result is consistent with prior evidence of funding disparities by gender and institution type. The finding that researcher mobility has the largest effect on subsequent funding success is key and novel, and enhances previous work showing the relationship between mobility and ones' access to resources, collaborators, or research objects (e.g., Sugimoto and Larivière, 2023, Equity for Women in Science (Harvard University Press)).

These results empirically demonstrate that even after receiving a prestigious early career grant, researchers with less mobility belonging to disadvantaged groups at less-resourced institutions continue to experience barriers that delay them from receiving their next major grant. This result has important policy implications aimed at reducing funding disparities - mainly that interventions that focus solely on early career or early stage investigator funding alone will not achieve the desired outcome of improving faculty diversity.

The authors also highlight two incredible facts: No postdoc at a historically Black college or university (HBCU) has been awarded a K99 since the program's launch. And out of all 2,847 R00 awards given thus far, only two have been made to faculty at HBCUs. Given the track record of HBCUs for improving diversity in STEM contexts, this distribution of awards is a massive oversight that demands attention.

At no fault of the authors, the analysis is limited to only examining K99 awardees and not those who applied but did not receive the award. This limitation is solely due to the lack of data made publicly available by the NIH. If this data were available, this study would have been able to compare the trajectory of winners versus losers and therefore could potentially quantify the impact of the award itself on later funding success, much like the landmark Bol et al. (2018) paper that followed the careers of winners of an early career grant scheme in the Netherlands. Such an analysis would also provide new insights that would inform policy.

Although data on applications versus awards for the K99/R00 mechanism are limited, there exists data for applicant race and ethnicity for the 2007-2017 period, which were made available by a Freedom of Information Act request through the now defunct Rescuing Biomedical Research Initiative: https://web.archive.org/web/20180723171128/http://rescuingbiomedicalresearch.org/blog/examining-distribution-k99r00-awards-race/ These results are not presently discussed in the paper, but are highly relevant given the discussion of K99 award impacts on the sociodemographic composition of U.S. biomedical faculty. From 2007 to 2017, the K99 award rate for white applicants was 31.0% compared to 26.7% for Asian applicants and 16.2% for Black applicants. In terms of award totals, these funding rates amount to 1,384 awards to white applicants, 610 to Asian applicants, and 25 to Black applicants for the entire 2007-2017 period. And in terms of R00 awards, or successful faculty transitions: whereas 77.0% of white K99 awardees received an R00 award, the conversion rate for Asian and Black K99 awardees was lower, at 76.1% and 60.0%, respectively. Regarding this K99-to-R00 transition rate, Woitowich et al. found no difference by gender (Table 2). These results are consistent with a growing body of literature that shows that while there have been improvements to equity in funding outcomes by gender, similar improvements for achieving racial equity are lagging.

The conclusions are well-supported by the data, and limitations of the data and the name-gender matching algorithm are described satisfactorily.

One aspect that the authors should expand or comment on is the change in the rate of K99 to R00 conversions. Since 2016, while the absolute number of K99 and R00 awards has been increasing, the percentage of R00 conversions appears to be decreasing, especially in 2020 and 2021. This observation is not clearly stated or shown in Figure 1 but is an important point - if the effectiveness of the K99/R00 mechanism for postdoc-to-faculty transitions has been decreasing lately, then something is undermining the purpose of this mechanism. This result bears emphasis and potentially discussion for possible reasons for why this is happening.

Reviewer #3 (Public Review):

The researchers aim add to the literature on faculty career pathways with particular attention to how gender disparities persist in the career and funding opportunities of researchers. The researchers also examine aspects of institutional prestige that can further amplify funding and career disparities. While some factors about individuals' pathways to faculty lines are known, including the prospects of certain K award recipients, the current study provides the only known examination of the K99/R00 awardees and their pathways.

Strengths:

The authors establish a clear overview of the institutional locations of K99 and R00 awardees and the pathways for K99-to-R00 researchers and the gendered and institutional patterns of such pathways. For example, there's a clear institutional hierarchy of hiring for K99/R00 researchers that echo previous research on the rigid faculty hiring networks across fields, and a pivotal difference in the time between awards that can impact faculty careers. Moreover, there's regional clusters of hiring in certain parts of the US where multiple research universities are located. Moreover, documenting the pathways of HBCU faculty is an important extension of the Wapman et al. study (among others from that research group), and provides a more nuanced look at the pathways of faculty beyond the oft-discussed high status institutions. (However, there is a need for more refinement in this segment of the analyses as discussed further below.). Also, the authors provide important caveats throughout the manuscript about the study's findings that show careful attention to the complexity of these patterns and attempting to limit misinterpretations of readers.

Weaknesses:

The authors reference institutional prestige in relation to some of the findings, but there's no specific measure of institutional prestige included in the analyses. If being identified as a top 25 NIH-funded institution is the proximate measure for prestige in the study, then more justification of how that relates to previous studies' measures of institutional prestige and status are needed to further clarify the interpretations offered in the manuscript.

The identification of institutional funding disparities impacting HBCUs is an important finding and highlights another aspect of how faculty at these institutions are under resourced and arguably undervalued in their research contributions. However, a lingering question exists: why compare HBCUs with Harvard? What are the theoretical and/or methodological justifications for such comparisons? This comparison lends itself to reifying the status hierarchy of institutions that perpetuate funding and career inequalities at the heart of the current manuscript. If aggregating all HBCU faculty together, then a comparable grouping for comparison is needed, not just one institution. Perhaps looking at the top 25 NIH funded institutions could be one way of providing a clearer comparison. Related to this point is the confusing inclusion of Gallaudet in Figure 6 as it is not an officially identified HBCU. Was this institution also included in the HBCU-related calculations?

There is a clear connection that is missed in the current iteration of the manuscript derived from the work of Robert Merton and others about cumulative advantages in science and the "Matthew effect." While aspects of this connection are noted in the manuscript such as well-resourced institutions (those with the most NIH funding in this circumstance) hire each others' K99/R00 awardees, elaborating on these connections are important for readers to understand the central processes of how a rigid hierarchy of funding and career opportunities exist around these pathways. The work the authors build on from Daniel Larremore, Aaron Clauset, and their colleagues have also incorporated these important theoretical connections from the sociology of knowledge and science, and it would provide a more interdisciplinary lens and further depth to understanding the faculty career inequalities documented in the current study.

Reviewer #1 (Public Review):

This paper proposes and evaluates a new approach for the registration of human hippocampal anatomy between individuals. Such registration is an essential step in group analysis of hippocampal structure and function, and in most studies to date, volumetric registration of MRI scans has been employed. However, it is known that volumetric deformable registration, due to its formulation as an optimization problem that minimizes the combination of an image similarity term and relatively simple geometric regularization terms, fails to preserve the topology of complex structures. In the cerebral cortex, surface-based registration of inflated cortical surfaces is broadly preferred over volumetric registration, which often causes voxels of different tissue types to be matched (e.g., voxels belonging to a sulcus in one individual mapping onto voxels belonging to a gurys in another). The authors recognize that hippocampal anatomy is similarly complex, and, with proper tools, can benefit from surface-based registration. They propose to first unfold the hippocampus to a two-dimensional rectangle domain using their prior HippUnfold technique, and then to perform deformable registration in this rectangle domain, matching geometric features (curvature, thickness, gyrification) between individuals. This registration approach is evaluated by comparing how well hippocampal subfields traced by experts using cytoarchitectural information align between individuals after registration. The authors indeed show that surface-based registration aligns subfields better than volumetric registration applied to binary segmentations of the hippocampal gray matter.

Overall, I find the methods and results in this paper to be convincing. The authors framed the comparison between surface-based and volumetric registration in a fair way, and the results convincingly show the advantage of surface-based registration. One slight limitation of the current study is that it is uncertain whether the benefits demonstrated here translate to in vivo MRI data for which the authors' HippUnfold algorithm is tailored. The current study utilized the unfolding technique used in HippUnfold on manual segmentations of high-resolution ex vivo MRI and blockface 3D volumes, which are likely closer to anatomical ground truth than automated segmentations of in vivo MRI. However, it is reasonable to assume that given that the volumetric registration to which the proposed approach was compared also used this high-detail data, the advantages of surface-based over volumetric registration would extend to in vivo MRI as well. However, I would encourage the authors to perform future evaluations on datasets with available in vivo and ex vivo MRI from the same individuals.

I would also like to point out the relevance of the 2021 paper "Unfolding the Medial Temporal Lobe Cortex to Characterize Neurodegeneration Due to Alzheimer's Disease Pathology Using Ex vivo Imaging" by Ravikumar et al. (https://link.springer.com/chapter/10.1007/978-3-030-87586-2_1) to the current work. This paper applied an earlier version of the unfolding method in HippUnfold to ex vivo extrahippocampal cortex and performed registration using curvature features in the rectangular unfolded space, also finding slight improvement with surface-based vs. volumetric registration, so its findings support the current paper.

Overall, the paper has the potential to significantly influence future research on hippocampal involvement in cognition and disease. Outside of simple volumetry studies, most hippocampal morphometry studies rely on volumetric deformable registration of some kind, typically applied to whole-brain T1-weighted MRI scans. With HippUnfold available for anyone to use and not requiring manual registration, the paper provides a strong impetus for using this approach in future studies, particularly where one is interested in localizing effects of interest to specific areas of the hippocampus. Additional evaluation of in vivo HippUnfold using in vivo / ex vivo datasets, would make the use of this approach even more appealing.

Reviewer #2 (Public Review):

DeKraker et al. propose a new method for hippocampal registration using a surface-based approach that preserves the topology of the curvature of the hippocampus and boundaries of hippocampal subfields. The surface-based registration method proved to be more precise and resulted in better alignment compared to traditional volumetric-based registration. Moreover, the authors demonstrated that this method can be performed across image modalities by testing the method with seven different histological samples. While the conclusions of this paper are mostly well supported by data, some aspects of the method need to be clarified. This work has the potential to be a powerful new registration technique that can enable precise hippocampal registration and alignment across subjects, datasets, and image modalities.

Regarding the methodological clarification of the surfaced-based registration method, the last step of the process needs further clarification. Specifically, after creating the averaged 2D template, it is unclear how each individual sample is registered to sample1's space. If I understand correctly, after creating the averaged 2D template, each individual sample is then registered to sample1's space via the transform from each sample to the averaged template and then the inverse transform from the template to sample1's space. Samples included both left and right hemispheres, so were all samples being propagated to left hemisphere sample 1 space? The authors also note that a measure of the subfield labels overlap with that sample's ground-truth subfield definitions was calculated. Is this a measure of overlap, for example, between sample 3 (registered to sample 1 space) and the ground-truth (unfolded, not registered) sample 3 labels? It would be beneficial to provide a full walkthrough of one example sample to clarify the steps. Clarification of this aspect of the method is critical for understanding the evaluation of the method.

Reviewer #3 (Public Review):

Dekraker and colleagues previously developed a new computational tool that creates a "surface representation" of the hippocampal subfields. This surface representation was previously constructed using histology from a single case. However, it was previously unclear how to best register and compare these surface-based representations to other cases with different morphology.

In the current manuscript, Dekraker and colleagues have demonstrated the ability to align hippocampal subfield parcellations across disparate 3D histology samples that differ in contrast, resolution, and processing/staining methods. In doing so, they validated the previously generated Big-Brain atlas by comparing seven different ground-truth subfield definitions. This is an impressive and valuable effort that provides important groundwork for future in vivo multi-atlas methods.

Reviewer #1 (Public Review):

Mignerot et al. performed a Herculean effort to measure and describe natural variation in C. elegans egg-laying behavior and egg retention. The paper is well written and organized, but almost seems like two papers in one. However, I understand the desire to put these stories together. The authors show wild strains vary in egg retention with some extremes that appear phenotypically similar to species with viviparity (or live birth / internal hatching of offspring). They previously published a rare variant in the gene kcnl-1 that plays a role in egg retention but identify common variants in this study. They classify wild strains based on egg-retention to separate out the extremely different isolates. Egg laying has been extensively studied in the laboratory strain N2, but rarely addressed in natural strains. The authors investigate egg-laying behaviors using standard assays and find that their classified egg-laying groups have differences in sub-behaviors suggesting diverse roles in the ultimate egg-laying output. Then, they turn to the egg-laying circuit using both exogenous serotonin (5-HT), 5-HT modulatory drugs (e.g. SSRIs), and even genome editing to test epistasis with the mod-5 5-HT reuptake. The effects of 5-HT modulation and mutants are not predictive based on the basal behaviors and egg-retention phenotypes with the most extreme egg-retention strains differing in their responses. Interestingly, strains with more egg retention have decreased fitness (in their laboratory) measures but also provide a protective environment for offspring when exposed to common "natural" stressors. Their final conclusion that egg retention could be a trade-off between antagonistic effects of maternal vs. offspring fitness is supported well and sets the stage for future mechanistic studies across Caenorhabditis.

Reviewer #2 (Public Review):

Mignerot et al. study variations in egg retention in a large set of wild C. elegans strains using detailed analysis of a subset of these strains to those that these variations in egg retention appear to arise from variations in egg-laying behavior. The authors then take advantage of the advanced genetic technology available in C. elegans, and the fact that the cellular and molecular mechanisms that drive egg-laying behavior in the N2 laboratory strain of C. elegans have been studied intensely for decades. Thus, they demonstrate that variations in multiple genetic loci appear to drive variations in egg laying across species, although they are unable to identify the specific genes that vary other than a potassium channel already identified in a previous study from some of these same authors (Vigne et al., 2021). Mignerot et al. also present evidence that variations in the response of the egg-laying system to the neuromodulator serotonin appear to underlie variations in egg-laying behavior across species. Finally, the authors present a series of studies examining how the retention of eggs in utero affects the fertility and survival of mothers versus the survival of their progeny in a variety of adverse conditions, including limiting food, and the presence of acute environmental insults such as alcohol or acid. The results suggest that variations in egg-laying behavior evolved as a response to adverse environmental conditions that impose a trade-off between survival of the mothers versus their progeny.

Strengths:

The analysis of variations in egg laying by a large set of wild species significantly extends the previous work of Vigne et al. (2021), who focused on just one wild variant strain. Mignerot finds that variations in egg laying are widespread across C. elegans strains and result from changes in multiple genetic loci.

To determine why various strains vary in their egg-laying behavior, the authors take advantage of the genetic tractability of C. elegans and the huge body of previous studies on the cellular and molecular basis of egg-laying behavior in the laboratory N2 strain. Since serotonin is one signal that induces egg laying, the authors subject various strains to serotonin and to drugs thought to alter serotonin signaling, and they also use CRISPR induced gene editing to mutate a serotonin reuptake transporter in some strains. The results are largely consistent with the idea that variations across strains alter how the egg-laying system responds to serotonin.

The final figures in the paper present a far more detailed analysis than Vigne et al. (2021) of how variations in egg retention across species can affect fitness under various environmental stresses. Thus, Mignerot et al. look at competition under conditions of limiting food, and response to acute environmental insults, and compare the ability of adults, in utero eggs, and ex vivo eggs to survive. The results lead to an interesting discussion of how variations in behavior result in a trade-off in survival of mothers versus their progeny. The authors in their Discussion do a good job describing the challenges in interpreting the relevance of these laboratory results to the poorly-understood environmental conditions that C. elegans may experience in the wild. The Discussion also had an excellent section about how the ability of a single species to strongly regulate egg-laying behavior in response to its environment, and how this ability could be adaptive. Overall, these were the strongest and most interesting aspects of Mignerot et al.

Weaknesses<br /> The specific potassium channel variation studied by Vigne et al. (2021) has by far the strongest effect on egg laying seen in the Mignerot et al. study and remains the only genetic variation that has been molecularly identified. So, Mignerot et al. were not able to identify any additional specific genes that vary across species to cause changes in egg laying, and this limited their ability to generate new insights into the specific cellular and molecular mechanisms that have changed across species to result in changes in egg laying behavior.

The authors' use of drug treatments and CRISPR to alter serotonin signaling yielded some insights into mechanistic variations in how the egg-laying system functions across strains, but these experiments only allow very indirect inferences into what is going on. The analysis in Figures 4 and 5 generates a complex set of results that are not easy to interpret. The clearest result seems to be that strains carrying the KCNL-1 point mutation lay eggs poorly and exogenous serotonin inhibits rather than stimulates egg laying in these strains. This basic result was to a large extent reported previously in Vigne et al. 2021.

The analysis of egg-laying behavior in Figure 3 is relatively weak. Whereas the state of the art in analyzing this behavior is to take videos of animals and track exactly when they lay eggs, the authors used a lower-tech method of just examining how many eggs were laid within 5 minute intervals. It is not clear that this allows adequate resolution to determine if the strains examined actually have clusters of egg-laying events (i.e. active phases) or not, so the entire analysis of active and inactive phase intervals seemed dubious. It was unclear that this analysis demonstrated differences in the patterns of egg-laying behavior between strains that could be sufficient to explain the differences in accumulation of unlaid eggs between these strains. In contrast, the variations in Fig 3G and 3H between strains were very strong. It is not clear why the authors did not focus more on these differences as being possibly largely responsible for the differences in egg retention between strains. In the discussion, the authors extensively write about the work of the Collins lab showing that retained eggs stretch the uterus to produce a signal that activates egg-laying muscles. Could it be that really this mechanism is the main one that varies between strains, leading to the observed variations in time to laying the first egg as well as variations in the number of retained eggs throughout adulthood?

Reviewer #2 (Public Review):

In this manuscript, Scheer and Bargmann investigate how behavioral arousal state affects foraging decisions in the nematode C. elegans. Previous work has shown that when placed on a lawn of bacterial food, C. elegans spontaneously switch between two behavioral states, termed roaming and dwelling, during which they exploit or explore the food environment, respectively. It has also been shown that animals spontaneously leave bacterial lawns depending on factors such as food quality or mate availability.

Here, the authors use quantitative behavioral analyses to describe in unprecedented detail the various behavioral choices animals make when encountering the lawn edge. They report that leaving the lawn is a rare outcome compared to other choices such as pausing or reversing back into the lawn. It occurs predominantly out of the roaming state and has a characteristic preceding fast crawling profile. They developed a refined analysis method, the result of which suggests that the arousal state of animals on food can be described by a 4-state behavior (as opposed to the 2-state roaming - dwelling classification); leaving the lawn occurs predominantly from "state 3", which corresponds to the highest level of arousal during roaming. They further show that various manipulations, such as optogenetic inhibition of feeding, stimulation of RIB neurons, or mutations of neuromodulator pathways, all of which have previously been reported to affect crawling speed and/or roaming/dwelling, maintain the coupling between roaming states and leaving, suggesting a dedicated mechanism for coupling leaving to the roaming state. Finally, they use genetics to implicate chemosensory neurons as neuronal circuit elements mediating this coupling.

How arousal states affect decision making is an active area of neuroscience research; therefore, the current manuscript will impact the field beyond the small community of C. elegans researchers. Also, in the past, roaming/dwelling and leaving have been treated as independent behaviors; the current manuscript is very intriguing, demonstrating both the interconnectedness of different behavioral programs and the importance of the animal's behavioral context for specific decisions.

Reviewer #3 (Public Review):

Scheer and Bargmann use a combination of computational and experimental approaches in C. elegans to investigate the neuronal mechanisms underlying the regulation of foraging decisions by the state of arousal. They showed that, in C. elegans, the decision to leave food substrates is linked to a high arousal state, roaming, and that an increase in speed at different timescale preceded the food leaving decisions. They found that mutants that exhibit increased roaming also leave food substrates more frequently and that both behaviors can be triggered if food intake is inhibited. They further identify a set of chemosensory neurons that express the transduction channel tax-4 that couple the roaming state and the food-leaving decisions. The authors postulate that these neurons integrate foraging decisions with behavioral states and internal feeding cues.

The strength of the paper relies on using quantitative and detailed behavioral analysis over multiple time scales in combination with the manipulation of genes and neurons to tackle the state-dependent control of behavioral decisions in C. elegans. The evidence is convincing, the analysis rigorous, and the writing is clear and to the point.

Reviewer #1 (Public Review):

Genetic, physiological, and environmental manipulations that increase roaming increase leaving rates. The connection between increased roaming and increased leaving is lost when tax4-expressing sensory neurons are inactivated. This study is conceptually important in its characterization of worm behaviors as time-series of discrete states, a promising framework for understanding behavioral decisions as algorithms that govern state transitions. This framework is well-established in other animals, thanks to Berman and others, but relatively new to worms.

A key discovery is that lawn leaving behavior is probabilistically favored in states of behavioral arousal. I like the use of response-triggered averages (triggered on leaving events) that illustrate a "state-dependent receptive field" of the behavioral response. Response-triggered averages are common in sensory neuroscience, used, for example, to characterize the diverse "stimulus-dependent receptive fields" of different retinal ganglion cell types. It's nice to adapt the idea to illustrate the state-dependence of behavioral state transitions.

The simplest metric of arousal state is crawling speed. When animals crawl faster, they are more likely to leave lawns. A more sophisticated metric of behavioral context is whether the animal is in a "roaming" or "dwelling" state, two-state HMM modeling from previous work (Flavell et al., 2013). Roaming animals are more likely to leave lawns than dwelling animals. Different autoregressive HMM tools can segment worm behavior into 4-states. Also with ARHMMs, the most aroused state is again the state that promotes lawn-leaving.

(With the AR-HMM, I have a small quibble in its characterization as "orthogonal" to the 2-state HMM. Orthogonal has a precise mathematical meaning, but here orthogonal is taken loosely to only mean "very different". I'd prefer the authors just call them "very different" and not use mathematical terms so loosely.)

HMM analysis seems to disentangle effects that were lumped by the simpler metric of overall speed. Crawling speed before lawn leaving events, when analyzed only within roaming periods, is only higher for ¡1 min before the event. I presume that the higher speed that is observed for several minutes before lawn leaving when all states are taken into account (e.g., Fig 1J, Fig 2A, and others) reflects the tendency to be in the faster roaming state than the slower dwelling state for several minutes before lawn leaving? If this is correct, it would be nice for the authors to be explicit about this interpretation, to help the reader understand what is going on.

My principal worry is about the possible artifact if worms are more likely to be at lawn boundaries when moving quickly or in an arousal state (roaming in the 2-state HMM or in state 3 in the AR-HMM)? Lawn-leaving events only occur when the animal is at lawn boundaries. If animals are more likely to be at lawn boundaries when aroused, this should artificially increase the likelihood that these states precede lawn-leaving behaviors for a trivial environment-dependent reason instead of their interesting internal state-dependent reason. The authors might consider trying to disentangle the state-dependent statistics of lawn edge proximity when assessing by how much arousal states precede lawn-leaving events. I realize this is could be a formidable analytical challenge.

One recourse is to align speed, HMM, and AR-HMM states to the other behavioral events that only happen at lawn boundaries. When they do this for head poke-reversals in Figure 2-supplement 3, they also observe an (albeit modest) increase in arousal states before head poke-reversals. It should be easy to also compare what happens with head poke-forward and head poke-pause to better understand potential artifacts in quantifying edge-associated events. In any case, this concern and their strategies to address it should be discussed for clarity and transparency.

The authors use diverse environmental, genetic, and optogenetic perturbations to regulate the roaming state, thereby regulating the statistics of leaving in the expected manner. One surprise is that feeding inhibition evokes roaming and lawn-leaving in both pdfr-1 and tph-1 mutants, even though the tph-1-expressing NSM neurons have been shown to sense bacterial ingestion and food availability. I'm curious, is there anything in these new results that is inconsistent with previous claims by Rhoades et al., 2019, or did Rhoades et al. simply not do these tests?

Another surprise is that evoking roaming does not evoke leaving in tax-4 mutants (which is something of an internal control that argues against the worry that roaming artificially increases the likelihood of leaving, see above). Without sensory neuron activity, worms are only more likely to roam for a minute before leaving rather than roaming for several minutes before leaving like wild-type (Figure 6C). ASJ seems to be the most important sensory neuron in this coupling between roaming and leaving (which is uncoupled when sensory neurons are inactivated).

I'm a little puzzled why the wild-type animals shown in Figure 6C show elevated roaming for several minutes before leaving events, whereas the wild-type animals shown in Figures 4I,J,K show elevated roaming for only about a minute, not much different than tax-4 mutants. Am I missing something? What is different about these different wild-type animals?

Reviewer #2 (Public Review):

The manuscript examined the behavioural and neural profile of weak and strong fear memories. The data provide strong evidence that weak but not strong fear memories are subject to extinction and reconsolidation disruption. Strong memories also show greater generalization. These differences were echoed in differential neural connectivity with weak fear memories showing greater connectivity between brains areas than strong fear memories.

Strengths:

The findings are of great importance and offer insight into why resistance to extinction and reconsolidation may underlie fear-related psychopathology.<br /> The study uses key behavioural tests to study the durability of weak vs strong memories (extinction and reconsolidation) as well as studies the generalisation of those memories. These behavioural effects nicely dovetail with the neural connectivity analyses that were performed.

The data presented in this paper will be the basis for future hypothesis driven examinations on the causal influence of specific pathways involved in contextual fear.<br /> Excellent use of the open field to control for motor effects.

Weaknesses:

One alternative account to the weak vs. strong memory distinction made in the paper is the opportunity for extinction in the 2S compared to the 10S group. In the 2S group, the last shock occurs in the 3rd minute, leaving 9 minutes of context exposure without reinforcement to follow. This is not the case for the 10S group. If context fear extinction is engaged during this time, then this would mean that two memories (acquisition and extinction) are taking place in the 2S group, weakening the fear memory in this group, setting up the ground for stronger effects of extinction, less generalization and of course potential greater connectivity required for representing and linking these memories. Indeed, the IL, a brain area linked to extinction, is more predominant in the connectivity map of the 2S compared to the 10S group. While testing this alternative is beyond the scope of this paper, it will need to be discussed.<br /> Methodological detail is lacking re the timeline of study, and connectivity analyses.

Reviewer #1 (Public Review):

The authors demonstrate that reactivation of mild vs strong aversive contextual associations produces dissociable effects on fos expression across a wide network of relevant brain regions. Mild, 2-shock memory recruits a 'small-world' network in which amygdalar regions are functionally connected to other regions that modulate their activity and behavioral output, whereas strong, 10-shock memory isolates amygdalar nuclei from the rest of the network. These different patterns of correlated neural activity correspond with functional/behavioral differences - the authors confirm that weak, 2-shock memory is more effectively extinguished and is susceptible to reconsolidation relative to strong, 10-shock memory.

One major drawback of the manuscript is the fact that the data were collected from male subjects only. One might expect similar behavioral outcomes from male and female rats receiving 2-shock and 10-shock training. However, increasing attention to sex as a biological variable has revealed an interesting truth, namely that males and females can engage distinct neural pathways to arrive at the same behavioral destination. It should not be taken for granted that retrieval of aversive contextual associations would reproduce the same networks in females, and, as such, the manuscript does not give a complete accounting of the phenomenon under study.

The aversive associative memories described by the authors are characterized as mild or strong. More analysis of the meaning of memory strength, and its relationship to conditioning parameters, is needed. In particular, the authors should discuss issues such as amount of training, US magnitude, and rate of shock delivery. If amount of training is important, would 2 vs 10 presentations of a milder shock produce the same networks at retrieval? Would a larger shock require fewer presentations to isolate amygdalar regions from the rest of the network? If the shocks were presented at the same rate during training, would you get the same result in both groups? More data examining these questions would be ideal, but, in the absence of that, a discussion of these issues is needed and missing from the manuscript in its current form.

Reviewer #3 (Public Review):

In this manuscript, Haubrich and Nader investigated the difference between mild and strong fear memory mechanisms at the circuit levels. Previous studies have shown the difference in mechanisms and functions of mild and strong fear memory. Interestingly, memory retrieval induces reconsolidation of mild fear memory, but not always strong fear memory; retrieved mild fear memory is disrupted by protein synthesis inhibition, whereas retrieved fear memory is more immune to this inhibition compared to mild memory. The authors measured c-fos expression following retrieval of mild and strong fear memories and compared functional connectivity of brain regions associated with retrieval of them using computation analyses. The authors suggested that mind and strong fear memories differ in neural networks at the circuit levels.<br /> These are interesting findings.

Major concerns:

1) Previous studies including Karim's lab have shown that protein synthesis in the hippocampus is required for the reconsolidation of contextual fear memory and that the retrieval of contextual fear memory activates gene expression such as c-fos in the hippocampus. However, the authors failed to confirm this observation. This may be due to the small number of rats or some technical problems.

2) The author's computation analyses suggested differences in neural networks activated by the retrieval of mild and strong fear memories. The results of computer analysis are interesting. However, it is not clear whether such results are actually occurring in vivo. At this moment, the author's findings are not a conclusion, but rather a suggestion or hypothesis. Therefore, it is also important to conduct interventional experiments to evaluate the validity of the authors' findings. Specifically, the authors' results could be validated by analyzing the effects of inhibition of specific brain regions on mild and strong fear memories retrieval using such as DREADD and other methods. These experiments seem hard, but would greatly improve the quality of the manuscript.

Joint Public Review:

It has been shown previously that maternal aging in mice is associated with an increase in accumulation of damaged mitochondria and activation of parkin-mediated autophagy (see DOI: 10.1080/15548627.2021.1946739). It has also been shown that C-natriuretic peptide (CNP) regulates oocyte meiotic arrest and that its use during in vitro oocyte maturation can improve parameters associated with decreased oocyte quality. Here the authors tested whether use of CNP treatment in vivo could improve oocyte quality and fertility of aged mice, for which they provided convincing evidence. They also attempted to determine how CNP improves oocyte developmental competence. They showed a correlation between CNP use in vivo and the appearance (and some functional qualities) of cytoplasmic organelles more closely approximating those of oocytes from young mice. However, this correlation could not be interpreted to imply causation. Additional experiments performed using CNP during in vitro maturation were not properly controlled and so are not possible to interpret.

A strength of the manuscript is that the authors use an in vivo treatment to improve oocyte quality rather than just using CNP during oocyte maturation in vitro as has been done previously. This strategy provides more potential for improving oocyte quality - over the course of oocyte growth and maturation - rather than just the final few hours of maturation alone. This strategy also has the potential to be translated into a more generally useful clinical therapeutic method that using CNP during in vitro maturation. However, it is difficult to glean information regarding how CNP might have its effects in vivo. A range of models are used in the manuscript with a mix of in vivo studies with in vitro experiments, which results in some disconnect between systemic CNP and its reported intrafollicular action as well as in the short-term versus longer-term actions of CNP on oocyte quality. Specifically, CNP was shown to be reduced in the plasma of aged mice, but this was not shown in the granulosa cells, which are the reported source of CNP that acts on oocytes. Whether the ovarian source of CNP is reduced in aged females was not demonstrated, and CNP is not known to act on oocytes through an endocrine effect. In vivo treatments with CNP by i.p. injection were performed, but the dose (120 ug/kg) and time (14 days) of treatment were not validated by any prior experiments to give them physiological relevance.

Weaknesses:

1. There are errors in the manuscript writing that make the Results difficult to follow. Reference to the Figures in the Results section does not match what is shown in the Figure panels. For example, the Results text reports differences in CNP levels in aged and young mice shown in Figure 1C, but the relevant panel is actually shown in Figure 1F. Other Figures have the same problem.<br /> 2. The Results section is not always clear regarding what CNP treatment was done - in vivo injections or in vitro maturation. For example, what is the difference, if any, between Figures 2C-D and Figures S2A-B?<br /> 3. Immature oocytes from aged females (~1 year) were treated with a two-step culture system with a pre-IVM step with CNP. Controls included oocytes from young (6-8 weeks) females or oocytes from aged females treated by conventional IVM. The description of these methods suggests that control oocytes did not receive an equivalent pre-IVM culture, hence the relevance of comparisons of CNP-treated versus control oocyte is questionable. It was observed that aged oocytes pre-cultured in CNP improved polar body extrusion rates and meiotic spindle morphology compared to oocytes in conventional IVM, as has been well established. The description of statistical methods does not make clear whether the PBE rate in CNP-treated old oocytes remained significantly lower than young controls.<br /> 4. The main effect of the CNP 2-week treatment appears to be increasing the number of follicles that grow into secondary and antral stages, but there is no attempt made to discover the mechanism by which this occurs and therefore to understand why there might be an increase in the number of ovulated eggs, quality of the eggs, and litter size. It is also not clear how an intraperitoneal injection can guarantee its effectiveness because the half-life of CNP is very short, only a few minutes.<br /> 5. Meiotic spindle morphology, as well as a number of putative markers of cytoplasmic maturation are also suggested to be improved after pre-culture with CNP. In each case a subjective interpretation of "normal" morphology of these markers is derived from observations of the young controls and the proportions of oocytes with normal or abnormal appearance is evaluated. However, parameters that define abnormal patterns of these markers appear to be subjective judgements, and whether these morphological patterns can be mechanistically attributed to the differences in developmental potential cannot be concluded.<br /> 6. In addition to the localization patterns of mitochondria, the mitochondrial membrane potential, oocyte ATP content and ROS levels were assessed through more objective quantitative methods. These are well known to be defective in oocytes of aged females and CNP treatment improved these measures. Mitochondrial dysfunction is the most obvious link between oocyte apoptosis, autophagy, cytoplasmic organelle miss-localization and aberrant spindle morphology. Among the most intriguing results is the finding that CNP mediated a cAMP-dependent protein kinase (PKA) dependent reduction in mitochondrial autophagy mediators PINK and Parkin and reduced the recruitment of Parkin to mitochondria in oocytes. However, it may not be possible to directly link this observation to the improvements in IVM oocyte quality, since PINK/Parkin assessments were performed in oocytes from cultured follicles treated with CNP for 6 days.<br /> 7. The gold standard assay for oocyte quality is embryo transfer and live birth. The authors assessed the impact of maturing oocytes in vitro in the presence of CNP on oocyte quality by less robust assays (e.g., preimplantation embryo development in vitro), so the impact on oocyte quality is less certain.<br /> 8. The terminology used to describe many of the Results exaggerates the findings. For example, the authors claim that many of their immunofluorescent markers of the various organelles have a pattern that is "restored" by CNP. However, in most cases the pattern is "improved" toward the control condition but is not fully restored.<br /> 9. The numbers of embryos should have been corrected for the number of eggs fertilized as a starting point so that the percentage that developed to each stage could be expressed as a percentage of successfully fertilized eggs rather than overall percentages. As currently shown in the Figures and described in the Legend, there is no information regarding what the percentage on the y-axis means. For example, does Figure 4B show the number of 2C embryos divided by the number of eggs inseminated? Or is it divided by the number of successfully fertilized eggs, and if so, how was that assessed?<br /> 10. When fewer eggs are fertilized, the numbers of embryos per group are lower and so the impact of culturing multiple embryos together is lost. As a result, it is possible that culture conditions rather than oocyte quality drove the differences in the numbers of embryos that achieved each stage of development.<br /> 11. Not all claims in the Discussion are supported by the evidence provided. For example, "In addition, the findings demonstrated that CNP improved cytoplasmic maturation events by maintaining normal CG, ER and Golgi apparatus distribution and function in aged oocytes" but it was never demonstrated that the altered distribution had any functional impact.<br /> 12. Incompleteness and errors in the Methods section reduce confidence in many of the results reported.<br /> 13. The methods used for Statistical Analysis are never explained in either the Methods or the Figure legends. It is unclear whether appropriate analyses were done, and it is frequently unclear what was the sample size and how many times a particular experiment was repeated. These weaknesses detract from confidence in the data.

Reviewer #1 (Public Review):

In this manuscript, the authors used an unbiased method to identify proteins from porcine oocyte extracts associated with permeabilised boar spermatozoa in vitro. The identification of the proteins is done by mass spectrometry. A previous publication of this lab validated the cell-free extract purification methods as recapitulating early events after sperm entry in the oocyte. This novel method with mammalian gametes has the advantage that it can be done with many spermatozoa at the time and allows the identification of proteins associated with many permeabilised boar spermatozoa at the time. This allowed the authors to establish a list of proteins either enriched or depleted after incubation with the oocytes extract or even only associated with spermatozoa after incubation for 4h or 24h. The total number of proteins identified in their test is around 200 and with very few present in the sample only when spermatozoa were incubated with the extracts.

The list of proteins identified using this approach and these criteria provide a list of proteins likely associated with spermatozoa remnants after their entry and either removed or recruited for the transformation of spermatozoa-derived structures. Using WB and histochemistry labelling of spermatozoa and early embryos using specific antibodies the authors confirmed the association/dissociation of 6 proteins suspected to be involved in autophagy.

While this unique approach provides a list of potential proteins involved in sperm mitochondria clearance it is (only) a starting point for many future studies and does not provide the demonstration that any of these proteins has indeed a role in the processes leading to sperm mitochondria clearance. The protein identified may also be involved in other processes going on in the oocyte at this time of early development.

Reviewer #2 (Public Review):

Mitochondria are essential cellular organelles that generate ATPs as the energy source for maintaining regular cellular functions. However, the degradation of sperm-borne mitochondria after fertilization is a conserved event known as mitophagy to ensure the exclusively maternal inheritance of the mitochondrial DNA genome. Defects on post-fertilization sperm mitophagy will lead to fatal consequences in patients. Therefore, understanding the cellular and molecular regulation of the post-fertilization sperm mitophagy process is critically important. In this study, Zuidema et. al applied mass spectrometry in conjunction with a porcine cell-free system to identify potential autophagic cofactors involved in post-fertilization sperm mitophagy. They identified a list of 185 proteins that might be candidates for mitophagy determinants (or their co-factors). Despite the fact that 6 (out of 185) proteins were further studied, based on their known functions, using a porcine cell-free system in conjunction with immunocytochemistry and Western blotting, to characterize the localization and modification changes these proteins, no further functional validation experiments were performed. Nevertheless, the data presented in the current study is of great interest and could be important for future studies in this field.

Reviewer #3 (Public Review):

In this manuscript, a cytosolic extract of porcine oocytes is prepared. To this end, the authors have aspirated follicles from ovaries obtained by first maturing oocytes to meiose 2 metaphase stage (one polar body) from the slaughterhouse. Cumulus cells (hyaluronidase treatment) and the zona pellucida (pronase treatment) were removed and the resulting naked mature oocytes (1000 per portion) were extracted in a buffer containing divalent cation chelator, beta-mercaptoethanol, protease inhibitors, and a creatine kinase phosphocreatine cocktail for energy regeneration which was subsequently triple frozen/thawed in liquid nitrogen and crushed by 16 kG centrifugation. The supernatant (1.5 mL) was harvested and 10 microliters of it were used for interaction with 10,000 permeabilized boar sperm per 10 microliter extract (which thus represents the cytosol fraction of 6.67 oocytes).

The sperm were in this assay treated with DTT and lysoPC to prime the sperm's mitochondrial sheath.

After incubation and washing these preps were used for Western blot for Fluorescence microscopy and for proteomic identification of proteins. I am very positive about the porcine cell-free assay approach and the results presented here.

Reviewer #1 (Public Review):

The first synapses of the pain pathway are concentrated in the superficial spinal cord dorsal horn. Here peripheral inputs are processed by local interneuron circuitry before ascending to the brain. The spinal dorsal horn is organized into lamina with the resident interneurons differentiated by their anatomy, physiological and molecular properties. Over the past decade, the restricted expression of select genes has been used to assign potential function to dorsal horn neuron "cell types". This type of work has relied on the genesis of Cre-reporter mouse strains and intersectional tools to generate mice where select sets of neurons can be activated, inhibited, or ablated. The picture that has emerged from these types of experiments is murky but favors the model where there exist genetically defined cell-types play distinct roles in the detection of painful, itchy, thermal, and mechanical stimuli under normal and pathological situations. The current work by Boyle and colleagues concerns itself with the dorsal horn neurons expressing the neuropeptide NPY. This study is directly related to previously published work that demonstrated that ablating spinal cord neurons that express Npy, including those who express this gene transiently during development, resulted in mice that had heightened touch-evoked itch that seemed different from the canonical chemical itch pathways previously identified. A major conclusion from this previous work was that other modalities were unaffected. Subsequent work built on these findings to identify the potential touch inputs and spinal neuron expressing the Npy receptor as part of a mechanical itch circuit.

This current work by Boyle and colleagues challenge challenges this view by providing evidence that in adult mice, the dorsal horn neurons expressing Npy function to broadly inhibit pain and itch. The authors use direct injection of viral vectors, chemogenetics and synaptic silencing to probe the behavioral effects of stimulating or silencing Npy-expressing dorsal horn neurons in a variety of assays under normal and pathological conditions known to produce allodynia and hyperalgesia. Overall, this is a rather carefully conducted study with the appropriate controls. The data are clear, the effect sizes robust and the presentation easy to follow. These findings challenge the conclusion that these neurons are involved selectively in mechanical itch and instead reveal a potentially clinically important group of neurons for pain.

Reviewer #2 (Public Review):

Whether and how molecularly defined neuronal groups in the spinal cord process distinct modalities are of great interest. In this study, Boyle et al. characterized roles of inhibitory neurons expressing NPY in adult mice. By using chemogenetic, electrophysiological tools and behavioral measurements, the authors discovered that activating NPY+ interneurons strongly reduced pruritogen-evoked itch and reflexive behaviors (acute nociception or under inflammation / neuropathic pain states). Silencing NPY+ spinal interneurons enhanced spontaneous and chemical itch in a GRPR+ neurons dependent manner. The authors concluded that, unlike previous findings suggesting that these neurons are selective for mechanical itch, adult NPY+ interneurons play dual roles in gating various types of itch and pain.

The authors performed careful characterization and comparisons between development lineage and adult spinal neurons expressing NPY. This lays the foundation of the current study. The behavioral measurements were also well designed with proper controls.

Reviewer #3 (Public Review):

In the present study by Boyle et al., the function of NPY expressing spinal neurons in pain and itch perception is studied. While the function of these neurons has been addressed previously, the difference to previous studies is the combinatorial use of AAV encoded effectors and cre transgenic mice whereas previous studies relied on cre transgenic mice and reporter mice encoding the effector or only viruses. Boyle at al. demonstrate that their strategy enabled them to restrict the analysis to only those neurons expressing NPY in the adult mouse compared to a more heterogenous population that had been studied before. By using a combination of morphology, electrophysiology and behavioral paradigms they convincingly show that NPY neurons impact pruritoception via inhibiting GRPR neurons. Furthermore, they indicate a role of NPY neurons also in nociception as activation attenuates not only responses to acute nociceptive stimuli but also blocks inflammation or nerve injury induced mechanical and heat hypersensitivity. Selectively activating NPY neurons in vivo may therefore be a promising strategy to treat neuropathic pain.

The result of this study extends and partially contrast previous studies. The authors argue that contrasting results may be due to the different experimental strategies (e.g. only neurons expressing NPY adult in the present study versus a more heterogeneous population before).

Overall, the experiments are convincing, and the quality of the data/figures is exceptionally high.

Reviewer #1 (Public Review):

The study utilizes a variety of methods, chemical and expressed probes, caged release of IP3, as well as oocytes with mutations that alter zinc availability, that provide an elegant examination of how zinc deficiency and zinc excess modulate the transient and cyclic release of calcium during egg activation. In this manuscript, the authors sought to determine if there is any interplay between zinc and calcium, two divalent cations that have been demonstrated to have important roles during fertilization. They employ agents that disrupt normal zinc homeostasis and then monitor the resulting calcium oscillations during egg activation. If zinc was made unavailable via chelation with TPEN, then the calcium oscillations halted. This occurred regardless of the activation method, which included ICSI, PLC𝛇, Acetylcholine, strontium chloride, and thimerosal. This phenotype could be rescued by introducing zinc back into the egg via an ionophore, such as zinc pyrithione; however, too much zinc pyrithione also halted calcium oscillations. Taken together, these two results demonstrate that there is a threshold level of zinc that is required for proper calcium oscillations to occur.

Furthermore, the authors sought to understand how zinc affects the IP3 receptor, IP3R1. IP3R1 is the receptor that modulates the release of calcium from the endoplasmic reticulum. The authors cited a previous study that identified zinc binding sites on IP3R1. The authors highlight that there exist no studies regarding the regulation of IP3R1 by zinc; however, such studies were cited for a similar calcium channel, the RyRs. The authors use thapsigargin to inhibit the SERCA pump, leading to calcium leak from the IP3R1. TPEN blunted the amount of calcium leaked from the ER following treatment, suggesting that zinc occupancy is necessary for IP3R1 function.

The results of these experiments support the authors conclusions that zinc is essential for the IP3R1-mediated release of calcium in an oscillatory manner during egg activation. These results provide further insight into signals necessary for proper egg activation and the ultimate success of the resulting embryo.

Reviewer #2 (Public Review):

The manuscript describes more fully the relationship between zinc fluxes and calcium oscillations during egg activation by directly manipulating the level of zinc ions inside and outside the cell with chelators and ionophores and then measuring resulting changes in Ca++ oscillations. The authors have provided solid evidence consistent with their hypothesis that zinc ions regulate Ca++ oscillations by directly modulating the gating of the IP3-R which is the main calcium channel responsible for calcium release into the cytoplasm. The authors employ well established methods of calcium measurement along with various chelators, ionophores and a wide variety of methods that cause egg activation to demonstrate that an optimal level of zinc ions are required for Ca++ oscillations to occur.

Helpfully, the authors provide a model to explain their observations in Figure 7. In the model, the increase in zinc during maturation is permissive for later IP3-R gating in response to IP3 generated at fertilization. The experiments with TPEN solidly demonstrate that Zn is required because lowering free zinc, as indicated by Fluozin staining), abrogates Ca++ oscillations. This is true regardless of the method of activation. What is not clearly described in the model or in the manuscript is whether the levels of zinc at MII are simply permissive for IP3-R gating or whether there is a more acute relationship between zinc fluxes and Ca++ oscillations. In the original paper describing the zinc spark (Kim et al., ACS Chem Biol 6:716-723), the authors show that zinc efflux very closely mirrors Ca++ oscillations suggesting a more active relationship such that zinc efflux associate with each calcium spike could be necessary for terminating the Ca spike by depleting cytoplasmic Zn. There is some evidence in the present manuscript to support this. For example, in figure 3B, TPEN appears to acutely terminate a Ca spike. Whether this is repeatable is not known. Conversely, in Figure 5C and 5E, PyT leads to a rapid restoration of Ca oscillations within minutes demonstrating that changes in free Zn can cause rapid changes in Ca++ oscillations. Perhaps, rather than simply a permissive role, the normal Zn fluxes during activation may be acutely changing IP3-R gating sensitivity.

The role of TRPv3 and Trpm7 in Zn homeostasis during egg activation seems to be minor and the results in the dKO oocytes compared to TPEN are a bit confusing. In the dKO oocytes, zinc acquisition was sufficient to make it to MII suggesting Zn transport through these channels is dispensable for maturation. During activation, however, the response to Tg in dKO eggs was opposite that of TPEN, higher cytosolic Ca and increase amplitude (Figure 4G) vs lower cytoplasmic Ca and frequency for TPEN (Figure 4A). Perhaps loss of these two channels changes Ca gating independent of Zinc.

The effect of PyT on the apparent rise in cytoplasmic Ca++ in figure 6 is interpreted as caused by an artifact of high Zn concentrations. However, it is not clear that 0.05 uM PyT would necessarily increase cytoplasmic Zn to the point where FURA-2 fluorescence would increase. A simpler interpretation is that PyT allows sufficient Zn to enter the cell and keeps the IP3-R channels open causing a sustained rise in cytoplasmic Ca and preventing oscillations in Ca++. This interpretation would also preclude inhibitory effects of high Zn concentrations as shown in figure 7 which may or may not be present but are simply speculation.

Overall, this study significantly advances our understanding of egg activation and could lead to better ways of in vitro egg activation in women undergoing assisted reproduction.

Reviewer #3 (Public Review):

This study investigated the role of Zn2+ on the maintenance of Ca2+ oscillation upon fertilization. TPEN was used to reduce the level of available Zn2+ in fertilized oocytes and different inhibitors were used to pinpoint the mechanistic involvement of intracellular Zn2+ on the maintenance of Ca2+ oscillation. As also stated in the manuscript, previous studies have demonstrated the role of Zn2+ for the successful completion of meiosis/fertilization. However, the mechanistic actions of Zn2+ on the hallmark of fertilization processes such as Ca2+ oscillation has not been elucidated. A previous publication used TPEN to cease Ca2+ oscillation, but the study was not focused on the involvement of Zn2+ signal. The manuscript expands our understanding of fertilization process by describing how the level of Zn2+ regulates Ca2+ channels and stores. The manuscript is well-organized and the topic is important in early embryo development fields.

Reviewer #1 (Public Review):

This paper introduces a new transgenic mouse line that allows the labelling of the AIS and nodes of Ranvier (noR) by tagging Ank-G with GFP in a Cre-dependent manner. The authors characterise the properties of the AIS and noR when labelled with GFP to show that it has no adverse effects on the properties of the AIS and noR, as well as the intrinsic excitability of neurons. They also show that this mouse line can be used to follow AIS plasticity in vitro and visualise the AIS of neurons in vivo. This is a very useful and timely tool that will make an important impact in the field.

In general, it is clear that this mouse line can label the AIS and noR and will certainly be a useful tool for the community. Although the authors provide a thorough description of the intrinsic properties of neurons and some of the structural properties of the AIS and noR, there are some aspects of these experiments that could be refined to help show that tagging Ank-G with GFP is mostly inert. In particular, some of the basal properties of the AIS (length, position, molecular distribution) following tagging with GFP are not fully explored.

An important advantage of this mouse line is the ability to follow the AIS in live neurons. This is particularly important for imaging the dynamics and plasticity of the AIS, which the authors show is possible both in vitro and ex vivo. Finally, they also show that it is possible to image the AIS in vivo, a finding that opens many experimental doors for the future.

Reviewer #2 (Public Review):

The axon initial segment (AIS) is the axonal domain where most neurons integrate inputs and generate action potentials. Though structural and electrophysiological studies have allowed to better understand the mechanisms of assembly and maintenance of this domain, as well as its functions, there is still a need for efficient tools to study its structural organization and plasticity in vivo.

In this article, the authors describe the generation of a knock-in mouse reporter line allowing the conditional expression of a GFP-tagged version of AnkyrinG (Ank-G), which is a major protein of the axon initial segment and the nodes of Ranvier in neurons. This reporter line can in particular be used to study axon initial segment assembly and plasticity, by combining it with mouse lines or viruses expressing the Cre recombinase under the control of a neuronal promoter. Furthermore, the design of the line should allow to preserve the expression of the main Ank-G isoforms observed in neurons and could thus allow to study Ank-G related mechanisms in various neuronal subcompartments.

Some mouse lines allowing the neuronal expression of AIS/node of Ranvier markers coupled to a fluorescent protein exist, however they correspond to transgenic lines leading to potential overexpression of the tagged protein. Depending on the promoter used, their expression can vary and be absent in some neuronal populations (in particular, the Thy-1 promoter can lead to variable expression depending on the transgene insertion locus). Furthermore, these lines do not allow conditional expression of the protein regarding neuronal subtypes nor controlled temporal expression. Finally, a thorough description of the in vivo expression of the tagged protein at the AIS, and its impact on the structural and electrophysiological properties of the AIS are missing for these lines.

The present reporter line is thus definitely of interest, as the authors convincingly show that it can be used to visualize AIS ans Nodes of Ranvier in various contexts (from in vitro to in vivo). It could in particular be useful to study the assembly and plasticity of the domains where Ank-G is expressed. In this work, the authors thoroughly characterize the Ank-G-GFP reporter line generated and show that the structural and electrophysiological properties of the labeled neurons are not altered by the expression of the tagged Ank-G.

Reviewer #1 (Public Review):

The present study provides a phylogenetic analysis of the size prefrontal areas in primates, aiming to investigate whether relative size of the rostral prefrontal cortex (frontal pole) and dorsolateral prefrontal cortex volume vary according to known ecological or social variables.

I am very much in favor of the general approach taken in this study. Neuroimaging now allows us to obtain more detailed anatomical data in a much larger range of species than ever before and this study shows the questions that can be asked using these types of data. In general, the study is conducted with care, focusing on anatomical precision in definition of the cortical areas and using appropriate statistical techniques, such as PGLS. That said, there are some points where I feel the authors could have taken their care a bit further and, as a result, inform the community even more about what is in their data.

The introduction sets up the contrast of 'ecological' (mostly foraging) and social variables of a primate's life that can be reflected in the relative size of brain regions. This debate is for a large part a relic of the literature and the authors themselves state in a number of places that perhaps the contrast is a bit artificial. I feel that they could go further in this. Social behavior could easily be a solution to foraging problems, making them variables that are not in competition, but simply different levels of explanation. This point has been made in some of the recent work by Robin Dunbar and Susanne Shultz.

In a similar vein, the hypotheses of relating frontal pole to 'meta-cognition' and dorsolateral PFC to 'working memory' is a dramatic oversimplification of the complexity of cognitive function and does a disservice to the careful approach of the rest of the manuscript. One can also question the predicted relationship between frontal pole meta-cognition and social abilities versus foraging, as Passingham and Wise show in their 2012 book that it is frontal pole size that correlates with learning ability-an argument that they used to relate this part of the brain to foraging abilities. I would strongly suggest the authors refrain from using such descriptive terms. Why not simply use the names of the variables actually showing significant correlations with relative size of the areas?

The major methodological judgements in this paper are of course in the delineation of the frontal pole and dorsolateral prefrontal cortex. As I said above, I appreciate how carefully the authors describe their anatomical procedure, allowing researchers to replicate and extend their work. They are also careful not to relate their regions of interest to precise cytoarchitectonic areas, as such a claim would be impossible to make without more evidence. That said, there is a judgement call made in using the principal sulcus as a boundary defining landmark for FP in monkeys and the superior frontal sulcus in apes. I do not believe that these sulci are homologous. Indeed, the authors themselves go on to argue that dorsolateral prefrontal cortex, where studied using cytoarchitecture, stretches to the fundus of principal sulcus in monkeys, but all the way to the inferior frontal sulcus in apes. That means that using the fundus of PS is not a good landmark. Of course, any definition will attract criticism, so the best solution might be to run the analysis multiple times, using different definitions for the areas, and see how this affects results.

If I understand correctly, the PGLS was run separately for the three brain measure (whole brain, FP, DLPFC). However, given that the measures are so highly correlated, is there an argument for an analysis that allows testing on residuals. In other words, to test effects of relative size of FP and DLPFC over and above brain size?

In the discussion and introduction, the authors discuss how size of the area is a proxy for number of neurons. However, as shown by Herculano-Houzel, this assumption does not hold across species. Across monkeys and apes, for instance, there is a different in how many neurons can be packed per volume of brain. There is even earlier work from Semendeferi showing how frontal pole especially shows distinct neuron-to-volume ratios.

Overall, I think this is a very valuable approach and the study demonstrates what can now be achieved in evolutionary neuroscience. I do believe that they authors can be even more thorough and precise in their measurements and claims.

Reviewer #2 (Public Review):

In the manuscript entitled "Linking the evolution of two prefrontal brain regions to social and foraging challenges in primates" the authors measure the volume of the frontal pole (FP, related to metacognition) and the dorsolateral prefrontal cortex (DLPFC, related to working memory) in 16 primate species to evaluate the influence of socio-ecological factors on the size of these cortical regions. The authors select 11 socio-ecological variables and use a phylogenetic generalized least squares (PGLS) approach to evaluate the joint influence of these socio-ecological variables on the neuro-anatomical variability of FP and DLPFC across the 16 selected primate species; in this way, the authors take into account the phylogenetic relations across primate species in their attempt to discover the influence of socio-ecological variables on FP and DLPF evolution.

The authors run their studies on brains collected from 1920 to 1970 and preserved in formalin solution. Also, they obtained data from the Mussée National d´Histoire Naturelle in Paris and from the Allen Brain Institute in California. The main findings consist in showing that the volume of the FP, the DLPFC, and the Rest of the Brain (ROB) across the 16 selected primate species is related to three socio-ecological variables: body mass, daily traveled distance, and population density. The authors conclude that metacognition and working memory are critical for foraging in primates and that FP volume is more sensitive to social constraints than DLPFC volume.

The topic addressed in the present manuscript is relevant for understanding human brain evolution from the point of view of primate research, which, unfortunately, is a shrinking field in neuroscience. But the experimental design has two major weak points: the absence of lissencephalic primates among the selected species and the delimitation of FP and DLPFC. Also, a general theoretical and experimental frame linking evolution (phylogeny) and development (ontogeny) is lacking.

Major comments.<br /> 1.- Is the brain modular? Is there modularity in brain evolution?: The entire manuscript is organized around the idea that the brain is a mosaic of units that have separate evolutionary trajectories:

"In terms of evolution, the functional heterogeneity of distinct brain regions is captured by the notion of 'mosaic brain', where distinct brain regions could show a specific relation with various socio-ecological challenges, and therefore have relatively separate evolutionary trajectories".

This hypothesis is problematic for several reasons. One of them is that each evolutionary module of the brain mosaic should originate in embryological development from a defined progenitor (or progenitors) domain [see García-Calero and Puelles (2020)]. Also, each evolutionary module should comprise connections with other modules; in the present case, FP and DLPFC have not evolved alone but in concert with, at least, their corresponding thalamic nuclei and striatal sector. Did those nuclei and sectors also expand across the selected primate species? Can the authors relate FP and DLPFC expansion to a shared progenitor domain across the analyzed species? This would be key to proposing homology hypotheses for FP and DLPFC across the selected species. The authors use all the time the comparative approach but never explicitly their criteria for defining homology of the cerebral cortex sectors analyzed.

Contemporary developmental biology has showed that the selection of morphological brain features happens within severe developmental constrains. Thus, the authors need a hypothesis linking the evolutionary expansion of FP and DLPFC during development. Otherwise, the claims form the mosaic brain and modularity lack fundamental support.

Also, the authors refer most of the time to brain regions, which is confusing because they are analyzing cerebral cortex regions.

2.- Definition and delimitation of FP and DLPFC: The precedent questions are also related to the definition and parcellation of FP and DLPFC. How homologous cortical sectors are defined across primate species? And then, how are those sectors parcellated?

The authors delimited the FP:

"...according to different criteria: it should match the functional anatomy for known species (macaques and humans, essentially) and be reliable enough to be applied to other species using macroscopic neuroanatomical landmarks".

There is an implicit homology criterion here: two cortical regions in two primate species are homologs if these regions have similar functional anatomy based on cortico-cortical connections. Also, macroscopic neuroanatomical landmarks serve to limit the homologs across species.

This is highly problematic. First, because similar function means analogy and not necessarily homology [for further explanation see Puelles et al. (2019); García-Cabezas et al. (2022)]. Second, because there are several lissencephalic primate species; in these primates, like marmosets and squirrel monkeys, the whole approach of the authors could not have been implemented. Should we suppose that lissencephalic primates lack FP or DLPFC? Do these primates have significantly more simplistic ways of life than gyrencephalic primates? Marmosets and squirrel monkeys have quite small brains; does it imply that they have not experience the influence of socio-ecological factors on the size of FP, DLPFC, and the rest of the brain?

The authors state that:

"the strong development of executive functions in species with larger prefrontal cortices is related to an absolute increase in number of neurons, rather than in an increase in the ration between the number of neurons in the PFC vs the rest of the brain".

How does it apply to marmosets and squirrel monkeys?

References:<br /> García-Cabezas MA, Hacker JL, Zikopoulos B (2022) Homology of neocortical areas in rats and primates based on cortical type analysis: an update of the Hypothesis on the Dual Origin of the Neocortex. Brain structure & function Online ahead of print. doi:doi.org/10.1007/s00429-022-02548-0

García-Calero E, Puelles L (2020) Histogenetic radial models as aids to understanding complex brain structures: The amygdalar radial model as a recent example. Front Neuroanat 14:590011. doi:10.3389/fnana.2020.590011

Nieuwenhuys R, Puelles L (2016) Towards a New Neuromorphology. doi:10.1007/978-3-319-25693-1

Puelles L, Alonso A, Garcia-Calero E, Martinez-de-la-Torre M (2019) Concentric ring topology of mammalian cortical sectors and relevance for patterning studies. J Comp Neurol 527 (10):1731-1752. doi:10.1002/cne.24650

Reviewer #3 (Public Review):

This is an interesting manuscript that addresses a longstanding debate in evolutionary biology - whether social or ecological factors are primarily responsible for the evolution of the large human brain. To address this, the authors examine the relationship between the size of two prefrontal regions involved in metacognition and working memory (DLPFC and FP) and socioecological variables across 16 primate species. I recommend major revisions to this manuscript due to: 1) a lack of clarity surrounding model construction; and 2) an inappropriate treatment of the relative importance of different predictors (due to a lack of scaling/normalization of predictor variables prior to analysis). My comments are organized by section below:

Introduction:<br /> • Well written and thorough, but the questions presented could use restructuring.

Methods:<br /> • It is unclear which combinations of models were compared or why only population density and distance travelled tested appear to have been included.<br /> • Brain size (vs. body size) should be used as a predictor in the models.<br /> • It is not appropriate to compare the impact of different predictors using their coefficients if the variables were not scaled prior to analysis.

Reviewer #1 (Public Review):

In this study, the authors have compared object recognition in humans and rats. To this end, they trained rats to touch a target object shown along with a distractor object. The rats were initially trained on a base pair, and then tested on sets of variant pairs where the target or distractor could be transformed through size, position, 3d rotation or lighting variations. In addition, the authors then used a cDNN to find image pairs that would elicit different performance from early vs late layers, and tested rats and humans on these pairs (zero vs high and high vs zero protocols). A similar protocol was used for humans as well to get their performance on the base pair and test pairs. Finally the authors find the correlation between cDNN performance on each layer and rat or human performance across all test protocols. The main finding is that rats show the best match to earlier cDNN layers compared to humans. Based on this the authors conclude that humans and rats show contrasting performance on object recognition.

General comments<br /> Whether rats and humans have similar object representations is an interesting and fundamental question, and I commend the authors for their extensive matched experiments on rats and humans. However, the conclusions must be tempered by the fact that the authors are testing a limited set of object variations derived from just two objects. There are also potentially substantial differences in the tasks given to rats and humans, if I understand the methods and procedures correctly. My concerns are detailed below.

My main concern is that the authors find very low agreement between rats and humans on comparable tasks, but it would be important if they can identify qualitative differences in the performance. For instance, can they say that rats are using low-level visual cues compared to humans. They could compare several low-level visual models (see below) and report how human and rat accuracy compares to each of these models. Since the visual representations of cDNNs are unknown, such a comparison would be useful.

The authors should also discuss the potential reason for the human-rat differences too, and importantly discuss whether these differences are coming from the rather unusual approach of training used in rats (i.e. to identify one item among a single pair of images), or perhaps due to the visual differences in the stimuli used (what were the image sizes used in rats and humans?). Can they address whether rats trained on more generic visual tasks (e.g. same-different, or category matching tasks) would show similar performance as humans?

I also found that a lot of essential information is not conveyed clearly in the manuscript. Perhaps it is there in earlier studies but it is very tedious for a reader to go back to some other studies to understand this one. For instance, the exact number of image pairs used for training and testing for rats and humans was either missing or hard to find out. The task used on rats was also extremely difficult to understand. An image of the experimental setup or a timeline graphic showing the entire trial with screenshots would have helped greatly.

The authors state that the rats received random reward on 80% of the trials, but is that on 80% of the correctly responded trials or on 80% of trials regardless of the correctness of the response? If these are free choice experiments, then the task demands are quite different. This needs to be clarified. Similarly, the authors mention that 1/3 of the trials in a given test block contained the old base pair - are these included in the accuracy calculations?

It would be good for the authors to articulate more clearly the nature of the differences between humans and rats. For instance, rat behaviour was found to be correlated with low-level image properties like brightness, whereas presumably, human behaviour is not. It would be useful if the authors can compare rat behaviour against several possible alternative models, including the dCNN layers in Figure 4. These models could include other rats (giving a reliability estimate), luminance based models, contrast based models, models based on V1 simple cells, etc - these models would elucidate further the nature of the rat performance. A similar analysis could be done for human performance.

The authors were injecting noise with stimuli to cDNN to match its accuracy to rat. However, that noise potentially can interacted with the signal in cDNN and further influence the results. That could generate hidden confound in the results. Can they acknowledge/discuss this possibility?

The authors claimed that discrimination task in rats was more dependent on concavity than component arrangement (figure 1 left panel). But that could be just an artifact due to sampling more values of concavity than component arrangement. In that case these two attributes are not comparable at all. Could the authors address this issue in some way.

Reviewer #2 (Public Review):

Schnell et al. performed two extensive behavioral experiments concerning the processing of objects in rats and humans. To this aim, they designed a set of objects parametrically varying along alignment and concavity and then they used activations from a pretrained deep convolutional neural network to select stimuli that would require one of two different discrimination strategies, i.e. relying on either low- or high-level processing exclusively. The results show that rodents rely more on low-level processing than humans.

Strengths:

1. The results are challenging and call for a different interpretation of previous evidence. Indeed, this work shows that common assumptions about task complexity and visual processing are probably biased by our personal intuitions and are not equivalent in rodents, which instead tend to rely more on low-level properties.<br /> 2. This is an innovative (and assumption-free) approach that will prove useful to many visual neuroscientists. Personally, I second the authors' excitement about the proposed approach, and its potential to overcome the limits of experimenters' creativity and intuitions. In general, the claims seem well supported and the effects sufficiently clear.<br /> 3. This work provides an insightful link between rodent and human literature on object processing. Given the increasing number of studies on visual perception involving rodents, these kinds of comparisons are becoming crucial.<br /> 4. The paper raises several novel questions that will prompt more research in this direction.

Weaknesses:

1. There are a few inconsistencies in the number of subjects reported. Sometimes 45 humans are mentioned and sometimes 50. Probably they are just typos, but it's unclear.<br /> 2. A few aspects mentioned in the introduction and results are only defined in the Methods thus making the manuscript a bit hard to follow (e.g. the alignment dimension), htus I had to jump often from the main text to the methods to get a sense of their meaning.<br /> 3. The choices related to the stimulus design and the network used to categorize them are not fully described and would benefit from some further clarification/justification. The choice of alignment and concavity as baseline properties of the stimuli is not properly discussed. Also, from the low-correlations I got the feeling that AlexNet is just not a good model of rat visual processing. Which indeed can be interpreted as further evidence of what the authors are trying to demonstrate, but it might also be an isolated case.<br /> 4. Many important aspects of the task are not fully described in the Methods (e.g. size of the stimuli, reaction times and basic statistics on the responses).

Reviewer #3 (Public Review):

Schnell and colleagues trained rats on a visual categorization task. They found that rats could discriminate objects across various image transformations. Rat performance correlated best with late convolutional layers of an artificial neural network. In contrast, human performance showed the strongest correlation with higher, fully connected layers, indicating that rats employed simpler strategies to accomplish this task as compared to humans. This is a methodologically rigorous study. The authors tested a substantial number of rats across a large variety of stimuli. One notable strength is the use of neural networks to generate stimuli with varying levels of complexity. This approach shows significant potential as a principled model for conducting studies on object recognition and other related visual behavioral phenomena. The data strongly support the conclusion that rats and humans rely on different visual features for discrimination tasks. Overall, this is a valuable study that provides novel, important insights into the visual capabilities of rats. However, some aspects of the study need further clarification. The study does not provide clear insights into the visual features that enable rats to perform these discriminations. The relationship between neural network layers and specific aspects of visual behavior is not well-defined, representing a key limitation of the current work. Further, the current analyses do not adequately address the consistency of visual behaviors across different rats or whether different rats rely on the same visual features to accomplish the task. Lastly, rodent performance was substantially lower compared to humans and generally worse than neural network classification. The factors contributing to this disparity are unclear.

Reviewer #1 (Public Review):

The authors were trying to investigate whether viral IBs are involved in antagonizing IFN-I production during EBOV trVLPs infection. They found that IRF3 is hijacked and sequestered into EBOV IBs after viral infection, thereby leading to the spatial isolation of IRF3 with TBK1 and IKKε. In such a progress, the activity of IRF3 is suppressed and downstream IFN-I induction is inhibited. The authors designed many experiments, such as the PLA that examined the colocalization, to support their conclusions. However, necessary negative controls were missed in several assays. More key index is needed to be examined in several assays.

The paper is well organized and most data in this paper could support the conclusions, while there are several issues that need to be further solved.

1) In Figure 2-4, authors should examine the expression of downstream IFNs as well as the phosphorylation and nuclear localization of IRF3 to further prove the suppression of IRF3 activity by infecting with trVLPs.

2) In Figure 5, to better prove the conclusion that EBOV NP and VP35 play an important role in sequestering IRF3 in IBS, authors should add the "NP+VP35+VP30" and "NP+VP35+VP24" groups to reperform the assay.

3) In Figure 6f, the expression of STING should be examined by immunostaining to show the knockdown efficiency in trVLPs-infected cells.

Reviewer #2 (Public Review):

The manuscript by Zhu et al explored molecular mechanisms by which Ebola virus (EBOV) evades host innate immune response. EBOV has a number of means to shut down the type I interferon induction (by viral VP35 protein) and block type I interferon action (by viral VP24 protein). This study reported a new mechanism that inclusion body (IB) used for viral replication sequesters IRF3, a key transcription factor involved in the interferon signaling, resulting in blockade of downstream type I interferon gene transcription. This finding is potentially interesting and may provide a new insight into EBOV's evasion of innate immunity. However, there are some flaws in the experimentations and analyses that need to be addressed.

1) Most of experiments were performed by transfection of trVLP plasmids, which is very different from virus infection. The conclusions should be examined and verified in the context of virus infection.

2) Fig 1 - VP35 displayed a classical IB staining only in Panel A, while much less so in Panel C and not in panel B. It seemed that the VP35 staining images were chosen in a way towards the authors' favor. The statistical analysis of co-localization of VP35 and IRF3, TBK1 or IKKe should be performed to draw the conclusion. Another concern is that IKKe is normally lowly expressed under a rest condition and becomes induced only when the interferon signaling is activated. It seemed to be expressed at a high level even when the interferon signaling is blocked in Panel C. The authors should comment on this discrepancy.

3) Fig 2 - Was this experiment done by transfection or infection? The description of result is not consistent with the figure legend. The labeling was also not consistent between panel A and B. I would suggest performing Western blot to analyze the expression level of IRF3.

4) Fig 3 and 4 - As VP35 is well known for its highly efficient blockade of type I interferon activation, how would the authors differentiate the effect of VP35 alone from the sequestration of IRF3 in IBs in these experiments?

5) Fig 3 - PolyIC can activate both RLR and TLR signaling pathways. Can the author comment on which pathway it activates in this experiment?

6) The authors demonstrated that VP35 interacts with STING and recruit the latter to IBs. How would this affect the function of STING given that STING plays essential roles in cGAS/cGAMP pathway?

7) It is difficult to follow the logics of Fig 7. The expression level of each viral protein should be determined. Ideally, a mutation in VP35 that disrupts its ability to antagonize the interferon signaling but still allows for the IB formation can be used to assess the relative contribution of IB sequestering IRF3.

Reviewer #1 (Public Review):

The enteroviruses comprise a medically important genus in the large and diverse picornavirus family, and are known to be released without lysis from infected cells in large vesicles containing numerous RNA genome-containing capsids - a feature allowing for en bloc transmission of multiple viral genomes to newly infected cells that engulf these vesicles. SIRT-1 is an NAD-dependent protein deacetylase that has numerous and wide ranging effects on cellular physiology and homeostasis, and it is known to be engaged in cellular responses to stress and autophagy.

Jassey et al. show that RNAi depletion of SIRT-1 impairs the release of enterovirus D-68 (EV-D68) in EVs recovered from the supernatant fluids of infected cells using a commercial exosome isolation kit. The many functions attributed to SIRT-1 in the literature reflect its capacity to deacetylate various cell proteins engaged in transcription, DNA repair, and regulation of metabolism, apoptosis and autophagy. However, Jassey et al. make the surprising claim that the proviral role of SIRT-1 in promoting enterovirus release is not dependent on its deacetylase activity. Fig. S1C is crucial to this suggestion, as it is said to show that reconstituting expression with a catalytically-inactive mutant can rescue virus release from SIRT-1 depleted cells. However, no information is provided concerning the levels of endogenous and ectopically-expressed SIRT-1 proteins in this experiment, making it very difficult to interpret the results. Is the mutant SIRT-1 protein expressed at a higher level than the non-mutant protein? Is there a 'sponging' effect with these transfections that lessens the siRNA efficiency and reduces knockdown of the endogenous protein? Fig. S1B and Fig. 4C convincingly show that EX527, a small molecule inhibitor of the deacetylase activity of SIRT-1, inhibits extracellular release of the virus. This suggests that the deacetylase activity of SIRT-1 is in fact required for the proviral effect of SIRT-1. This is a fundamentally important question that will require more investigation.

Fig. 6 shows how SIRT-I knockdown impacts the release of enterovirus D68 in EVs recovered from cell culture supernatant using a commercial 'Total Exosome Isolation Kit'. The authors should describe the principle this kit exploits to isolate 'exosomes' (affinity isolation?) and specify which antibodies it involves (anti-phosphatidylserine, anti-CD63, others?) This could impact the outcome of these experiments, and moreover is important to include in the long-term scientific record. The authors are appropriately cautious in describing the vesicles they presume to be isolated by the kit as simply 'extracellular vesicles', since there are multiple types of EVs with very different mechanisms of biogenesis, of which 'exosomes' are but one specific type. It would have been more elegant had the authors shown that SIRT-1 is required for EV-D68 release in detergent-sensitive vesicles with low buoyant density in isopycnic gradients, and to characterize the size and number of viral capsids in these vesicles by electron microscopy.

Fig. 6 shows that SIRT-1 depletion upregulates CD63 expression, but has no apparent impact on the release of CD63-positive 'EVs' from uninfected cells. EV-D68 infection also upregulates CD63 expression in SIRT-1 replete cells, and in this case, increases the release of CD63-positive EVs. The combination of infection and SIRT-1 depletion massively upregulates CD63 expression, but appears to eliminate the enhanced release of CD63-positive EVs resulting from infection alone. These are interesting results, from which the authors infer CD63 is associated with EVs containing EV-D68. But, do we know this? Can a CD63 pulldown immunoprecipitate EV-D68 capsid proteins or viral RNA? CD63 is strongly associated with exosomes released from cells through the multi-vesicular body pathway, which are distinct from the LC3-positive EVs released by secretory autophagy that have previously been associated with enteroviruses. The authors suggest that 'knockdown of SIRT-1 may prevent the exocytosis of CD63-positive EVs", but this is a very broad claim (and not really demonstrated by Fig. 6): it requires a clearer definition of what the authors mean by 'exocytosis' and a much more detailed analysis of the size and buoyant density of EVs released in a SIRT-1-dependent process.

The authors suggest that almost all EV-D68 released from infected cells is released without cell lysis in EVs. However, they generally show data from only a single time point following infection (5 or 6 hrs post-infection). It would have been interesting to see a more complete temporal analysis, and to know whether a high proportion of virus continues to be released in EVs, or if it is swamped out ultimately by lytic release of nonenveloped virus.

Fig. 1D indicates that a small fraction of SIRT-1 leaks from the nucleus in EV-D68 infected cells. The authors suggest this is due to targeted nuclear export, rather than simply leaky nuclear pores which are well known to exist in enterovirus-infected cells. The authors present similar fluorescent microscopy data showing inhibition of TFEB export in leptomycin-B treated cells in Fig. S2A in support of their claim that this is specific SIRT-1 export, but these data are far from convincing - there is equivalent residual TFEB and SIRT-1 in the cytoplasm of the treated cells. Quantitative immunoblots of cytoplasmic and nuclear cell fractions might prove more compelling.

Finally, the authors should be more specific in describing the viruses they have studied (EV-D68 and PV). It would be preferable to describe these as 'enteroviruses' (including in the title of the manuscript), rather than more broadly as 'picornaviruses'. There is no certainty that the requirement for SIRT-1 in non-lytic release of virus extends to hepatoviruses or other picornaviral genera, for which mechanisms of nonlytic release may be quite different.

Reviewer #2 (Public Review):

The authors aimed to connect SIRT-1 to EV-D68 virus release through mediating ER stress. They are successful in robustly connecting these pathways experimentally and show a new role for SIRT-1 in EV-D68 infection. These results extend to additional viruses, suggesting role(s) for SIRT-1 in diverse virus infection.

The authors note that EV-D68 does not significantly impact SIRT-1 protein levels (Fig 1E and F), though this has been described for other picornaviruses (Xander et al., J Immunol 2019; Han et al., J Cell Sci 2016; Kanda et al Biochem Biophys Res Commun 2015). This may be of interest to note in the manuscript.

The data regarding CVB3 (Fig S4) are especially interesting because they show no discernable impact on infection. The manuscript should describe this further and perhaps speculate on potential reasons. Could it be due to inefficient knockdown?

SIRT-1 (and other sirtuins) have been linked to an innate interferon response. Are any of the phenotypes observed here due to IFN responses? The use of H1HeLa cells would suggest this is not the case.

Reviewer #1 (Public Review):

Nitta et al, in their manuscript titled, "Drosophila model to clarify the pathological significance of OPA1 in autosomal dominant optic atrophy." The novelty of this paper lies in its use of human (hOPA1) to try to rescue the phenotype of an OPA1 +/- Drosophilia DOA model (dOPA). The authors then use this model to investigate the differences between dominant-negative and haploinsufficient OPA1 variants. The value of this paper lies in the study of DN/HI variants rather than the establishment of the drosophila model per se as this has existed for some time and does have some significant disadvantages compared to existing models, particularly in the extra-ocular phenotype which is common with some OPA1 variants but not in humans. I judge the findings of this paper to be valuable with regards to significance and solid with regards to the strength of the evidence.

Suggestions for improvements:

1. Stylistically the results section appears to have significant discussion/conclusion/inferences in each section with reference to existing literature. I feel that this information would be better placed in the separate discussion section. E.g. lines 149-154

2. I do think further investigation as to why a reduction of mitochondria was noticed in the knockdown. There are conflicting reports on this in the literature. My own experience of this is fairly uniform mitochondrial number in WT vs OPA1 variant lines but with an increased level of mitophagy presumably reflecting a greater turnover. There are a number of ways to quantify mitochondrial load e.g. mtDNA quantification, protein quantification for tom20/hsp60 or equivalent. I feel the reliance on ICC here is not enough to draw conclusions. Furthermore, mitophagy markers could be checked at the same time either at the transcript or protein level. I feel this is important as it helps validate the drosophila model as we already have a lot of experimental data about the number and function of mitochondria in OPA+/- human/mammalian cells.

3. Could the authors comment on the failure of the dOPA1 rescue to return their biomarker, axonal number to control levels. In Figure 4D is there significance between the control and rescue. Presumably so as there is between the mutant and rescue and the difference looks less.

4. The authors have chosen an interesting if complicated missense variant to study, namely the I382M with several studies showing this is insufficient to cause disease in isolation and appears in high frequency on gnomAD but appears to worsen the phenotype when it appears as a compound het. I think this is worth discussing in the context of the results, particularly with regard to the ability for this variant to partially rescue the dOPA1 model as shown in Figure 5.

5. I feel the main limitation of this paper is the reliance on axonal number as a biomarker for OPA1 function and ultimately rescue. I have concerns because a) this is not a well validated biomarker within the context of OPA1 variants b) we have little understanding of how this is affected by over/under expression and c) if it is a threshold effect e.g. once OPA1 levels reach x%. I think this is particularly relevant when the authors are using this model to make conclusions on dominant negativity/HI with the authors proposing that if expression of a hOPA1 transcript does not increase opa1 expression in a dOPA1 KO then this means that the variant is DN. The authors have used other biomarkers in parts of this manuscript e.g. ROS measurement and mito trafficking but I feel this would benefit from something else particularly in the latter experiments demonstrated in figure 5 and 6.

6. Could the authors clarify what exons in Figure 5 are included in their transcript. My understanding is transcript NM_015560.3 contains exon 4,4b but not 5b. According to Song 2007 this transcript produces invariably s-OPA1 as it contains the exon 4b cleavage site. If this is true, this is a critical limitation in this study and in my opinion significantly undermines the likelihood of the proposed explanation of the findings presented in Figure 6. The primarily functional location of OPA1 is at the IMM and l-OPA1 is the primary opa1 isoform probably only that localizes here as the additional AA act as a IMM anchor. Given this is where GTPase likely oligomerizes the expression of s-OPA1 only is unlikely to interact anyway with native protein. I am not aware of any evidence s-OPA1 is involved in oligomerization. Therefore I don't think this method and specifically expression of a hOPA1 transcript which only makes s-OPA1 to be a reliable indicator of dominant negativity/interference with WT protein function. This could be checked by blotting UAS-hOPA1 protein with a OPA1 antibody specific to human OPA1 only and not to dOPA1. There are several available on the market and if the authors see only s-OPA1 then it confirms they are not expressing l-OPA1 with their hOPA1 construct.

Reviewer #2 (Public Review):

The data presented support and extend some previously published data using Drosophila as a model to unravel the cellular and genetic basis of human Autosomal dominant optic atrophy (DOA). In human, mutations in OPA1, a mitochondrial dynamin like GTPase (amongst others), are the most common cause for DOA. By using a Drosophila loss-of-function mutations, RNAi-mediated knockdown and overexpression, the authors could recapitulate some aspects of the disease phenotype, which could be rescued by the wild-type version of the human gene. Their assays allowed them to distinguish between mutations causing human DOA, affecting the optic system and supposed to be loss-of-function mutations, and those mutations supposed to act as dominant negative, resulting in DOA plus, in which other tissues/organs are affected as well.

Based on the lack of information in the Materials and Methods section and in several figure legends, it was not in all cases possible to follow the conclusions of the authors. Similarly, how the knowledge gained could help to "inform early treatment decisions in patients with mutations in hOPA1" (Line 38) cannot be followed.

Reviewer #3 (Public Review):

Nitta et al. establish a fly model of autosomal dominant optic atrophy, of which hundreds of different OPA1 mutations are the cause with wide phenotypic variance. It has long been hypothesized that missense OPA1 mutations affecting the GTPase domain, which are associated with more severe optic atrophy and extra-ophthalmic neurologic conditions such as sensorineural hearing loss (DOA plus), impart their effects through a dominant negative mechanism, but no clear direct evidence for this exists particularly in an animal model. The authors execute a well-designed study to establish their model, demonstrating a clear mitochondrial phenotype with multiple clinical analogs including optic atrophy measured as axonal degeneration. They then show that hOPA1 mitigates optic atrophy with the same efficacy as dOPA1, setting up the utility of their model to test disease-causing hOPA1 variants. Finally, they leverage this model to provide the first direct evidence for a dominant negative mechanism for 2 mutations causing DOA plus by expressing these variants in the background of a full hOPA1 complement.

Strengths of the paper include well-motivated objectives and hypotheses, overall solid design and execution, and a generally clear and thorough interpretation of their results. The results technically support their primary conclusions with caveats. The first is that both dOPA1 and hOPA1 fail to fully restore optic axonal integrity, yet the authors fail to acknowledge that this only constitutes a partial rescue nor do they discuss how this fact might influence our interpretation of their subsequent results. The second caveat is that their effect sizes are small. Statistically, the results indeed support a dominant negative effect of DOA plus-associated variants, yet the data show a marginal impact on axonal degeneration for these variants. The authors might have considered exploring the impact of these variants on other mitochondrial outcome measures they established earlier on. They might also consider providing some functional context for this marginal difference in axonal optic nerve degeneration.

Despite these caveats, the authors provide the first animal model of DOA that also allows for rapid assessment and mechanistic testing of suspected OPA1 variants. The impact of this work in providing the first direct evidence of a dominant negative mechanism is under-stated considering how important this question is in development of genetic treatments for DOA. The authors discuss important points regarding the potential utility of this model in clinical science. Comments on the potential use of this model to investigate variants of unknown significance in clinical diagnosis requires further discussion of whether there is indeed precedent for this in other genetic conditions (since the model is nevertheless so evolutionarily removed from humans).

Reviewer #1 (Public Review):

Summary:

Favate et al. measure the relative levels of metabolites in 12 Escherichia coli strains isolated from different replicate populations after 50,000 generations of the Lenski long-term laboratory evolution experiment. They use untargeted LC/MS methods that include standards and report both positive and negative ionization mode measurements. They initially use principal component analysis (PCA) to broadly compare how the metabolomes of these strains are similar and different. Then, they describe several instances where the changes in metabolite abundance they see in specific pathways correlate with mutations that lead to changes in the expression of genes that encode enzymes in those pathways.

Strengths:

The statistical analyses and presentation of the high-throughput data are excellent. The most compelling results are communicated in wonderful figures that integrate their measurements of metabolite levels in this study with results from a prior study they conducted looking at changes in gene expression levels in the same bacterial strains. These sections include the ones describing large increases in NAD(P) pools due to mutations in nadR, changes in the levels of arginine and related compounds due to mutations in argR, and changes in metabolites from glycolysis and the TCA cycle related to iclR and arcB.

Weaknesses:

After addressing prior reviews, the main remaining weaknesses of the study are limitations inherent to the metabolomics approach that are noted by the authors. Namely, that it gives a static and incomplete picture of cellular metabolism, lacking any information about flux and missing measurements for many metabolites. Additional biochemical and genetic experiments will be necessary to fully test the hypotheses suggested by the metabolomics data.

Impact and Significance:

While there has been past speculation about the effects of LTEE mutations on metabolism, this study measures changes in the levels of metabolites in related metabolic pathways for the first time. Therefore, it provides useful information about how metabolism evolves, in general, and will also be a useful resource those studying other aspects of the LTEE related to metabolism, such as contingency in the evolution of citrate utilization.

Reviewer #2 (Public Review):

This preprint presents a compelling study examining the relationship between genotypic changes and phenotypic traits in bacteria over an extended period using the Long-Term Evolution Experiment (LTEE) as a model. The primary advances in methodology include employing high-resolution mass spectrometry for comprehensive metabolic profiling and combining it with previous gene expression and DNA sequencing datasets. This approach provides insight into how specific genetic mutations can alter metabolic pathways over 50,000 generations, enabling a deeper understanding of how genetic changes lead to observed differences in evolved bacterial strains. The findings reveal that evolved bacteria possess more diverse metabolic profiles compared to their ancestors, suggesting that these populations have uniquely adapted to their environment. The work also attempts to uncover the molecular basis for this adaptive evolution, demonstrating how specific genetic changes have influenced the bacteria's metabolic pathways.

Overall, this is a significant and well-executed research study. It offers new insights into the complex relationship between genetic changes and observable traits in evolving populations and utilizes metabolomics in the LTEE, a novel approach in combination with RNA-seq and mutation datasets.

Reviewer #2 (Public Review):

The authors investigate the origin of asexual reproduction through hybridization between species. In loaches, diploid, polyploid, and asexual forms have been described in natural populations. The authors experimentally cross multiple species of loaches and conduct an impressively detailed characterization of gametogenesis using molecular cytogenetics to show that although meiosis arrests early in male hybrids, a subset of cells in females undergo endoreplication before meiosis, producing diploid eggs. This only occurred in hybrids of parental species that were of intermediate divergence. This work supports an expanding view of speciation where asexuality could emerge during a narrow evolutionary window where genomic divergence between species is not too high to cause hybrid inviability, but high enough to disrupt normal meiotic processes.

I enjoyed reading this study and I appreciate the amount of work it takes to conduct these types of cytogenetic experiments. But, my main concern with this study is I was left wondering if the sample sizes are large enough to get a sense how variable endoreplication is in these loach species. Most of the hybrids between species are the result of crosses between 1-2 families. Within males and females, meiocyte observations are limited to a handful of pachytene and diplotene stages. I think it would be helpful to be more transparent about the sample sizes in the main text.

Along these lines, the authors argue against the possibility that endoreplication may be predisposed to occur at a higher rate in some species (line 291). Instead, they suggest that endoreplication is a result of perturbing the cell cycle by combining the genomes of two different species. Their main argument is based on gonocyte counts from parental females in a previous reference. It is essential to include counts from the parents used in this study to make a clear comparison with the F1s.

In the discussion (lines 320-333), the authors postulate the sex-specific clonality they observe could be a result of Haldane's rule. Given these fish do not have known sex chromosomes, I do not find this argument strong. Haldane's rule refers to the exposure of recessive incompatibilities with the sex chromosomes in the hybrid heterogametic sex. This effect would therefore be limited to degenerated sex chromosomes where much of the sequence content on the Y or W has been lost. These species may have homomorphic sex chromosomes, but if this is the case, they likely are not very degenerated. Instead, it seems more plausible that the sex-specific effect the authors observe is due to intrinsic differences of spermatogenesis and oogenesis. Is there any information about sex-specific differences in the fidelity of gametogenesis from other species that would support a higher likelihood of endoreplication?

The final thing I was left wondering about was this missing link between endoreplication and activating embryonic development of the diploid egg. In these loach species, a sperm is required to activate egg development, but the sperm genome is discarded (line 100). What is the mechanism of this and how does it evolve concurrently during hybridization?

Reviewer #1 (Public Review):

This paper provides new evidence on the relationship between genetic/chromosome divergence and capacity for asexual reproduction (via unreduced, clonal gametes) in hybrid males or females. Whereas previous studies have focussed just on the hybrid combinations that have yielded asexual lineages in nature, the authors take an experimental approach, analysing meiotic processes in F1 hybrids for combinations of species spanning different levels of divergence, whether or not they form asexual lineages in nature. As such, the findings here are a substantial advance towards understanding how new asexual lineages form.

The quality of the work is high, the analyses are sound, and the authors sensibly link their observations to the speciation continuum. I should also add that the cytogenetic work here is just beautiful!

A key finding is that the precondition for asexual reproduction - the formation of unreduced gametes - is not unusual among hybrid females, so that we have to consider other factors to explain the rarity of asexual species - a major unresolved issue in evolutionary biology. This work also highlights a previously overlooked effect of chromosome organisation on speciation.

Joint Public Review:

The flowering plant Capsella bursa-pastoris is an allotetraploid formed from the genomes of Capsella orientalis and Capsella grandiflora. An outstanding question in the evolution of allotetraploids is the relative contribution of immediate consequences of allopolyploidization vs. long-term evolution after the event. The authors address this question by re-synthesizing the allotetraploid in the lab using the two progenitor species, and comparing its phenotypic and gene expression variation to naturally occurring C. bursa-pastoris. They compared five categories of plant: the two progenitors of the allopolyploid, hybrids resynthesized from the progenitors with a whole-genome duplication either before or after the hybridization event, and the naturally occurring allopolyploid. Two lines of evidence were used: phenotypic data from the plants grown in a common environment, and RNAseq data from a subset of the plants.

The phenotypic data indicate that the selfing syndrome of C. bursa-pastoris likely evolved after the initial allopolyploidization event, and that pollen and seed viability recovered following the allopolyploidization event. They find evidence primarily for long-term phenotypic evolution towards a selfing syndrome in C. bursa-pastoris, and a combination of short and long-term changes to gene expression.

The manuscript is thorough and provides lots of new insights into the mechanisms driving evolution in allopolyploids. The work provides an interesting and valuable contribution to the field's understanding of how expression evolves in interaction with hybridization and polyploidy. Particularly in combination with the team's previous study on these lines, this experimental design is effective for separating the contributions of hybridization, WGD, and evolution over time.

>>The results are compelling but would benefit from small clarifications to the methods and statistics to account for possible positional effects in the growth chamber. Using a linear mixed model rather than a simple ANOVA would solve this problem.

>>The RNAseq data are used to explore overall expression patterns (using multi-dimensional scaling), patterns of differential expression (additive, dominant, or transgressive), and homeolog expression bias, and to determine the relative contributions of the original allopolyploidization event and subsequent evolution. Statistical cutoffs were used to categorize gene expression patterns, but the description and categorization of these patterns appears to have been largely qualitative and might be strengthened by including more statistical detail in questions like whether homeologous expression bias did indeed show more variation in resynthesized and evolved allopolyploids.

>>The study includes evidence that homeolog expression bias (overrepresentation of an allele from one species) results in part from homeologous synapsis (uneven inheritance of chromosome segments). These deviations from patterns consistent with 2:2 inheritance of genomic regions are highly variable between individuals in resynthesized allopolyploids but appeared to be mostly consistent within (but not between) populations in natural C. bursa-pastoris. This is intriguing evidence that segregation can be an important source of variation in allopolyploids. However, it was limited by the difficulty of inferring homeologous recombination breakpoints with RNAseq data because of the scale of recombination in wild populations (rather than resynthesized allopolyploids). In the future identifying such breakpoints will be an interesting direction for this and other allopolyploid systems.

>>The study could also valuably explore what kinds of genes experienced what forms of expression evolution. A brief description of GO terms frequently represented in genes which showed strong patterns of expression evolution might be suggestive of which selective pressures led to the changes in expression in the C. bursa-pastoris lineage, and to what extent they related to adaptation to polyploidization (e.g. cell-cycle regulators), compensating for the initial pollen and seed inviability or adapting to selfing (endosperm- or pollen-specific genes), or adaptation to abiotic conditions.

Reviewer #1 (Public Review):

The paper offers some potentially interesting insight into the allosteric communication pathways of the CTFR protein. A mutation to this protein can cause cystic fibrosis and both synthetic and endogenous ligands exert allosteric control of the function of this pivotal enzyme. The current study utilizes Gaussian Network Models (GNMs) of various substrate and mutational states of CFTR to quantify and characterize the role of individual residues in contributing to two main quantities that the authors deem important for allostery: transfer entropy (TE) and cross correlation. I found the TE of the Apo system and the corresponding statistical analysis particularly compelling. I found it difficult, however, to assess the limitations of the chosen model (GNM) and thus the degree of confidence I should have in the results. This mainly stems from a lack of a proposed mechanism by which allostery is achieved in the protein. Proposing a mechanism and presenting logical alternatives in the introduction would greatly benefit this manuscript. It would also allow the authors to place the allosteric mechanism of this protein in the broader context of protein allostery.

Reviewer #2 (Public Review):

In this study, the authors used ANM-LD and GNM-based Transfer Entropy to investigate the allosteric communications network of CFTR. The modeling results are validated with experimental observations. Key residues were identified as pivotal allosteric sources and transducers and may account for disease mutations.

The paper is well written and the results are significant for understanding CFTR biology.

Reviewer #3 (Public Review):

This study of CFTR, its mutants, dynamics, and effects of ATP binding, and drug binding is well written and highly informative. They have employed coarse-grained dynamics that help to interpret the dynamics in useful and highly informative ways. Overall the paper is highly informative and a pleasure to read.

The investigation of the effects of drugs is particularly interesting, but perhaps not fully formed.

Reviewer #1 (Public Review):

Liu et al. investigated the brain functional lateralization in typically developing infants and infants with congenital sensorineural hearing loss (SNHL) to understand how early auditory deprivation disrupts the development of functional network organization using resting-state fNIRS imaging and the graph theory approach. They found that hemispheric asymmetry formed in early life and the initial lack of auditory exposure affected the typical development of functional network asymmetry in infants with hearing loss. Although the infants with hearing loss exhibited a balance between information segregation and integration within two hemispheres, consistent with the typically developing (TD) controls, the development of the leftward hemispheric asymmetry in network efficiency measures was disrupted. At the regional level, infants with hearing loss exhibited aberrant development of hemispheric network asymmetry especially in frontal regions.

Strengths:<br /> The strengths of this study include its focus on a relatively understudied area of research, namely the impact of hearing loss on brain network asymmetry in infants. The study used advanced neuroimaging techniques to examine the development of cerebral asymmetry in infants with hearing loss and compared their results to typically developing controls. The study's findings provide valuable insights into the importance of early auditory exposure for typical brain development. Overall, this study contributes to our understanding of the brain functional network changes underlying hearing loss and has important implications for early intervention and treatment strategies.

Weaknesses:<br /> Although this study does have strengths in principle, the weaknesses of this work are that the key claims cannot be fully supported due to inappropriate statistical analyses, the theoretical significance and the narrative logic are not well presented. In particular:

Theoretical significance: In the Introduction, the authors did not nicely explain why it is important to investigate how the brain functional network asymmetry develops in SNHL infants, and what new knowledge this analytical approach can tell the readers. It is insufficient to merely state that few studies have focused on this. The authors did not elaborate on the broader significance of studying the hemispherical asymmetry in SNHL infants.

Narrative logic: The organization of the Results part needs substantial improvement. The authors did not provide an overview of the analysis at the beginning of each results section, including the relationships between different measurements, the purpose of each analysis, the specific methods employed, and the meaning of the neural index used. It is therefore very difficult to understand why the authors conducted each analysis and how it contributes to the main narrative of the study. For instance, what is the relationship between the small-world properties within the hemisphere and the hemispherical asymmetry of network efficiency? What is the relationship between global/local efficiency and regional nodal efficiency? What global efficiency and local efficiency reflect? It is crucial to clarify and justify the analysis.

Problems on the statistics:<br /> 1) To support the major claim that the left hemisphere dominance of the functional network organization was significantly disrupted in SNHL infants, the authors should also report a statistically significant interaction (between leftward hemispheric asymmetry and type of infants), but instead they only reported that one effect (the leftward hemispheric asymmetry in the TD infants) was statistically significant, whereas the other effect (the leftward hemispheric asymmetry in the infants with SNHL) was not. And why not directly use asymmetry index and compare it between groups?<br /> 2) The necessary statistical values to support the conclusions are missing in several places. For example, Lines 111 - 113 and section 2.4.<br /> 3) The authors conducted multiple comparisons without correction in section 2.3 and section 2.5. It is likely that some of these comparisons would not survive the multiple comparison correction; therefore, the results need to be rephrased and the findings reinterpreted accordingly.<br /> 4) Inconsistent results exist. If "a significant group × age interaction effect on the mean AI of nodal efficiency was observed only in the frontal cortex, while other regions did not exhibit such an interaction" (Line 170-172), and the authors "investigated the group × age interaction effect on the mean nodal efficiencies of the frontal regions for each hemisphere" (Line 178-179), why "a significant interaction effect was observed in the frontal, temporal, parietal, and occipital regions of the left hemisphere" (Line 179-182)?

Reviewer #2 (Public Review):

Using fNIRS and resting state recordings of brain activity, authors have compared functional network organization in infants with congenital sensorineural hearing loss (SNHL) as well as typically developing infants. The manuscript reports a disruption in the development of leftward hemispheric lateralization in SNHL infants as compared to typically developing infants, across several network measures. The study used an adapted methodology for infants, and involved an adequate number of infants for cross-sectional studies and the findings are valuable. However, a number of methodological points and controls need to be taken into account to better explain the results and to remove redundancy. Moreover, the discussion can be improved by a more detailed comparison between the current work and the past literature.

- My major concern is that functional connectivity patterns change importantly depending on the sleep stage (Uchitel et al., 2021 Pediatric Research; Tóth et al., 2017 Human Brain mapping), it is therefore not enough to have all infants sleep, but to have them on the same sleep stage. Therefore, authors need to re-analyze their dataset taking into account sleep stage as a factor, i.e. grouping infants based on the sleep stage (otherwise it can be a confounding factor - as one can imagine that infants with sensorineural hearing loss may enter "quiet sleep" faster in a short recording session - given the environmental noise does not bother them etc.). This could completely change the interpretation of the results. Do authors have a mean in the data or via additional recordings (respiration, EMG, ECG?) to separate the sleep stages?

- Several statistical analyses are performed with redundancy, i.e. several effects are looked at in more than one test: for example one ANOVA analysis with several factors including group (SNHL/typical) as a factor, is followed by two other separate ANOVAs with the same variables as before but redone for each group separately. The latter tests are redundant. This has happened across different sections, making the manuscript unnecessarily long while also reporting effects that are redundant.

- Given the number of statistical comparisons performed, it would be helpful that authors better explain how corrections are performed: number of comparisons for each correction or which tests are considered independent (i.e. across which correction of multiple comparisons are not performed).

- The discussion generally needs to be improved: both for the position of the current study/novelty/strength and its limitations with respect to the previous works (Cui et al 2022- also looking into early functional organization in SNHL, etc) and also in terms of the differences in findings (i.e. associations of functional connectivity measures to hearing loss severity)

Reviewer #2 (Public Review):

The authors examine the transport of chemical compounds from a surrounding fluid environment to the surface of the polyp Hydra. They propose that spontaneous contractions of the body, which are known to occur roughly three times per hour, provide a new fluid environment near the body surface and thereby increase the total rate of compound uptake. Experimental measurements and a mathematical model are used to support the main claim. Active probes of the system involve the use of ion channel inhibitors, which can affect the frequency of contractions. But there is a useful feature of Hydra already present which the authors also use for a comparative study, namely the different microbial environments near the Hydra's motionless foot and near its moving head. The evidence which is provided puts the claim on solid footing. The main result represents an important observation about the role of hydrodynamics on organism behavior, in particular in its relation to diffusive chemical transport processes.

Reviewer #2 (Public Review):

The authors wanted to determine if the mRNA modification m6A is involved in axonal regeneration pathways. They performed a small-scale siRNA screen targeting major components of this pathway to determine if not down if any of these genes would influence axonal regeneration. They identified ALKBH5, an m6A demethylating enzyme, as a gene that represses axonal regeneration after injury, and when knocked down, promotes axonal growth. They identify a putative mRNA target of ALKBH5, Lpin2, which they believe is demethylated by ALKBH5, resulting in higher levels of m6A on this transcript and thus greater mRNA degradation and reduced expression.

This study has major weaknesses. The ALKBH5 knockout mouse is not used. Thus the experiment relies on the selectivity of the siRNA. Many experiments relied on the single siRNA. The knockdown efficiency was relatively poor, with only a small change in ALKBH5 protein levels. The authors never assess whether m6A levels are indeed affected by ALKBH5 depletion using their approach. The results are therefore unconvincing because of not using the appropriate mouse model. Additionally, the authors' attempt to identify a target of ALKBH5 was not done using the appropriate approach, which would involve globally profiling m6A levels in control and ALKBH5 knockout conditions. Since they did not do global profiling of m6A, the authors cannot report how the exact stoichiometry of m6A sites in Lpin2 is affected (and if other mRNAs are affected which might be the true targets of ALKBH5). Attempts by other investigators to identify bona fide targets of ALKBH5 have been difficult, and the authors did not do the appropriate unbiased transcriptome-wide screen but instead used generic gene expression approaches to come to their target. It is not clear if they have a direct or indirect target of ALKBH5 based on the presented data.

Overall, the authors have not achieved their aims and the results do not support the overall conclusions. However, some studies related to Lpin2 overexpression and not down suggest that this gene indeed can influence axonal regeneration in some way. But whether it is a direct target of ALKBH5 and whether ALKBH5 indeed has any role in axonal regeneration is still not clear.

Reviewer #1 (Public Review):

Olszyński and colleagues present data showing variability from canonical "aversive calls", typically described as long 22 kHz calls rodents emit in aversive situations. Similarly long but higher-frequency (44 kHz) calls are presented as a distinct call type, including analyses both of their acoustic properties and animals' responses to hearing playback of these calls. While this work adds an intriguing and important reminder, namely that animal behavior is often more variable and complex than perhaps we would like it to be, there is some caution warranted in the interpretation of these data. The authors also do not provide adequate justification for the use of solely male rodents. With several reported sex differences in rat vocal behaviors this means caution should be exercised when generalizing from these findings.

Firstly, the authors argue that the shift to higher-frequency aversive calls is due to an increase in arousal (caused by the animals having received multiple aversive foot shocks towards the end of the protocols). However, it cannot be ruled out that this shift would be due to factors such as the passage of time and increase in fatigue of the animals as they make vocalizations (and other responses) for extended periods of time. In fact the gradual frequency increase reported for 22kHz calls and the drop in 44 kHz calls the next day in testing is in line with this.

Secondly, regarding the analysis where calls were sorted using DBSCAN based on peak frequency and duration, it is not surprising that the calls cluster based on frequency and duration, i.e. the features that are used to define the 44 kHz calls in the first place. Thus presenting this clustering as evidence of them being truly distinct call types comes across as a circular argument. The sparsity of calls in the 30-40 kHz range (shown in the individual animal panels in Figure 2C) could in theory be explained by some bioacoustics properties of rat vocal cords, without necessarily the calls below and above that range being ethologically distinct.

The behavioral response to call playback is intriguing, although again more in line with the hypothesis that these are not a distinct type of call but merely represent expected variation in vocalization parameters. Across the board animals respond rather similarly to hearing 22 kHz calls as they do to hearing 44 kHz calls, with occasional shifts of 44 kHz call responses to an intermediate between appetitive and aversive calls. This does raise interesting questions about how, ethologically, animals may interpret such variation and integrate this interpretation in their responses. However, the categorical approach employed here does not address these questions fully.

In sum, rather than describing the 44kHz long calls as a new call type, it may be more accurate to say that sometimes aversive calls can occur at frequencies above 22 kHz. Individual and situational variability in vocalization parameters seems to be expected, much more so than all members of a species strictly adhering to extremely non-variable behavioral outputs.

Reviewer #2 (Public Review):

Olszyński et al. claim that they identified a "new-type" ultrasonic vocalization around 44 kHz that occurs in response to prolonged fear conditioning (using foot-shocks of relatively high intensity, i.e. 1 mA) in rats. Typically, negative 22-kHz calls and positive 50-kHz calls are distinguished in rats, commonly by using a frequency threshold of 30 or 32 kHz. Olszyński et al. now observed so-called "44-kHz" calls in a substantial number of subjects exposed to 10 tone-shock pairings, yet call emission rate was low (according to Fig. 1G around 15%, according to the result text around 7.5%). They also performed playback experiments and concluded that "the responses to 44-kHz aversive calls presented from the speaker were either similar to 22-kHz vocalizations or in-between responses to 22-kHz and 50-kHz playbacks".

Strengths: Detailed spectrographic analysis of a substantial data set of ultrasonic vocalizations recorded during prolonged fear conditioning, combined with playback experiments.

Weaknesses: I see a number of major weaknesses.

While the descriptive approach applied is useful, the findings have only focused importance and scope, given the low prevalence of "44 kHz" calls and limited attempts made to systematically manipulate factors that lead to their emission. In fact, the data presented appear to be derived from reanalyses of previously conducted studies in most cases and the main claims are only partially supported. While reading the manuscript, I got the impression that the data presented here are linked to two or three previously published studies (Olszyński et al., 2020, 2021, 2023). This is important to emphasize for two reasons: 1) It is often difficult (if not impossible) to link the reported data to the different experiments conducted before (and the individual experimental conditions therein). While reanalyzing previously collected data can lead to important insight, it is important to describe in a clear and transparent manner what data were obtained in what experiment (and more specifically, in what exact experimental condition) to allow appropriate interpretation of the data. For example, it is said that in the "trace fear conditioning experiment" both single- and group-housed rats were included, yet I was not able to tell what data were obtained in single- versus group-housed rats. This may sound like a side aspect, however, in my view this is not a side aspect given the fact that ultrasonic vocalizations are used for communication and communication is affected by the social housing conditions. 2) In at least two of the previously published manuscripts (Olszyński et al., 2021, 2023), emission of ultrasonic vocalizations was analyzed (Figure S1 in Olszyński et al., 2021, and Fig. 1 in Olszyński et al., 2023). This includes detailed spectrographic analyses covering the frequency range between 20 and 100 kHz, i.e. including the frequency range, where the "new-type" ultrasonic vocalization, now named "44 kHz" call, occurs, as reflected in the examples provided in Fig. 1 of Olszyński et al. (2023). In the materials and methods there, it was said: "USV were assigned to one of three categories: 50-kHz (mean peak frequency, MPF >32 kHz), short 22-kHz (MPF of 18-32 kHz, <0.3 s duration), long 22-kHz (MPF of 18-32 kHz, >0.3 s duration)". Does that mean that the "44 kHz" calls were previously included in the count for 50-kHz calls? Or were 44 kHz calls (intentionally?) left out? What does that mean for the interpretation of the previously published data? What does that mean for the current data set? In my view, there is a lack of transparency here.

Moreover, whether the newly identified call type is indeed novel is questionable, as also mentioned by the authors in their discussion section. While they wrote in the introduction that "high-pitch (>32 kHz), long and monotonous ultrasonic vocalizations have not yet been described", they wrote in the discussion that "long (or not that long (Biały et al., 2019)), frequency-stable high-pitch vocalizations have been reported before (e.g. Sales, 1979; Shimoju et al., 2020), notably as caused by intense cholinergic stimulation (Brudzynski and Bihari, 1990) or higher shock-dose fear conditioning (Wöhr et al., 2005)" (and I wish to add that to my knowledge this list provided by the authors is incomplete). Therefore, I believe, the strong claims made in abstract ("we are the first to describe a new-type..."), introduction ("have not yet been described"), and results ("new calls") are not justified.

In general, the manuscript is not well written/ not well organized, the description of the methods is insufficient, and it is often difficult (if not impossible) to link the reported data to the experiments/ experimental conditions described in the materials and methods section. For example, I miss a clear presentation of basic information: 1) How many rats emitted "44 kHz" calls (in total, per experiment, and importantly, also per experimental condition, i.e. single- versus group-housed)? 2) Out of the ones emitting "44 kHz" calls, what was the prevalence of "44 kHz" calls (relative to 22- and 50-kHz calls, e.g. shown as percentage)? 3) How did this ratio differ between experiments and experimental conditions? 4) Was there a link to freezing? Freezing was apparently analyzed before (Olszyński et al., 2021, 2023) and it would be important to see whether there is a correlation between "44-kHz" calls and freezing. Moreover, it would be important to know what behavior the rats are displaying while such "44-kHz" calls are emitted? (Note: Even not all 22-kHz calls are synced to freezing.) All this could help to substantiate the currently highly speculative claims made in the discussion section ("frequency increases with an increase in arousal" and "it could be argued that our prolonged fear conditioning increased the arousal of the rats with no change in the valence of the aversive stimuli"). Such more detailed analyses are also important to rule out the possibility that the "new-type" ultrasonic vocalization, the so-called "44 kHz" call, is simply associated with movement/ thorax compression.

The figures currently included are purely descriptive in most cases - and many of them are just examples of individual rats (e.g. majority of Fig. 1, all of Fig. 2 to my understanding, with the exception of the time course, which in case of D is only a subset of rats ("only rats that emitted 44-kHz calls in at least seven ITI are plotted" - is there any rationale for this criterion?)), or, in fact, just representative spectrograms of calls (all of Fig. 3, with the exception of G, all of Fig. 4). Moreover, the differences between Fig. 5 and Fig. 6 are not clear to me. It seems Fig. 5B is included three times - what is the benefit of including the same figure three times? A systematic comparison of experimental conditions is limited to Fig. 7 and Fig. 8, the figures depicting the playback results (which led to the conclusion that "the responses to 44-kHz aversive calls presented from the speaker were either similar to 22-kHz vocalizations or in-between responses to 22-kHz and 50-kHz playbacks", although it remains unclear to me why differences were seen b e f o r e the experimental manipulation, i.e. the different playback types in Fig. 8B).

Related to that, I miss a clear presentation of relevant methodological aspects: 1) Why were some rats single-housed but not the others? 2) Is the experimental design of the playback study not confounded? It is said that "one group (n = 13) heard 50-kHz appetitive vocalization playback while the other (n = 16) 22-kHz and 44-kHz aversive calls". How can one compare "44 kHz" calls to 22- and 50-kHz calls when "44 kHz" calls are presented together with 22-kHz calls but not 50-kHz calls? What about carry-over effects? Hearing one type of call most likely affects the response to the other type of call. It appears likely that rats are a bit more anxious after hearing aversive 22-kHz calls, for example. Therefore, it would not be very surprising to see that the response to "44 kHz" calls is more similar to 22-kHz calls than 50-kHz calls. Of note, in case of the other playback experiment it is just said that rats "received appetitive and aversive ultrasonic vocalization playback" but it remains unclear whether "44 kHz" calls are seen as appetitive or aversive. Later it says that "rats were presented with two 10-s-long playback sets of either 22-kHz or 44-kHz calls, followed by one 50-kHz modulated call 10-s set and another two playback sets of either 44-kHz or 22-kHz calls not previously heard" (and wonder what data set was included in the figures and how - pooled?). Again, I am worried about carry-over effects here. This does not seem to be an experimental design that allows to compare the response to the three main call types in an unbiased manner. Of note, what exactly is meant by "control rats" in the context of fear conditioning is also not clear to me. One can think of many different controls in a fear conditioning experiment. More concrete information is needed.