Reviewer #3 (Public review):

Summary:

One goal of this paper is to introduce a new approach for highly accurate decoding of finger movements from human magnetoencephalography data via dimension reduction of a "multi-scale, hybrid" feature space. Following this decoding approach, the authors aim to show that early skill learning involves "contextualization" of the neural coding of individual movements, relative to their position in a sequence of consecutive movements. Furthermore, they aim to show that this "contextualization" develops primarily during short rest periods interspersed with skill training, and correlates with a performance metric which the authors interpret as an indicator of offline learning.

Strengths:

A clear strength of the paper is the innovative decoding approach, which achieves impressive decoding accuracies via dimension reduction of a "multi-scale, hybrid space". This hybrid-space approach follows the neurobiologically plausible idea of the concurrent distribution of neural coding across local circuits as well as large-scale networks. A further strength of the study is the large number of tested dimension reduction techniques and classifiers (though the manuscript reveals little about the comparison of the latter).

A simple control analysis based on shuffled class labels could lend further support to this complex decoding approach. As a control analysis that completely rules out any source of overfitting, the authors could test the decoder after shuffling class labels. Following such shuffling, decoding accuracies should drop to chance level for all decoding approaches, including the optimized decoder. This would also provide an estimate of actual chance-level performance (which is informative over and beyond the theoretical chance level). Furthermore, currently, the manuscript does not explain the huge drop in decoding accuracies for the voxel-space decoding (Figure 3B). Finally, the authors' approach to cortical parcellation raises questions regarding the information carried by varying dipole orientations within a parcel (which currently seems to be ignored?) and the implementation of the mean-flipping method (given that there are two dimensions - space and time - what do the authors refer to when they talk about the sign of the "average source", line 477?).

Weaknesses:

A clear weakness of the paper lies in the authors' conclusions regarding "contextualization". Several potential confounds, described below, question the neurobiological implications proposed by the authors and provide a simpler explanation of the results. Furthermore, the paper follows the assumption that short breaks result in offline skill learning, while recent evidence, described below, casts doubt on this assumption.

The authors interpret the ordinal position information captured by their decoding approach as a reflection of neural coding dedicated to the local context of a movement (Figure 4). One way to dissociate ordinal position information from information about the moving effectors is to train a classifier on one sequence and test the classifier on other sequences that require the same movements, but in different positions (Kornysheva et al., Neuron 2019). In the present study, however, participants trained to repeat a single sequence (4-1-3-2-4). As a result, ordinal position information is potentially confounded by the fixed finger transitions around each of the two critical positions (first and fifth press). Across consecutive correct sequences, the first keypress in a given sequence was always preceded by a movement of the index finger (=last movement of the preceding sequence), and followed by a little finger movement. The last keypress, on the other hand, was always preceded by a ring finger movement, and followed by an index finger movement (=first movement of the next sequence). Figure 4 - Supplement 2 shows that finger identity can be decoded with high accuracy (>70%) across a large time window around the time of the key press, up to at least {plus minus}100 ms (and likely beyond, given that decoding accuracy is still high at the boundaries of the window depicted in that figure). This time window approaches the keypress transition times in this study. Given that distinct finger transitions characterized the first and fifth keypress, the classifier could thus rely on persistent (or "lingering") information from the preceding finger movement, and/or "preparatory" information about the subsequent finger movement, in order to dissociate the first and fifth keypress. Currently, the manuscript provides no evidence that the context information captured by the decoding approach is more than a by-product of temporally extended, and therefore overlapping, but independent neural representations of consecutive keypresses that are executed in close temporal proximity - rather than a neural representation dedicated to context.

Such temporal overlap of consecutive, independent finger representations may also account for the dynamics of "ordinal coding"/"contextualization", i.e., the increase in 2-class decoding accuracy, across Day 1 (Figure 4C). As learning progresses, both tapping speed and the consistency of keypress transition times increase (Figure 1), i.e., consecutive keypresses are closer in time, and more consistently so. As a result, information related to a given keypress is increasingly overlapping in time with information related to the preceding and subsequent keypresses. The authors seem to argue that their regression analysis in Figure 5 - Figure Supplement 3 speaks against any influence of tapping speed on "ordinal coding" (even though that argument is not made explicitly in the manuscript). However, Figure 5 - Figure Supplement 3 shows inter-individual differences in a between-subject analysis (across trials, as in panel A, or separately for each trial, as in panel B), and, therefore, says little about the within-subject dynamics of "ordinal coding" across the experiment. A regression of trial-by-trial "ordinal coding" on trial-by-trial tapping speed (either within-subject or at a group-level, after averaging across subjects) could address this issue. Given the highly similar dynamics of "ordinal coding" on the one hand (Figure 4C), and tapping speed on the other hand (Figure 1B), I would expect a strong relationship between the two in the suggested within-subject (or group-level) regression. Furthermore, learning should increase the number of (consecutively) correct sequences, and, thus, the consistency of finger transitions. Therefore, the increase in 2-class decoding accuracy may simply reflect an increasing overlap in time of increasingly consistent information from consecutive keypresses, which allows the classifier to dissociate the first and fifth keypress more reliably as learning progresses, simply based on the characteristic finger transitions associated with each. In other words, given that the physical context of a given keypress changes as learning progresses - keypresses move closer together in time and are more consistently correct - it seems problematic to conclude that the mental representation of that context changes. To draw that conclusion, the physical context should remain stable (or any changes to the physical context should be controlled for).

A similar difference in physical context may explain why neural representation distances ("differentiation") differ between rest and practice (Figure 5). The authors define "offline differentiation" by comparing the hybrid space features of the last index finger movement of a trial (ordinal position 5) and the first index finger movement of the next trial (ordinal position 1). However, the latter is not only the first movement in the sequence but also the very first movement in that trial (at least in trials that started with a correct sequence), i.e., not preceded by any recent movement. In contrast, the last index finger of the last correct sequence in the preceding trial includes the characteristic finger transition from the fourth to the fifth movement. Thus, there is more overlapping information arising from the consistent, neighbouring keypresses for the last index finger movement, compared to the first index finger movement of the next trial. A strong difference (larger neural representation distance) between these two movements is, therefore, not surprising, given the task design, and this difference is also expected to increase with learning, given the increase in tapping speed, and the consequent stronger overlap in representations for consecutive keypresses. Furthermore, initiating a new sequence involves pre-planning, while ongoing practice relies on online planning (Ariani et al., eNeuro 2021), i.e., two mental operations that are dissociable at the level of neural representation (Ariani et al., bioRxiv 2023).

Given these differences in the physical context and associated mental processes, it is not surprising that "offline differentiation", as defined here, is more pronounced than "online differentiation". For the latter, the authors compared movements that were better matched regarding the presence of consistent preceding and subsequent keypresses (online differentiation was defined as the mean difference between all first vs. last index finger movements during practice). It is unclear why the authors did not follow a similar definition for "online differentiation" as for "micro-online gains" (and, indeed, a definition that is more consistent with their definition of "offline differentiation"), i.e., the difference between the first index finger movement of the first correct sequence during practice, and the last index finger of the last correct sequence. While these two movements are, again, not matched for the presence of neighbouring keypresses (see the argument above), this mismatch would at least be the same across "offline differentiation" and "online differentiation", so they would be more comparable.

A further complication in interpreting the results regarding "contextualization" stems from the visual feedback that participants received during the task. Each keypress generated an asterisk shown above the string on the screen, irrespective of whether the keypress was correct or incorrect. As a result, incorrect (e.g., additional, or missing) keypresses could shift the phase of the visual feedback string (of asterisks) relative to the ordinal position of the current movement in the sequence (e.g., the fifth movement in the sequence could coincide with the presentation of any asterisk in the string, from the first to the fifth). Given that more incorrect keypresses are expected at the start of the experiment, compared to later stages, the consistency in visual feedback position, relative to the ordinal position of the movement in the sequence, increased across the experiment. A better differentiation between the first and the fifth movement with learning could, therefore, simply reflect better decoding of the more consistent visual feedback, based either on the feedback-induced brain response, or feedback-induced eye movements (the study did not include eye tracking). It is not clear why the authors introduced this complicated visual feedback in their task, besides consistency with their previous studies.

The authors report a significant correlation between "offline differentiation" and cumulative micro-offline gains. However, it would be more informative to correlate trial-by-trial changes in each of the two variables. This would address the question of whether there is a trial-by-trial relation between the degree of "contextualization" and the amount of micro-offline gains - are performance changes (micro-offline gains) less pronounced across rest periods for which the change in "contextualization" is relatively low? Furthermore, is the relationship between micro-offline gains and "offline differentiation" significantly stronger than the relationship between micro-offline gains and "online differentiation"?

The authors follow the assumption that micro-offline gains reflect offline learning. However, there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level. On the contrary, recent evidence questions this interpretation (Gupta & Rickard, npj Sci Learn 2022; Gupta & Rickard, Sci Rep 2024; Das et al., bioRxiv 2024). Instead, there is evidence that micro-offline gains are transient performance benefits that emerge when participants train with breaks, compared to participants who train without breaks, however, these benefits vanish within seconds after training if both groups of participants perform under comparable conditions (Das et al., bioRxiv 2024).

Reviewer #3 (Public review):

Summary:

To make feeding decisions, animals need to process three types of information: positive cues like sweetness, negative cues like bitterness, and internal states such as hunger or satiety. This study aims to identify where the information is integrated into the fruit fly brain. The authors applied RNA sequencing on second-order gustatory neurons responsible for sweet and bitter processing, under fed and starved conditions. The sequencing data reveal significant changes in gene expression across sweet vs. bitter pathways and fed vs. starved states. The authors focus on the neuropeptide Leucokinin (Lk), whose expression is dependent on the starvation state. They identify a pair of neurons, named SELK neurons, which express Lk and receive direct input from both sweet and bitter gustatory neurons. These SELK neurons are ideal candidates to integrate gustatory and internal state information. Behavioral experiments show that blocking these neurons in starved flies alters their tolerance to bitter substances during feeding.

Strengths:

(1) The study employs a well-designed approach, targeting specific neuronal populations, which is more efficient and precise compared to traditional large-scale genetic screening methods.

(2) The RNAseq results provide valuable data that can be utilized in future studies to explore other molecules beyond Lk.

(3) The identification of SELK neurons offers a promising avenue for future research into how these neurons integrate conflicting gustatory signals and internal state information.

Weaknesses:

(1) Unfortunately, due to technical challenges, the authors were unable to directly image the functional activity of SELK neurons.

(2) In the behavioral experiments, tetanus toxin was used to block SELK neurons. Since these neurons may release multiple neurotransmitters or neuropeptides, the results do not specifically demonstrate that Leucokinin (Lk) is the critical factor, as suggested in Figure 8. To address this, I recommend using RNAi to inhibit Lk expression in SELK neurons and comparing the outcomes to wild-type controls via the PER assay.

DOI: 10.1038/s41598-023-51091-3

Resource: RRID:BDSC_33797

Curator: @maulamb

SciCrunch record: RRID:BDSC_33797

What is this?

Reviewer #3 (Public review):

Summary:

In this manuscript, Last and colleagues describe Ais, an open-source software package for the semi-automated segmentation of cryo-electron tomography (cryo-ET) maps. Specifically, Ais provides a graphical user interface (GUI) for the manual segmentation and annotation of specific features of interest. These manual annotations are then used as input ground-truth data for training a convolutional neural network (CNN) model, which can then be used for automatic segmentation. Ais provides the option of several CNNs so that users can compare their performance on their structures of interest in order to determine the CNN that best suits their needs. Additionally, pretrained models can be uploaded and shared to an online database.

Algorithms are also provided to characterize "model interactions" which allows users to define heuristic rules on how the different segmentations interact. For instance, a membrane adjacent protein can have rules where it must colocalize a certain distance away from a membrane segmentation. Such rules can help reduce false positives; as in the case above, false negatives predicted away from membranes are eliminated.

The authors then show how Ais can be used for particle picking and subsequent subtomogram averaging and for segmentation of cellular tomograms for visual analysis. For subtomogram averaging, they used a previously published dataset and compared the averages of their automated picking with the published manual picking. Analysis of cellular tomogram segmentations were primarily visual.

Strengths:

CNN-based segmentation of cryo-ET data is a rapidly developing area of research, as it promises substantially faster results than manual segmentation as well as the possibility for higher accuracy. However, this field is still very much in the development and the overall performance of these approaches, even across different algorithms, still leaves much to be desired. In this context, I think Ais is an interesting packages, as it aims to provide both new and experienced users streamlined approaches for manual annotation, access to a number of CNNs, and methods to refine the outputs of CNN models against each other. I think this can be quite useful for users, particularly as these methods develop.

Reviewer #3 (Public review):

Summary:

The manuscript by Wang and colleagues describes single molecule localization microscopy to quantify the distribution and organization of Nipah virus F expressed on cells and on virus-like particles. Notably the crystal structure of F indicated hexameric assemblies of F trimers. The authors propose that F clustering favors membrane fusion.

Strengths:

The manuscript provides solid data on imaging of F clustering with the main findings of:<br /> - F clusters are independent of expression levels<br /> - Proteolytic cleavage does not affect F clustering<br /> - Mutations that have been reported to affect the hexamer interface reduce clustering on cells and its distribution on VLPs<br /> - F nanoclusters are stabilized by AP

Comments on the revised version:

The authors addressed most of my previous concerns.

Reviewer #3 (Public review):

This valuable manuscript demonstrates the long-held prediction that the glycosyltransferase UGGT slows degradation of endoplasmic reticulum (ER)-associated degradation substrates through a mechanism involving re-glucosylation of asparagine-linked glycans following release from the calnexin/calreticulin lectins. The evidence supporting this conclusion is solid using genetically-deficient cell models and well established biochemical methods to monitor the degradation of trafficking-incompetent ER-associated degradation substrates, although this could be improved by better defining of the importance of UGGT in the secretion of trafficking competent substrates. This work will be of specific interest to those interested in mechanistic aspects of ER protein quality control and protein secretion.

The authors have largely addressed my comments from the previous round of review. The only remaining comment is about defining the impact of UGGT1 in the regulation of secretion-competent proteins, which the authors indicate they will continue to pursue in subsequent work, which is fine, but remains a minor limitation of the study.

As I mentioned in my previous review, I think that this work is interesting and addresses an important gap in experimental evidence supporting a previously asserted dogma in the field. I do think that the authors would be better suited for highlighting the limitations of the study, as discussed above. Ultimately, though, this is an important addition to the literature.

Reviewer #3 (Public review):

Jo and colleagues set out to investigate the origins and functions of localized FGF/ERK signaling for the differentiation and spatial patterning of primitive streak fates of human embryonic stem cells in a well-established micropattern system. They demonstrate that endogenous FGF signaling is required for ERK activation in a ring-domain in the micropatterns, and that this localized signaling is directly required for differentiation and spatial patterning of specific cell types. Through high-resolution microscopy and transwell assays, they show that cells receive FGF signals through basally localized receptors. Finally, the authors find that there is a requirement for exogenous FGF2 to initiate primitive streak-like differentiation, but endogenous FGFs, especially FGF4 and FGF17, fully take over at later stages.

Even though some of the authors' findings - such as the localized expression of FGF ligands during gastrulation and the importance of FGF/ERK signaling for cell differentiation in the primitive streak - have been reported in model organisms before, this is one of the first studies to investigate the role of FGF signaling during primitive streak-like differentiation of human cells. In doing so, the paper reports a number of interesting and valuable observations, namely the basal localization of FGF receptors which mirrors that of BMP and Nodal receptors, as well as the existence of a positive feedback loop centered on FGF signaling that drives primitive-streak differentiation. The authors also perform a comparison of the role of different FGFs across species and try to assign specific functions to individual FGFs. In the absence of clean genetic loss-of-function cell lines, this part of the work remains less strong.

Reviewer #3 (Public review):

Summary:

In this study, the authors show that DNA polymerase kappa POLK relocalizes in the cytoplasm as granules with age in mice. The reduction of nuclear POLK in old brains is congruent with an increase in DNA damage markers. The cytoplasmic granules colocalize with stress granules and endo-lysosome. The study proposes that protein localization of POLK could be used to determine the biological age of brain tissue sections.

Strengths:

Very few studies focus on the POLK protein in the peripheral nervous system (PNS). The microscopy approach used here is also very relevant: it allows the authors to highlight a radical change in POLK localization (nuclear versus cytoplasmic) depending on the age of the neurons.

The conclusions of the study are strong. Several types of neurones are compared, the colocalization with several proteins from the NHEJ and BER repair pathways is tested, and microscopy images are systematically quantified.

Weaknesses:

The authors do not discuss the physical nature of POLK granules. There is a large field of research dedicated to the nature and function of condensates: in particular numerous studies have shown that some condensates but not all exhibit liquid-like properties (https://www.nature.com/articles/nrm.2017.7, https://pubmed.ncbi.nlm.nih.gov/33510441/ https://www.mdpi.com/2073-4425/13/10/1846). The change of physical properties of condensates is particularly important in cells undergoing stress and during aging. The authors should discuss this literature.

Reviewer #3 (Public review):

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

There are some limitations to the work. The argument for the novelty of the approach could be better articulated. While the opportunities for new discoveries presented by the identification of discrepant susceptibility results between related species are evident, it is less clear how the macroevolutionary approach is further leveraged for the discovery of truly novel resistance determinants. The example of the discovery of Arr-X enzymes presented here relied upon foundational knowledge of previously characterized Arr orthologs. There is little clarity on what the pipeline for identifying more novel resistance determinants would look like. In other words, what does the macroevolutionary perspective contribute to discovery from the point of finding interspecies differences in susceptibility? Does the framework still remain distinct from other discovery frameworks and approaches? If so, how?

While the experimentation and analyses performed appear well-designed and rigorous, there are a few instances in which broad claims are based on inferences from sample sets or data sets that are too limited to provide robust support. For example, the claim that rifampicin modification, and precisely ADP-ribosylation, is the dominant mechanism of resistance to rifampicin in mycobacteria may be a bit premature or an over-generalization, as other enzymatic modification mechanisms and other mechanisms such as helR-mediated dissociation of rifampicin-stalled RNA polymerases, efflux, etc were not examined nor were CRISPRi knockdown experiments conducted beyond an experiment to tease out the role of Arr-X and Arr-1 in one strain. The general claim that intra-bacterial antibiotic accumulation does not predict potency in mycobacteria may be another over-generalization based on the limited number of drugs and species studied, but perhaps the intended assertion was that antibiotic accumulation ALONE does not predict potency.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors were trying to establish whether competition between the RNA-binding proteins SF1 and QKI controlled splicing outcomes. These two proteins have similar binding sites and protein sequences, but SF1 lacks a dimerization motif and seems to bind a single version of the binding sequence. Importantly, these binding sequences correspond to branchpoint consensus sequences, with SF1 binding leading to productive splicing, but QKI binding leading instead to association with paraspeckle proteins. They show that in human cells SF1 generally activates exons and QKI represses, and a large group of the jointly regulated exons (43% of joint targets) are reciprocally controlled by SF1 and QKI. They focus on one of these exons RAI14 that shows this reciprocal pattern of regulation, and has 2 repeats of the binding site that make it a candidate for joint regulation, and confirm regulation within a minigene context. The authors used the assembly of proteins within nuclear extracts to explain the effect of QKI versus SF1 binding. Finally, the authors show that the expression of QKI is lethal in yeast, and causes splicing defects.

How this fits in the field. This study is interesting and provides a conceptual advance by providing a general rule on how SF1 and QKI interact in relation to binding sites, and the relative molecular fates followed, so is very useful. Most of the analysis seems to focus on one example, although the molecular analysis and global work significantly add to the picture from the previously published paper about NUMB joint regulation by QKI and SF (Zong et al, cited in text as reference 50, that looked at SF1 and QKI binding in relation to a duplicated binding site/branchpoint sequence in NUMB).

Strengths:

The data presented are strong and clear. The ideas discussed in this paper are of wide interest, and present a simple model where two binding sites generate a potentially repressive QKI response, whereas exons that have a single upstream sequence are just regulated by SF1. The assembly of splicing complexes on RNAs derived from RAI14 in nuclear extracts, followed by mass spec gave interesting mechanistic insight into what was occurring as a result of QKI versus SF1 binding.

Weaknesses:

I did not think the title best summarises the take-home message and could be perhaps a bit more modest. Although the authors investigated splicing patterns in yeast and human cells, yeast do not have QKI so there is no ancient competition in that case, and the study did not really investigate physiological or evolutionary outcomes in splicing, although it provides interesting speculation on them. Also as I understood it, the important issue was less conserved branchpoints in higher eukaryotes enabling alternative splicing, rather than competition for the conserved branchpoint sequence. So despite the the data being strong and properly analysed and discussed in the paper, could the authors think whether they fit best with the take-home message provided in the title? Just as a suggestion (I am sure the authors can do a better job), maybe "molecular competition between variant branchpoint sequences predict physiological and evolutionary outcomes in splicing"?

Although the authors do provide some global data, most of the detailed analysis is of RAI14. It would have been useful to examine members of the other quadrants in Figure 1C as well for potential binding sites to give a reason why these are not co-regulated in the same way as RAI14. How many of the RAI14 quadrants had single/double sites (the motif analysis seemed to pull out just one), and could one of the non-reciprocally regulated exons be moved into a different quadrant by addition or subtraction of a binding site or changing the branchpoint (using a minigene approach for example).

Reviewer #3 (Public review):

Summary:

In this study, the authors set out to investigate whether and how Shigella avoids cell-autonomous immunity initiated through M1-linked ubiquitin and the immune sensor and E3 ligase RNF213. The key findings are that the Shigella flexneri T3SS effector, IpaH1.4 induces degradation of RNF213. Without IpaH1.4, the bacteria are marked with RNF213 and ubiquitin following stimulation with IFNg. Interestingly, this is not sufficient to initiate the destruction of the bacteria, leading the authors to conclude that Shigella deploys additional virulence factors to avoid this host immune response. The second key finding of this paper is the suggestion that M1 chains decorate the mxiE/ipaH Shigella mutant independent of LUBAC, which is, by and large, considered the only enzyme capable of generating M1-linked ubiquitin chains.

Strengths:

The data is for the most part well controlled and clearly presented with appropriate methodology. The authors convincingly demonstrate that IpaH1.4 is the effector responsible for the degradation of RNF213 via the proteasome, although the site of modification is not identified.

Weaknesses:

The work builds on prior work from the same laboratory that suggests that M1 ubiquitin chains can be formed independently of LUBAC (in the prior publication this related to Chlamydia inclusions). In this study, two pieces of evidence support this statement -fluorescence microscopy-based images and accompanying quantification in Hoip and Hoil knockout cells for association of M1-ub, using an antibody, to Shigella mutants and the use of an internally tagged Ub-K7R mutant, which is unable to be incorporated into ubiquitin chains via its lysine residues. Given that clones of the M1-specific antibody are not always specific for M1 chains, and because it remains formally possible that the Int-K7R Ub can be added to the end of the chain as a chain terminator or as mono-ub, the authors should strengthen these findings relating to the claim that another E3 ligase can generate M1 chains de novo.

The main weakness relating to the infection work is that no bacterial protein loading control is assayed in the western blots of infected cells, leaving the reader unable to determine if changes in RNF213 protein levels are the result of the absent bacterial protein (e.g. IpaH1.4) or altered infection levels.

The importance of IFNgamma priming for RNF213 association to the mxiE or ipaH1.4 strain could have been investigated further as it is unclear if RNF213 coating is enhanced due to increased protein expression of RNF213 or another factor. This is of interest as IFNgamma priming does not seem to be needed for RNF213 to detect and coat cytosolic Salmonella.

Overall, the findings are important for the host-pathogen field, cell-autonomous/innate immune signaling fields, and microbial pathogenesis fields. If further evidence for LUBAC independent M1 ubiquitylation is achieved this would represent a significant finding.

Reviewer #3 - Public Review

Summary:

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

Strengths:

The authors confirmed that coordinated Ca2+ oscillations are important for glycemic control. In addition, they definitively disproved the role of individual privileged cells, which were suggested to lead or coordinate Ca²⁺ oscillations. They provided evidence for differential regional stability, confirming the previously described stochastic nature of the beta cells that act as strongly connected hubs as well as beta cells in initiating regions (doi.org/10.1103/PhysRevLett.127.168101).

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

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

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

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

Some issues concerning inconsistencies between data presented and statements made as well as statistical analysis need to be addressed.

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

Reviewer #3 (Public review):

This study presents a detailed examination of the molecular and cellular organization of the mouse VNO, unveiling new cell types, receptor co-expression patterns, lineage specification regulation, and potential associations between transcription factors, guidance molecules, and receptor types crucial for vomeronasal circuitry wiring specificity. The study identifies a novel type of VSN molecularly different from classic VSNs, which may serve as accessory to other VSNs by secreting olfactory binding proteins and mucins in response to VNO activation. They also describe a previously undetected co-expression of multiple VRs in individual VSNs, providing an interesting view to the ongoing discussion on how receptor choice occurs in VSNs, either stochastic or deterministic. Finally, the study correlates the expression of axon guidance molecules associated with individual VRs, providing a putative molecular mechanism that specifies VSN axon projections and their connection with postsynaptic cells in the accessory olfactory bulb.

The conclusions of this paper are well supported by data, but some aspects of data analysis and acquisition need to be clarified and extended.

(1) The authors claim that they have identified two new classes of sensory neurons, one being a class of canonical olfactory sensory neurons (OSNs) within the VNO. This classification as canonical OSNs is based on expression data of neurons lacking the V1R or V2R markers but instead expressing ORs and signal transduction molecules, such as Gnal and Cnga2. Since OR-expressing neurons in the VNO have been previously described in many studies, it remains unclear to me why these OR-expressing cells are considered here a "new class of OSNs." Moreover, morphological features, including the presence of cilia, and functional data demonstrating the recognition of chemosignals by these neurons, are still lacking to classify these cells as OSNs akin to those present in the MOE. While these cells do express canonical markers of OSNs, they also appear to express other VSN-typical markers, such as Gnao1 and Gnai2 (Fig 2B), which are less commonly expressed by OSNs in the MOE. Therefore, it would be more precise to characterize this population as atypical VSNs that express ORs, rather than canonical OSNs.

(2) The second new class of sensory neurons identified corresponds to a group of VSNs expressing prototypical VSN markers (including V1Rs, V2Rs, and ORs), but exhibiting lower ribosomal gene expression. Clustering analysis reveals that this cell group is relatively isolated from V1R- and V2R-expressing clusters, particularly those comprising immature VSNs. The question then arises: where do these cells originate? Considering their fewer overall genes and lower total counts compared to mature VSNs, I wonder if these cells might represent regular VSNs in a later developmental stage, i.e., senescent VSNs. While the secretory cell hypothesis is compelling and supported by solid data, it could also align with a late developmental stage scenario. Further data supporting or excluding these hypotheses would aid in understanding the nature of this new cell cluster, with a comparison between juvenile and adult subjects appearing particularly relevant in this context.

(3) The authors' decision not to segregate the samples according to sex is understandable, especially considering previous bulk transcriptomic and functional studies supporting this approach. However, many of the highly expressed VR genes identified have been implicated in detecting sex-specific pheromones and triggering dimorphic behavior. It would be intriguing to investigate whether this lack of sex differences in VR expression persists at the single-cell level. Regardless of the outcome, understanding the presence or absence of major dimorphic changes would hold broad interest in the chemosensory field, offering insights into the regulation of dimorphic pheromone-induced behavior. Additionally, it could provide further support for proposed mechanisms of VR receptor choice in VSNs.

(4) The expression analysis of VRs and ORs seems to have been restricted to the cell clusters associated to the neuronal lineage. Are VRs/ORs expressed in other cell types, i.e. sustentacular, HBC or other cells?

Review update:

I believe the novel discovery of two classes of sensory neurons within the VNO-canonical olfactory sensory neurons (OSNs) and secretory vomeronasal sensory neurons (sVSNs)-should be interpreted with caution. Firstly, these cell types are relatively rare, constituting less than 2% of total cells and only 2-6% of the neuronal population (according to Fig. S3). While the OSNs exhibit gene expression profiles consistent with canonical olfactory signal transduction and cilia-related gene ontology, key aspects such as their cell morphology (including the presence of cilia) and functional evidence for chemosignal detection have yet to be demonstrated. The neuronal lineage of sVSNs remains unclear to me. It is uncertain what developmental trajectories these cells follow: do they arise as a specialized subtype of V1R or V2R lineages, or do they have an independent lineage determination, similar to OSNs? At what stage does the commitment to the sVSN lineage begin-during the INP stage or the immature sensory neuron stage? A pseudotime inference analysis of sVSNs could help clarify these questions.

Reviewer #3 (Public review):

Summary:

The cell wall of human fungal pathogens, such as Candida albicans, is crucial for structural support and modulating the host immune response. Although extensively studied in yeasts and molds, the structural composition has largely focused on the structural glucan b,1,3-glucan and the surface exposed mannans, while the fibrillar component β-1,6-glucan, a significant component of the well wall, has been largely overlooked. This comprehensive biochemical and immunological study by a highly experienced cell wall group provides a strong case for the importance of β-1,6-glucan contributing critically to cell wall integrity, filamentous growth, and cell wall stability resulting from defects in mannan elongation. Additionally, β-1,6-glucan responds to environmental stimuli and stresses, playing a key role in wall remodeling and immune response modulation, making it a potential critical factor for host-pathogen interactions.

Strengths:

Overall, this study is well designed and executed. It provides the first comprehensive assessment of β-1,6-glucan as a dynamic, albeit underappreciated, molecule. The role of β-1,6-glucan genetics and biochemistry has been explored in molds like Aspergillus fumigatus, but this work shines important light on its role in Candida albicans. This is important work that is of value to Medical Mycology, since β-1,6-glucan plays more than just a structural role in the wall. It may serve as a PAMP and a potential modulator of host-pathogen interactions.

Weaknesses:

In keeping with an important role in immune recognition, it was suggested that the manuscript rigor would benefit from a more physiological evaluation ex vivo and preferably in vivo, assessment on stimulating the immune system within in the cell wall and not just as a purified component. This is a critical outcome measure for this study and gets squarely at its importance for host-pathogen interactions, especially in response to environmental stimuli and drug exposure. The authors addressed this issue contextually and indicate that it will require a more detailed immunologic evaluation but is not in keeping with the intent of this foundational study.

Reviewer #3 (Public review):

Summary:

Understanding the molecular regulation of muscle stem cell quiescence. The authors evaluated the role of the MuSK-BMP pathway in regulating adult SC quiescence by the deletion of the BMP-binding MuSK Ig3 domain ('ΔIg3-MuSK').

Strengths:

A novel mouse model to interrogate muscle stem cell molecular regulators. The authors have developed a nice mouse model to interrogate the role of MuSK signaling in muscle stem cells and myofibers and have unique tools to do this.

Weaknesses:

Only minor technical questions remain and there is a need for additional data to support the conclusions.

(1) The authors claim that dIg3-MuSK satellite cells break quiescence and start fusing, based on the reduction of Pax7+ and increase of nuclei/fiber (Fig 2-3), and maybe the gene expression (Fig6). However, direct evidence is needed to support these findings such as quantifying quiescent (Pax7+Ki67-) or activated (Pax7+Ki67+) satellite cells (and maybe proliferating progenitors Pax7-Ki67+) in the dIg3-MuSK muscle.

(2) It is not clear if the MuSK-BMP pathway is required to maintain satellite cell quiescence, by the end of the regeneration (29dpi), how Pax7+ numbers are comparable to the WT (Fig4d). I would expect to have less Pax7+, as in uninjured muscle. Can the authors evaluate this in more detail?

(2) Figure 4 claims that regeneration is accelerated, but to claim this at a minimum they need to look at MYH3+ fibers, in addition to fiber size.

(3) The Pax7 specific dIg3-MuSK (Fig5) is very exciting. However, it will be important to quantify the Pax7+ number. Could the authors check the reduction of Pax7+ in this model since it would confirm the importance of MuSK in quiescence?

(3) Rescue of the BMP pathway in the model would be further supportive of the authors' findings.

(4) Is the stem cell pool maintained long term in the deleted dIg3-MuSK SCs? Or would they be lost with extended treatment since they are reduced at the 5-month experiments? This is an important point and should be considered/discussed relevant to thinking about these data therapeutically.

(5) Without the Pax7-specific targeting, when you target dIg3-MuSK in the entire muscle, what happens to the neuromuscular nuclei?

(6) Why were differences seen in males and not females? Is XIST downregulation occurring in both sexes? Could the authors explain these findings in more detail?

Reviewer #3 (Public review):

Summary:

In this manuscript by Mestre-Fos and colleagues, authors have analyzed the involvement of eIF3 binding to mRNA during differentiation of neural progenitor cells (NPC). The authors bring a lot of interesting observations leading to a novel function for eIF3 at the 3'UTR.

During the translational burst that occurs during NPC differentiation, analysis of eIF3-associated mRNA by Quick-irCLIP reveals the unexpected binding of this initiation factor at the 3'UTR of most mRNA. Further analysis of alternative polyadenylation by APAseq highlights the close proximity of the eIF3-crosslinking position and the poly(A) tail. Furthermore, this interaction is not detected in Poly(A)-less transcripts. Using Riboseq, the authors then attempted to correlate eIF3 binding with the translation efficacy of mRNA, which would suggest a common mechanism of translational control in these cells. These observations indicate that eIF3-binding at the 3'UTR of mRNA, near the poly(A) tail, may participate to the closed-loop model of mRNA translation, bridging 5' and 3', and allowing ribosomes recycling. However, authors failed to detect interactions of eIF3, with either PABP or Paip1 or 40S subunit proteins, which is quite unexpected.

Strength:

The well-written manuscript presents an attractive concept regarding the mechanism of eIF3 function at the 3'UTR. Most mRNA in NPC seems to have eIF3 binding at the 3'UTR and only a few at the 5'end where it's commonly thought to bind. In a previous study from the Cate lab, eIF3 was reported to bind to a small region of the 3'UTR of the TCRA and TCRB mRNA, which was responsible for their specific translational stimulation, during T cell activation. Surprisingly in this study, the eIF3 association with mRNA occurs near polyadenylation signals in NPC, independently of cell differentiation status. This compelling evidence suggests a general mechanism of translation control by eIF3 in NPC. This observation brings back the old concept of mRNA circularization with new arguments, independent of PABP and eIF4G interaction. Finally, the discussion adequately describes the potential technical limitations of the present study compared to previous ones by the same group, due to the use of Quick-irCLIP as opposed to the PAR-CLIP/thiouridine.

Weaknesses:

(1) These data were obtained from an unusual cell type, limiting the generalizability of the model.

(2) This study lacks a clear explanation for the increased translation associated with NPC differentiation, as eIF3 binding is observed in both differentiated and undifferentiated NPC. For example, I find a kind of inconsistency between changes in Riboseq density (Figure 3B) and changes in protein synthesis (Figure 1D). Thus, the title overstates a modest correlation between eIF3 binding and important changes in protein synthesis.

(3) This is illustrated by the candidate selection that supports this demonstration. Looking at Figure 3B, ID2, and SNAT2 mRNA are not part of the High TE transcripts (in red). In contrast, the increase in mRNA abundance could explain a proportionally increased association with eIF3 as well as with ribosomes. The example of increased protein abundance of these best candidates is overall weak and uncertain.

(4) Despite several attempts (chemical and UV cross-linking) to identify eIF3 partners in NPC such as PABP, PAIP1, or proteins from the 40S, the authors could not provide any evidence for such a mechanism consistent with the closed-loop model. Overall, this rather descriptive study lacks mechanistic insight (eIF3 binding partners).

(5) Finally, the authors suspect a potential impact of technical improvement provided by Quick-irCLIP, that could have been addressed rather than discussed.

Reviewer #3 (Public review):

Summary:

The manuscript by Eggan et al provides insights into conformational transitions in the cyclic nucleotide binding domain of a cyclic nucleotide-gated (CNG) channel. The authors use transition metal FRET (tmFRET) which has been pioneered by this lab and previously led to detailed insights into ion channel conformational changes. Here, the authors not only use steady-state measurements but also time-resolved, fluorescence lifetime measurements to gain detailed insights into conformational transitions within a protein construct that contains the cytosolic C-linker and cyclic nucleotide binding domain (CNBD) of a bacterial CNG channel. The use of time-resolved tmFRET is a clear advancement of this technique and a strength of this manuscript.

In summary, the present work introduces time-resolved tmFRET as a novel tool to study conformational distributions in proteins. This is a clear technological advance. The limitations of the truncated construct used in this study and how they relate to the energetics in full-length CNG channels are discussed. It will be interesting to see in the future how results compare to similar measurements on full-length channels, for example, reconstituted into nanodiscs.

Strengths:

The results capture known differences in promoting the open state between different ligands (cAMP and cGMP) and are consistent across three donor-acceptor FRET pairs. The calculated distance distributions are further in agreement with predicted values based on available structures. The finding that the C-helix is conformationally more mobile in the closed state as compared to the open state quantitatively increases our understanding of conformational changes in these channels.

Weaknesses:

The results describe movements of the C-helix in CNBDs, but detailed energetics as calculated in this study, need to be limited to the truncated protein construct. This is a weakness that cannot be overcome easily as it will require future experiments using the full-length channel.

The data only describe movements of the C-helix. Upon ligand binding, the C-helix moves upwards to coordinate the ligand. Thus, the results are ligand-induced conformational changes (as the title states). Allosteric regulation usually involves remote locations in the protein, which is applicable only in a limited fashion here.

Reviewer #3 (Public review):

Summary:

The manuscript by Rios-Jimenez developed a computational tool, BEHAV3D Tumor Profiler, to analyze intravital imaging data and extract distinctive tumor cell migratory phenotypes based on the quantified 3D image data.

Weaknesses:

(1) The most challenging task of analyzing 3D time-lapse imaging data is to accurately segment and track the individual cells in 3D over a long time duration. BEHAV3D Tumor Profiler did not provide any new advancement in this regard, and instead relies on commercial software, Imaris, for this critical step. Imaris is known to have a very high error rate when used for analyzing 3D time-lapse data. In the Methods section, the authors themselves stated that "Tumor cell tracks were manually corrected to ensure accurate tracking". Based on our own experience of using Imaris, such manual correction is tedious and often required for every time step of the movie. Therefore, Imaris is not a satisfactory tool for analyzing 3D time-lapse data. Moreover, Imaris is expensive and many research labs probably can't afford to buy it. The fact that BEHAV3D Tumor Profiler critically depends on the faulty ImarisTrack module makes it unclear whether the BEHAV3D tool or the results are reliable.

(2) The authors developed a "Heterogeneity module" to extract distinctive tumor migratory phenotypes from the cell tracks quantified by Imaris. The cell tracks of the individual tumor cells are all quite short, indicating relatively low motility of the tumor cells. It's unclear whether such short migratory tracks are sufficient to warrant the PCA analysis to identify the 7 distinctive migratory phenotypes shown in Figure 2d. It's also unclear whether these 7 migratory phenotypes correspond to unique functional phenotypes.

(3) Using only motility to classify tumor cell behaviours in the tumor microenvironment (TME) is probably not sufficient to capture the tumor cell difference. There are also other non-tumor cell types in the TME. If the authors aim to develop a computational tool that can elucidate tumor cell behaviors in the TME, they should consider other tumor cell features, e.g., morphology, proliferation state, and tumor cell interaction with other cell types, e.g., fibroblasts and distinct immune cells.

(4) The authors have already published two papers on BEHAV3D [Alieva M et al. Nat Protoc. 2024 Jul;19(7): 2052-2084; Dekkers JF, et al. Nat Biotechnol. 2023 Jan;41(1):60-69]. Although the previous two papers used BEHAV3D to analyze T cells, the basic pipeline and computational steps are similar, in particular regarding cell segmentation and tracking. The addition of a "Heterogeneity module" based on PCA analysis does not make a significant advancement in terms of image analysis and quantification.

Reviewer #3 (Public review):

Summary:

The manuscript by Zhao et al. explored the function of adhesion G protein-coupled receptor A3 (ADGRA3) in thermogenic fat biology.

Strengths:

Through both in vivo and in vitro studies, the authors found that the gain function of ADGRA3 leads to browning of white fat and ameliorates insulin resistance.

Comments on revised version:

The revised manuscript by Zhao et al. has limited improvement. The authors refused to perform revised experiments using primary cultures even though two reviewers pointed out the same weakness (3T3-L1 adipocytes are unsuitable). Using infrared thermography to measure body temperature is also problematic.

Reviewer #3 (Public review):

Summary:

REV7 facilitates the recruitment of Shieldin complex and thereby inhibits end resection and controls DSB repair choice in metazoan cells. Puzzlingly, Shieldin is absent in many organisms, and it is unknown if and how Rev7 regulates DSB repair in these cells. The authors surmised that yeast Rev7 physically interacts with Mre11/Rad50/Xrs2 (MRX), the short-range resection nuclease complex and tested this premise using yeast two hybrid (Y2H) and microscale thermophoresis (MST). The results convincingly showed that the individual subunits of MRX interacts robustly with Rev7. By AlphaFold Multimer modelling followed by Y2H confirmed that the carboxy terminal 42 amino acid is essential for interaction with MR and G4 DNA binding by REV7. The mutant rev7 lacking the binding interface (Rev7-C1) to MR shows moderate inhibition to the nuclease and the ATPase activity of Mre11/Rad50 in biochemical assays. Deletion of REV7 also causes a mild reduction in NHEJ using both plasmid and chromosome-based assays and increases mitotic recombination between chromosomal ura3-01 and the plasmid ura3 allele interrupted by G4. The revision also showed that rev7 deleted cells exhibit mild hyper-resection phenotype at 0.7 and 3 kb from the DSB using qPCR assays. The authors concluded that Rev7 facilitates NHEJ and antagonises HR even in budding yeast, but it achieves this by blocking Mre11 nuclease and Rad50 ATPase.

Weaknesses:

There are several strengths to the studies and the broad types of well-established assays were used to deduce the conclusion. Nevertheless, there are notable discrepancies on the mutant phenotypes that were to test the functionality of Rev7-MRX interaction on the repair outcomes, raising concerns on the validity of the proposed model. The manuscript also needs a few additional functional assays to reach the accurate conclusions as proposed. The revision responded to several comments raised by the reviewers, but they are inadequate to address the key concerns and did not offer sufficient and compelling experimental support to the main premise that Rev7-Mre11/Rad50/Xrs2 interactions regulate MRX activities in cells and thereby modulates DSB repair choice in budding yeast.

(1) AlphaFold model predicts that Mre11-Rev7 and Rad50-Rev7 binding interfaces overlap and Rev7 might bind only to Mre11 or Rad50 at a time. Interestingly, however, Rev7 appears dimerized (Fig.1). Since MR complex also forms with 2M and 2R in the complex, it should still be possible if REV7 can interact both M and R in the MR complex. The author should perform MST using MR complex instead of individual MR components. The authors should also analyze if Rev7-C1 is indeed deficient in interaction with MR individually and with complex using MST assay.

(2) The nuclease and the ATPase assays require additional controls. Does Rev7 inhibit the other nuclease or ATPase non-specifically? Are these outcomes due to the non-specific or promiscuous activity of Rev7? In fig.6, the effect of REV7 on the ATP binding of Rad50 could be hard to assess because the maximum Rad50 level (1 uM) was used in the experiments. The author should use the suboptimal level of Rad50 to check if REV7 still does not influence ATP binding by Rad50.

(3) The moderate deficiency in NHEJ using plasmid based assay in REV7 deleted cells can be attributed to aberrant cell cycle or mating type in rev7 deleted cells. The authors should demonstrate that rev7 deleted cells retain largely normal cell cycle pattern and the mating type phenotypes. The author should also analyze the breakpoints in plasmid based NHEJ assays in all mutants especially from rev7 and rev7-C1 cells.

(4) It is puzzling why the authors did not analyze end resection defects in rev7 deleted cells after a DSB. The author should employ the widely used resection assay after a HO break in rev3, rev7 and mre11 rev7 cells as described previously.

(5) Is it possible that Rev7 also contributes to NHEJ as the part of TLS polymerase complex? Although NHEJ largely depends on Pol4, the authors should not rule out the possibility if the observed NHEJ defect in rev7 cells are due at least partially to its well-known TLS defect and not all due to their role in MRX activity regulation as the authors proposed. In fact, rev3 or rev1 cells are partially defective in NHEJ (Fig. 7). Rev7-C1 is less deficient in NHEJ than REV7 deletion. These results predict that rev7-C1 rev3 could be more deficient than rev3 or rev7-C1, and such results might indicate that Rev7 contributes to NHEJ by two ways; one by interacting (and modulating) MRX and the other as part of Rev3-Rev7 complex. Additionally, the authors should examine if Rev7-C1 might be deficient in TLS. In this regard, does rev7-C1 reduce TLS and TLS dependent mutagenesis? Is it dominant? The authors should also check if Rev3/Rev1 complexes are stable in Rev7 deleted or rev7-C1 cells by immunoblot assays.

(6) Due to the G4 DNA and G4 binding activity of REV7, it is not clear which class of events the authors are measuring in plasmid-chromosome recombination assay in Fig.9. Do they measure G4 instability or the integrity of recombination or both in rev7 deleted cells. Instead, the effect of rev7 deletion or rev7-C1 on recombination should be measured directly by more standard mitotic recombination assays like mating type switch or his3 repeat recombination. The revision did not address these concerns, which still makes the interpretation of the provided recombination results difficult.

Reviewer #3 (Public review):

Papalamprou et al sought to fine tune existing tenogenic differentiation protocols to develop a robust multi-step differentiation protocol to induce tendon cells from human GMP-ready iPSCs. In so doing, they found that while existing protocols are capable of driving cells towards a syndetome-like fate, the resultant cultures contain highly heterogeneous cell populations with sub-optimal cell survival. Through single cell transcriptomic analysis they identify WNT signaling as a potential driver of an off-target neural population and show that inhibition of WNT signaling at the later 2 stages of differentiation can be used to promote higher efficiency of generation of syndetome-like cells.

This paper includes a useful paradigm for identifying transcriptional modulators of cell fate during differentiation and a clear example where transcriptional data can be used to guide the chemical modulation of a differentiation protocol to improve cell output. The paper's conclusions are mostly well supported by the data, but the image analysis and discussion need to be improved to strengthen the impact.

The data outlining the differences between the differentiation outcome of the two tested iPSCs is intriguing, but the authors fail to comment on potential differences between the two iPSC lines that could result in drastically different cell outputs from the same differentiation protocol. This is a critically important point, as the majority of the SCX+ cells generated from the 007i cells using their WNTi protocol were found in the FC subpopulation that failed to form from the 83i line under the same protocol. From the analysis of only these 2 cells lines in vitro, it is difficult to assess whether this WNTi protocol can be broadly used across multiple cell lines to generate tenogenic cells. The authors failed to update the text of the manuscript to reflect the potential differences in the two cell lines and the general applicability of their protocol, but rather just include the description of the proposed explanation in the response to reviewer comments. These critical differences in the response to their protocol and their implications for the applications of this proof-of-concept study should be included in the main text.

The authors make claims about changes in protein expression but fail to quantify either fluorescence intensity or percent cell expression from their immunofluorescence analyses to substantiate these claims. The authors state in their response to reviewers that immunofluorescence is qualitative but continue to make quantitative statements such as upregulated or downregulated in both the text and legend describing these images. The authors should either perform the quantification of the IFs, use Western blots for protein quantification of their cell cultures, use Flow Cytometry to count cell numbers, or remove these quantitative words from the description of the images. The image quality and staining specificity continue to be a limitation of this study. These claims are not fully supported by the data as presented as it is unclear whether there is increased expression of tendon markers at the protein level or more cells surviving the protocol.

Reviewer #4 (Public review):

Summary:

In this elegant study XX and colleagues use a combination of fixed tissue analyses and live imaging to characterise the role of Laminin in olfactory placode development and neuronal pathfinding in the zebrafish embryo. They describe Laminin dynamics in the developing olfactory placode and adjacent brain structures and identify potential roles for Laminin in facilitating neuronal pathfinding from the olfactory placode to the brain. To test whether Laminin is required for olfactory placode neuronal pathfinding they analyse olfactory system development in a well-established laminin-gamma-1 mutant, in which the laminin-rich basement membrane is disrupted. They show that while the OP still coalesces in the absence of Laminin, Laminin is required to contain OP cells during forebrain flexure during development and maintain separation of the OP and adjacent brain region. They further demonstrate that Laminin is required for growth of OP neurons from the OP-brain interface towards the olfactory bulb. The authors also present data describing that while the Laminin mutant has partial defects in neural crest cell migration towards the developing OP, these NCC defects are unlikely to be the cause of the neuronal pathfinding defects upon loss of Laminin. Altogether the study is extremely well carried out, with careful analysis of high-quality data. Their findings are likely to be of interest to those working on olfactory system development, or with an interest in extracellular matrix in organ morphogenesis, cell migration, and axonal pathfinding.

Strengths:

The authors describe for the first time Laminin dynamics during the early development of the olfactory placode and olfactory axon extension. They use an appropriate model to perturb the system (lamc1 zebrafish mutant), and demonstrate novel requirements for Laminin in pathfinding of OP neurons towards the olfactory bulb.<br /> The study utilises careful and impressive live imaging to draw most of its conclusions, really drawing upon the strengths of the zebrafish model to investigate the role of laminin in OP pathfinding. This imaging is combined with deep learning methodology to characterise and describe phenotypes in their Laminin-perturbed models, along with detailed quantifications of cell behaviours, together providing a relatively complete picture of the impact of loss of Laminin on OP development.

Weaknesses:

Some of the statistical tests are performed on experiments where n=2 for each condition (for example the measurements in Figure S2) - in places the data is non-significant, but clear trends are observed, and one wonders whether some experiments are under-powered.

Reviewer #3 (Public review):

Summary:

Varani et al present important findings regarding the role of distinct cerebellothalamic connections in motor learning and performance. Their key findings are that:<br /> (1) cerebellothalamic connections are important for learning motor skills<br /> (2) cerebellar efferents specifically to the central lateral (CL) thalamus are important for short-term learning<br /> (3) cerebellar efferents specifically to the ventral anterior lateral (VAL) complex are important for offline consolidation of learned skills, and<br /> (4) that once a skill is acquired, cerebellothalamic connections become important for online task performance.

The authors went to great lengths to separate effects on motor performance from learning, for the most part successfully. While one could argue about some of the specifics, there is little doubt that the CN-CL and CN-VAL pathways play distinct roles in motor learning and performance. An important next step will be to dissect the downstream mechanisms by which these cerebellothalamic pathways mediate motor learning and adaptation.

Strengths:

(1) The dissociation between online learning through CN-CL and offline consolidation through CN-VAL is convincing.

(2) The ability to tease learning apart from performance using their titrated chemogenetic approach is impressive. In particular, their use of multiple motor assays to demonstrate preserved motor function and balance is an important control.

(3) The evidence supporting the main claims is convincing, with multiple replications of the findings and appropriate controls.

Weaknesses:

(1) Despite the care the authors took to demonstrate that their chemogenetic approach does not impair online performance, there is a trend towards impaired rotarod performance at higher speeds in Supplementary Figure 4f, suggesting that there could be subtle changes in motor performance below the level of detection of their assays.

(2) There is likely some overlap between CN neurons projecting to VAL and CL, somewhat limiting the specificity of their conclusions.

Reviewer #3 (Public review):

Summary:

In their manuscript entitled "Parallel mechanisms signal a hierarchy of sequence structure violations in the auditory cortex", Jamali et al. provide evidence for cellular-level mechanisms in the auditory cortex of mice for the encoding of predictive information on different temporal and contextual scales. The study design separates more clearly than previous studies between the effects of local and global deviants and separates their respective effects on the neuronal responses clearly through the use of various contextual conditions and short and long time scales. Further, it identifies a contribution from a small set of VIP interneurons to the detection of omitted sounds, and shows the influence of isofluorane anesthesia on the neural responses.

Strengths:

(1) The study provides a rather encompassing set of experimental techniques to study the cellular level responses, using two complementary recording techniques in the same animal and similar cortical location.

(2) Comparison between awake and anesthetized states are conducted in the same animals, which allows for rather a direct comparison of populations under different conditions, thus reducing sampling variability.

(3) The set of paradigms is well developed and specifically chosen to provide appropriate and meaningful controls/comparisons, which were missing from previous studies.

(4) The addition of cell-type specific recordings is valuable and in particular in combination with the contrast of awake and anesthetized animals provides novel insights into the cellular level representation of deviant signals, such as surprise, prediction error, and general adaptation.

(5) The analysis and presentation of the data are clear and quite complete, yet remain succinct and perform insightful contrasts.

(6) The study will have an impact on multiple levels, as it introduces important variations in the paradigm and analytical contrasts that both human and animal researchers can pick up and improve their studies. The cell-type-specific results are particularly intriguing, although these would likely require replication before being completely reliable. Further, the study provides a substantial and diverse dataset that others can explore.

Weaknesses:

(1) The responses from cells recorded via Neuropixel and 2p differ qualitatively, as noted by the authors, with NP-recorded cells showing much more inhibited/reduced responses between acoustic stimulations. The authors briefly qualify these differences as potentially indicating a sampling issue, however, this matter deserves more detailed consideration in my opinion. Specifically, the authors could try to compare the different depths at which these neurons were sampled or relate the locations in the cortex to each other (as the Neuropixel recordings were collected in the same animals, a subset of the 2p recordings could be compared to the Neuropixel recordings.).

(2) The current study did not monitor the attentional state of the mouse in relation to the stimulus by either including a behavioral component or pupil monitoring, which could influence the neural responses to deviant stimuli and omissions. .

(3) Given the complexity and variety of the paradigms, conditions, and analyzed cell-types, the manuscript could profit from a more visual summary figure that provides an easy-to-access overview of what was found.

Reviewer #3 (Public Review):

Summary:

Previous research on the Drosophila mushroom body (MB) has made this structure the best-understood example of an associative memory center in the animal kingdom. This is in no small part due to the generation of cell-type specific driver lines that have allowed consistent and reproducible genetic access to many of the MB's component neurons. The manuscript by Shuai et al. now vastly extends the number of driver lines available to researchers interested in studying learning and memory circuits in the fly. It is an 800-plus collection of new cell-type specific drivers target neurons that either provide input (direct or indirect) to MB neurons or that receive output from them. Many of the new drivers target neurons in sensory pathways that convey conditioned and unconditioned stimuli to the MB. Most drivers are exquisitely selective, and researchers will benefit from the fact that whenever possible, the authors have identified the targeted cell types within the Drosophila connectome. Driver expression patterns are beautifully documented and are publicly available through the Janelia Research Campus's Flylight database where full imaging results can be accessed. Overall, the manuscript significantly augments the number of cell type-specific driver lines available to the Drosophila research community for investigating the cellular mechanisms underlying learning and memory in the fly. Many of the lines will also be useful in dissecting the function of the neural circuits that mediate sensorimotor circuits.

Strengths:

The manuscript represents a huge amount of careful work and leverages numerous important developments from the last several years. These include the thousands of recently generated split-Gal4 lines at Janelia and the computational tools for pairing them to make exquisitely specific targeting reagents. In addition, the manuscript takes full advantage of the recently released Drosophila connectomes. Driver expression patterns are beautifully illustrated side-by-side with corresponding skeletonized neurons reconstructed by EM. A comprehensive table of the new lines, their split-Gal4 components, their neuronal targets, and other valuable information will make this collection eminently useful to end-users. In addition to the anatomical characterization, the manuscript also illustrates the functional utility of the new lines in optogenetic experiments. In one example, the authors identify a specific subset of sugar reward neurons that robustly promotes associative learning.

Comments on revised version:

Overall, I thought the authors addressed my comments well with the possible exception of what is actually new here. This was the most important thing that I thought should be included in the revision. Although the authors rewrote the paragraph describing the lines presented in the paper, I still can't tell exactly which ones haven't been previously published. Their revised paragraph says that 40 lines have been "previously used," but Supplemental Table 1 shows references for over 200 of the lines, which sounds more reasonable based on papers that have come out.

Also, in the revised paragraph they state that "All transgenic lines newly generated in this study are listed in Supplementary File 2" but that table lists only the 36 LexA hemidriver lines! Confusingly, this comment cites the same 8 references as are cited for the 40 line that they say were previously published. I am thus only more confused about how many previously uncharacterized lines are presented in this paper.

Further clarification would be helpful. On the one hand, I think this paper is a very nice summary of a ton of work and brings it all under one umbrella in a way that will be useful for many in the field. In that sense, the manuscript is worth publishing simply as a useful resource even if all the lines were previously published. On the other hand, it would be useful for readers to know which lines were previously characterized in other publications and which ones were not. This information may or may not be in Supplementary Tables 1 and 2 (but I can't tell).

Reviewer #3 (Public review):

Public review:

The claustrum is one of the most enigmatic regions of the cerebral cortex, with a potential role in consciousness and integrating multisensory information. Despite extensive connections with almost all cortical areas, its functions and mechanisms are not well understood. In an attempt to unravel these complexities, Shelton et al. employed advanced circuit mapping technologies to examine specific neurons within the claustrum. They focused on how these neurons integrate incoming information and manage the output. Their findings suggest that claustrum neurons selectively communicate based on cortical projection targets and that their responsiveness to cortical inputs varies by cell type.

Imaging studies demonstrated that claustrum axons respond to both single and multiple sensory stimuli. Extended inhibition of the claustrum significantly reduced animals' responsiveness to multisensory stimuli, highlighting its critical role as an integrative hub in the cortex.

However, the study's conclusions at times rely on assumptions that may undermine their validity. For instance, the comparison between RSC projecting and non-RSC projecting neurons is problematic due to potential false negatives in the cell labeling process, which might not capture the entire neuron population projecting to a brain area. This issue casts doubt on the findings related to neuron interconnectivity and projections, suggesting that the results should be interpreted with caution. The study's approach to defining neuron types based on projection could benefit from a more critical evaluation or a broader methodological perspective.

Nevertheless, the study sets the stage for many promising future research directions. Future work could particularly focus on exploring the functional and molecular differences between E1 and E2 neurons and further assess the implications of the distinct responses of excitatory and inhibitory claustrum neurons for internal computations. Additionally, adopting a different behavioral paradigm that more directly tests the integration of sensory information for purposeful behavior could also prove valuable.

Reviewer #3 (Public review):

Summary:

The authors conducted a well-designed experiment, incorporating VR classroom scenes and background sound events, with both control and ADHD participants. They employed multiple neurophysiological measures, such as EEG, eye movements, and skin conductance, to investigate the mechanistic underpinnings of paying attention in class and the disruptive effects of background noise.

The results revealed that individuals with ADHD exhibited heightened sensory responses to irrelevant sounds and reduced tracking of the teacher's speech. Overall, this manuscript presented an ecologically valid paradigm for assessing neurophysiological responses in both control and ADHD groups. The analyses were comprehensive and clear, making the study potentially valuable for the application of detecting attentional deficits.

Strengths:

• The VR learning paradigm is well-designed and ecologically valid.

• The neurophysiological metrics and analyses are comprehensive, and two physiological markers are identified capable of diagnosing ADHD.

• This research provides a valuable dataset that could serve as a benchmark for future studies on attention deficits.

Weaknesses:

• Several results are null results, i.e., no significant differences were found between ADHD and control populations.

• Although the paradigm is well-designed and ecologically valid, the specific contributions or insights from the results remain unclear.

• Lack of information regarding code and data availability.

Reviewer #3 (Public review):

Coatl et al. investigated the mechanisms of synaptic plasticity of two important hippocampal synapses, the excitatory afferents from lateral and medial perforant pathways (LPP and MPP, respectively) of the entorhinal cortex (EC) connecting to granule cells of the hippocampal dentate gyrus (DG). They find that these two different EC-DG synaptic connections in mice show a presynaptically expressed form of long-term depression (LTD) requiring postsynaptic calcium, eCB synthesis, CB1R activation, astrocyte activity, and metabotropic glutamate receptor activation. Interestingly, LTD at MPP-GC synapses requires ionotropic NMDAR activation whereas LTD at LPP-GC synapse is NMDAR independent. Thus, they discovered two novel forms of t-LTD that require astrocytes at EC-GC synapses. Although plasticity of EC-DG granule cell (GC) synapses has been studied using classical protocols, These are the first analyses of the synaptic plasticity induced by spike timing dependent protocols at these synapses. Interestingly, the data also indicate that t-LTD at each type of synapse require different group I mGluRs, with LPP-GC synapses dependent on mGluR5 and MPP-GC t-LTD requiring mGluR1.

The authors performed a detailed analysis of the coefficient of variation of the EPSP slopes, miniature responses and different approaches (failure rate, PPRs, CV, and mEPSP frequency and amplitude analysis) they demonstrate a decrease in the probability of neurotransmitter release and a presynaptic locus for these two forms of LTD at both types of synapses. By using elegant electrophysiological experiments and taking the advantage of the conditional dominant-negative (dn) SNARE mice in which doxycycline administration blocks exocytosis and impairs vesicle release by astrocytes, they demonstrate that both LTD forms require the release of gliotransmitters from astrocytes. These data add in an interesting way to the ongoing discussion on whether LTD induced by STDP participates in refining synapses potentially weakening excitatory synapses under the control of different astrocytic networks. The conclusions of this paper are well supported by data.

Reviewer #3 (Public review):

Summary:

Marchand, Akinnola, et al. describe the use of the novel model to study BM regeneration. Here, they harvest intact femurs and subcutaneously graft them into recipient mice. Similar to standard BM regeneration models, there is a rapid decrease in cellularity followed by a gradual recovery over 5 months within the grafts. At 5 months, these grafts have robust HSC activity, similar to HSCs isolated from the host femur. They find that periosteum skeletal stem cells (p-SSCs) are the primary source of BM-MSCs within the grafted femur and that these cells are more resistant to the acute stress of grafting the femur.

Strengths:

This is an interesting manuscript that describes a novel model to study BM regeneration. The model has tremendous promise.

Weaknesses:

The authors claim that grafting intact femurs subcutaneously is a model of BM regeneration and can be used as a replacement for gold standard BM regeneration assays such as sublethal chemo/irradiation. However, there isn't enough explanation as to how this model is equivalent or superior to the traditional models. For instance, the authors claim that this model allows for the study of "BM regeneration in vivo in response to acute injury using genetic tools." This can and has been done numerous times with established, physiologically relevant BM regeneration models. The onus is on the authors to discuss or perform the necessary experiments to justify the use of this model. For example, standard BM regeneration models involve systemic damage that is akin to therapies that require BM regeneration. How is studying the current model that provides only an acute injury more relevant and useful than other models? As it stands, it seems as if the authors could have done all the experiments demonstrating the importance of these p-SSCs in the traditional myelosuppressive BM regeneration models to be more physiologically relevant. Along these lines, the use of a standard BM regeneration model (e.g., sublethal chemo/irradiation) as a critical control is missing and should be included. Even if the control doesn't demonstrate that p-SSCs can contribute to the BM-MSC during regeneration, it will still be important because it could be the justification for using the described model to specifically study p-SSCs' regulation of BM regeneration.

The authors perform some analysis that suggests that grafting a whole femur mimics BM regeneration, but there are many experiments missing from the manuscript that will be necessary to support the use of this model. To demonstrate that this new model mimics current BM regeneration models, the authors need to perform a careful examination of the early kinetics of hematopoietic recovery post-transplant. Complete blood counts should be performed on the grafts, focusing on white blood cells (particularly neutrophils), red blood cells, platelets, all critical indicators of BM regeneration. This analysis should be done at early time points that include weekly analysis for a minimum of 28 days following the graft. Additionally, understanding how and when the vasculature recovers is critical. This is particularly important because it is well-established that if there is a delay in vascular recovery, there is a delay in hematopoietic recovery. As mentioned above, a standard BM regeneration model should be used as a control.

The contribution of donor and host cells to the BM regeneration of the graft is interesting. Particularly, the chimerism of the vasculature. One can assume that for the graft to undergo BM regeneration, there needs to be the delivery of nutrients into the graft via the vasculature. The chimerism of the vascular network suggests that host endothelial cells anastomose with the graft. Host mice should have their vascular system labeled with a dye such as dextran to determine if anastomosis has occurred. If not, the authors need to explain how this graft survives up to 5 months. If anastomosis does occur, then it is very surprising that the hematopoietic system of the graft is not a chimera because this would essentially be a parabiosis model. This needs to be explained.

Most of the data presented for the resistance of p-SSCs to stress suggests DNA damage response. Do p-SSCs demonstrate a higher ability to resolve DNA damage? Do they accumulate less DNA damage? Staining for DNA damage foci or performing comet assays could be done to further define the mechanism of stress resistance properties of p-SSCs.

Given the importance of BM-MSCs in hematopoiesis and that the majority of the emerging BM-MSCs appear to be derived from p-SSCs, the authors should perform experiments to determine if p-SSC-derived BM-MSCs are critical regulators of BM regeneration. For example, the authors could test this by crossing the Postn-creER mice with iDTR mice to ablate these cells and see if recovery is inhibited or delayed. This should be done with the described periosteum-wrapped femur graft model as well as a control BM regeneration model. Demonstrating that the deletion of these cells affects BM regeneration in both models would further justify the physiological relevance and utility of the femur graft model.

Reviewer #3 (Public review):

In this study, Cao et al. explore the neural mechanisms by which chronic heat exposure induces negative valence and hyperarousal in mice, focusing on the role of the posterior paraventricular nucleus (pPVT) neurons that receive projections from the preoptic area (POA). The authors show that chronic heat exposure leads to heightened activity of the POA projection-receiving pPVT neurons, potentially contributing to behavioral changes such as increased anxiety level and reduced sociability, along with heightened startle responses. In addition, using electrophysiological methods, the authors suggest that increased membrane excitability of pPVT neurons may underlie these behavioral changes. The use of a variety of behavioral assays enhances the robustness of their claim. Moreover, while previous research on thermoregulation has predominantly focused on physiological responses to thermal stress, this study adds a unique and valuable perspective by exploring how thermal stress impacts affective states and behaviors, thereby broadening the field of thermoregulation. However, a few points warrant further consideration to enhance the clarity and impact of the findings.

(1) The authors claim that behavior changes induced by chronic heat exposure are mediated by the POA-pPVT circuit. However, it remains unclear whether these changes are unique to heat exposure or if this circuit represents a more general response to chronic stress. It would be valuable to include control experiments with other forms of chronic stress, such as chronic pain, social defeat, or restraint stress, to determine if the observed changes in the POA-pPVT circuit are indeed specific to thermal stress or indicative of a more universal stress response mechanism.

(2) The authors use the term "negative emotion and hyperarousal" to interpret behavioral changes induced by chronic heat (consistently throughout the manuscript, including the title and lines 33-34). However, the term "emotion" is broad and inherently difficult to quantify, as it encompasses various factors, including both valence and arousal (Tye, 2018; Barrett, L. F. 1999; Schachter, S. 1962). Therefore, the reviewer suggests the authors use a more precise term to describe these behaviors, such as valence. Additionally, in lines 117 and 137-139, replacing "emotion" with "stress responses," a term that aligns more closely with the physiological observations, would provide greater specificity and clarity in interpreting the findings.

(3) Related to the role of POA input to pPVT,<br /> a) The authors showed increased activity in pPVT neurons that receive projections from the POA (Figure 3), and these neurons are necessary for heat-induced behavioral changes (Figures 4N-W). However, is the POA input to the pPVT circuit truly critical? Since recipient pPVT neurons can receive inputs from various brain regions, the reviewer suggests that experiments directly inhibiting the POA-to-pPVT projection itself are needed to confirm the role of POA input. Alternatively, the authors could show that the increased activity of pPVT neurons due to chronic heat exposure is not observed when the POA is blocked. If these experiments are not feasible, the reviewer suggests that the authors consider toning down the emphasis on the role of the POA throughout the manuscript and discuss this as a limitation.<br /> b) In the electrophysiology experiments shown in Figures 6A-I, the authors conducted in vitro slice recordings on pPVT neurons. However, the interpretation of these results (e.g., "The increase in presynaptic excitability of the POA to pPVT excitatory pathway suggested plastic changes induced by the chronic heat treatment.", lines 349-350) appears to be an overclaim. It is difficult to conclude that the increased excitability of pPVT neurons due to heat exposure is specifically caused by inputs from the POA. To clarify this, the reviewer suggests the authors conduct experiments targeting recipient neurons in the pPVT, with anterograde labeling from the POA to validate the source of excitatory inputs.

(4) The authors focus on the excitatory connection between the POA and pPVT (e.g., "Together, our results indicate that most of the pPVT-projecting POA neurons responded to heat treatment, which would then recruit their downstream neurons in the pPVT by exerting a net excitatory influence.", lines 169-171). However, are the POA neurons projecting to the pPVT indeed excitatory? This is surprising, considering i) the electrophysiological data shown in Figures 2E-K that inhibitory current was recorded in 52.4% of pPVT neurons by stimulation of POA terminal, and ii) POA projection neurons involved in modulating thermoregulatory responses to other brain regions are primarily GABAergic (Tan et al., 2016; Morrison and Nakamura, 2019). The reviewer suggests showing whether the heat-responsive POA neurons projecting to the pPVT are indeed excitatory (This could be achieved by retrogradely labeling POA neurons that project to the pPVT and conducting fluorescence in situ hybridization (FISH) assays against Slc32a1, Slc17a6, and Fos to label neurons activated by warmth). Alternatively, demonstrate, at least, that pPVT-projecting POA neurons are a distinct population from the GABAergic POA neurons that project to thermoregulatory regions such as DMH or rRPa. This would clarify how the POA-pPVT circuit integrates with the previously established thermoregulatory pathways.

Reviewer #3 (Public review):

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

Strengths:

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

Weaknesses:

This study is majorly based on sequencing data analysis. At the bench, they used a very strident technique to study fibroblast functions by ablating one of the major cell populations of the heart. Considering the importance of the fibroblast population, intriguing in vivo findings were expected. Also, they analyzed the downstream genes in ablated hearts, but did not execute any experimental validation for any of the targets.

Reviewer #3 (Public review):

Summary:

Ecker et al. utilized a biologically realistic, large-scale cortical model of the rat's non-barrel somatosensory cortex, incorporating a calcium-dependent plasticity rule to examine how various factors influence synaptic plasticity under in vivo-like conditions. Their analysis characterized the resulting plastic changes and revealed that key factors, including the co-firing of stimulus-evoked neuronal ensembles, the spatial organization of synaptic clusters, and the overall network topology, play an important role in affecting the extent of synaptic plasticity.

Strengths:

The detailed, large-scale model employed in this study enables the evaluation of diverse factors across various levels that influence the extent of plastic changes. Specifically, it facilitates the assessment of synaptic organization at the subcellular level, network topology at the macroscopic level, and the co-activation of neuronal ensembles at the activity level. Moreover, modeling plasticity under in vivo-like conditions enhances the model's relevance to experiments.

Weaknesses:

(1) The authors claimed that, under in vivo-like conditions and in the presence of plasticity, firing rates and weight distributions remain stable without additional homeostatic mechanisms during a 10-minute stimulation period. However, the weights do not reach the steady state immediately after the 10-minute stimulation. Therefore, extended simulations are necessary to substantiate the claim.

(2) Another major limitation of the paper lies in its lack of mechanistic insights into the observed phenomena (particularly on aspects that are typically impossible to assess in traditional simplified models, like layer-specific and layer-to-layer pathways-specific plasticity changes), as well as the absence of discussions on the potential computational implications of the corresponding observed plastic changes.

这是一整句话而不是逗号后面另起一句的意思，因为“that” 引导了一个宾语从句，这个从句需要包含完整的主谓结构来表达意思，to look good不是一个句子而是一个目的性不定式短语，说明为了“看起来好”，所以需要后面的a proof has to have lots of symbols and almost no English text.去补充

Reviewer #3 (Public review):

Summary:

This paper investigates the relationship between the proteolytic stability of an antibiotic target enzyme and the evolution of antibiotic resistance via increased gene copy number. The target of the antibiotic trimethoprim is dihydrofolate reductase (DHFR). In Escherichia coli, DHFR is encoded by folA and the major proteolysis housekeeping protease is Lon (lon). In this manuscript, the authors report the results of the experimental evolution of a lon mutant strain of E. coli in response to sub-inhibitory concentrations of the antibiotic trimethoprim and then investigate the relationship between proteolytic stability of DHFR mutants and the evolution of folA gene duplication. After 25 generations of serial passaging in a fixed concentration of trimethoprim, the authors found that folA duplication events were more common during the evolution of the lon strain, than the wt strain. However, with continued passaging, some folA duplications were replaced by a single copy of folA containing a trimethoprim resistance-conferring point mutation. Interestingly, the evolution of the lon strain in the setting of increasing concentrations of trimethoprim resulted in evolved strains with different levels of DHFR expression. In particular, some strains maintained two copies of a mutant folA that encoded an unstable DHFR. In a lon+ background, this mutant folA did not express well and did not confer trimethoprim resistance. However, in the lon- background, it displayed higher expression and conferred high-level trimethoprim resistance. The authors concluded that maintenance of the gene duplication event (and the absence of Lon) compensated for the proteolytic instability of this mutant DHFR. In summary, they provide evidence that the proteolytic stability of an antibiotic target protein is an important determinant of the evolution of target gene copy number in the setting of antibiotic selection.

Strengths:

The major strength of this paper is identifying an example of antibiotic resistance evolution that illustrates the interplay between the proteolytic stability and copy number of an antibiotic target in the setting of antibiotic selection. If the weaknesses are addressed, then this paper will be of interest to microbiologists who study the evolution of antibiotic resistance.

Weaknesses:

Although the proposed mechanism is highly plausible and consistent with the data presented, the analysis of the experiments supporting the claim is incomplete and requires more rigor and reproducibility. The impact of this finding is somewhat limited given that it is a single example that occurred in a lon strain and compensatory mutations for evolved antibiotic resistance mechanisms are described. In this case, it is not clear that there is a functional difference between the evolution of copy number versus any other mechanism that meets a requirement for increased "expression demand" (e.g. promoter mutations that increase expression and protein stabilizing mutations).

Reviewer #3 (Public review):

Summary:

Using a specparam (1/f) analysis of task-evoked activity, the authors propose that "substantial changes traditionally attributed to theta oscillations in working memory tasks are, in fact, due to shifts in the spectral slope of aperiodic activity." This is a very bold and ambitious statement, and the field of event-related EEG would benefit from more critical assessments of the role of aperiodic changes during task events. Unfortunately, the data shown here does not support the main conclusion advanced by the authors.

Strengths:

The field of event-related EEG would benefit from more critical assessments of the role of aperiodic changes during task events. The authors perform a number of additional control analyses, including different types of baseline correction, ERP subtraction, as well as replication of the experiment with two additional datasets.

Weaknesses:

The authors did not first show that their first task successfully evoked theta power, nor that specparam is capable of quantifying the background around a short theta burst, nor that theta effects are different between baseline corrected vs. spectral parameterized quantifications.

Reviewer #3 (Public review):

Summary:

The present study reports findings from a series of experiments suggesting that bovine oviductal fluid and species-specific oviductal glycoprotein (OVGP1 or oviductin) from bovine, murine, or human sources modulate the species specificity of bovine and murine oocytes.

Strengths:

The study reported in the manuscript deals with an important topic of interest in reproductive biology.

Weaknesses:

The manuscript began with a well-written introduction, but problems started to surface in the Results section, in the Discussion, as well as in the Materials and Methods. Major concerns include inconsistencies, misinterpretation of results, lacking up-to-date literature search, numerous errors found in the figure legends, misleading and incorrect information given in the Materials and Methods, missing information regarding statistical analysis, and inadequate discussion. These concerns raise questions regarding the authenticity of the study, reliability of the findings, and interpretation of the results. The manuscript does not provide solid and convincing findings to support the conclusion.

Reviewer #3 (Public review):

Freire and co-authors examine the role of the exocyst complex during the formation and secretion of mucins from secretory granules in the larval salivary gland of Drosophila melanogaster. Using transgenic lines with a tagged Sgs3 mucin, the authors KD expression of exocyst subunit members and observe a defect in secretory granules with a heterogeneity of phenotypes. By carefully controlling RNAi expression using a Gal4-based system, the authors can KD exocyst subunit expression to varying degrees. The authors find that the stronger the inhibition of expression of the exocyst is, the earlier the defect is in the secretory pathway. The manuscript is well written, the model system is physiological, and the techniques are innovative.

In my initial review, my major concern was the pleiotropic effect of the loss of exocyst. The authors have responded to this point with clarity and have argued that the multiple localisations of exocyst during the Sgs3 synthesis programme indicate it is likely a direct phenotype. They also performed some analysis of PM lipids but did not detect a difference. I accept the arguments presented. However, I remain concerned that these are due to a pleiotropic effect. It is very hard to absolutely prove a direct effect, and due to the unusual claim and nature of the evidence (depletion levels), I think that there is still the possibility of this being an indirect effect. Perhaps it is just worth the authors writing a paragraph in the discussion, at least accepting the possibility that it is an indirect effect so future readers are aware of that.

Reviewer #3 (Public review):

Summary:

The study by Fallah et al provides a thorough characterization of the effects of two basal ganglia output pathways on cholinergic, glutamatergic, and GABAergic neurons of the PPN. The authors first found that SNr projections spread over the entire PPN, whereas GPe projections are mostly concentrated in the caudal portion of the nucleus. Then the authors characterized the postsynaptic effects of optogenetically activating these basal ganglia inputs and identified the PPN's cell subtypes using genetically encoded fluorescent reporters. Activation of inputs from the SNr inhibited virtually all PPN neurons. Activation of inputs from the GPe predominantly inhibited glutamatergic neurons in the caudal PPN, and to a lesser extent GABAergic neurons. Finally, the authors tested the effects of activating these inputs on locomotor activity and place preference. SNr activation was found to increase locomotor activity and elicit avoidance of the optogenetic stimulation zone in a real-time place preference task. In contrast, GPe activation reduced locomotion and increased the time in the RTPP stimulation zone.

Strengths:

The evidence of functional connectivity of SNr and GPe neurons with cholinergic, glutamatergic, and GABAergic PPN neurons is solid and reveals a prominent influence of the SNr over the entire PPN output. In addition, the evidence of a GPe projection that preferentially innervates the caudal glutamatergic PPN is unexpected and highly relevant for basal ganglia function.

Opposing effects of two basal ganglia outputs on locomotion and valence through their connectivity with the PPN.

Overall, these results provide an unprecedented cell-type-specific characterization of the effects of basal ganglia inputs in the PPN and support the well-established notion of a close relationship between the PPN and the basal ganglia.

Weaknesses:

The behavioral experiments require further analysis as some motor effects could have been averaged out by analyzing long segments. Additional controls are needed to rule out a motor effect in the real-time place preference task. Importantly, the location of the stimulation is not reported even though this is critical to interpret the behavioral effects.

There are some concerns about the possible recruitment of dopamine neurons in the SNr experiments.

Reviewer #2 (Public review):

Summary:

Developing neuronal models that are shareable, reproducible, and interoperable allows the neuroscience community to make better use of published models and to collaborate more effectively. In this manuscript, the authors present a consolidated overview of the NeuroML model description system along with its associated tools and workflows. They describe where different components of this ecosystem lay along the model development pathway and highlight resources, including documentation and tutorials, to help users employ this system.

Strengths:

The manuscript is well-organized and clearly written. It effectively uses the delineated model development life cycle steps, presented in Figure 1, to organize its descriptions of the different components and tools relating to NeuroML. It uses this framework to cover the breadth of the software ecosystem and categorize its various elements. The NeuroML format is clearly described, and the authors outline the different benefits to its particular construction. As primarily a means of describing models, NeuroML also depends on many other software components to be of high utility to computational neuroscientists; these include simulators (ones that both pre-date NeuroML and those developed afterwards), visualization tools, and model databases.

Overall, the rationale for the approach NeuroML has taken is convincing and well-described. The pointers to existing documentation, guides, and the example usages presented within the manuscript are useful starting points for potential new users. This manuscript can also serve to inform potential users of features or aspect of the ecosystem that they may have been unaware of, which could lower obstacles to adoption. While much of what is presented is not new to this manuscript, it still serves as a useful resource for the community looking for information about an established, but perhaps daunting, set of computational tools.

Weaknesses:

The manuscript in large part catalogs the different tools and functionalities that have been produced through the long development cycle of NeuroML. Overall, the interoperability of NeuroML is a benefit, but it does increase the complexity of choices facing users entering into the ecosystem.

In many respects this is an intractable fact of the current environment, but the authors do try to mitigate the issue with user guides (e.g., Table 1) and example code (e.g. Box 1) which address a range of target user audiences, from those learning about the ecosystem for the first time to those looking to implement specific model features. They also categorize different simulator options (Figure 5) and provide feature comparisons (Table 3), which could assist with the most daunting choice faced by new users.

Comments on revised version:

The authors have addressed my major concerns with the original manuscript. The discussion of simulators in particular is much clearer now, and the manuscript has been restructured so that specific details pertinent to a much more focused audience have been rewritten or shifted to more appropriate locations.

Reviewer #3 (Public review):

Summary:

This study investigates evidence for a hypothesised, causal relationship between education, specifically the number of years spent in school, and brain structure as measured by common brain phenotypes such as surface area, cortical thickness, total volume, and diffusivity.

To test their hypothesis, the authors rely on a "natural" intervention, that is, the 1972 ROSLA act that mandated an extra year of education for all 15-year-olds. The study's aim is to determine potential discontinuities in the outcomes of interest at the time of the policy change, which would indicate a causal dependence. Naturalistic experiments of this kind are akin to randomised controlled trials, the gold standard for answering questions of causality.

Using two complementary, regression-based approaches, the authors find no discernible effect of spending an extra year in primary education on brain structure. The authors further demonstrate that observational studies showing an effect between education and brain structure may be confounded and thus unreliable when assessing causal relationships.

Strengths:

(1) A clear strength of this study is the large sample size totalling up to 30k participants from the UK Biobank. Although sample sizes for individual analyses are an order of magnitude smaller, most neuroimaging studies usually have to rely on much smaller samples.

(2) This study has been preregistered in advance, detailing the authors' scientific question, planned method of inquiry, and intended analyses, with only minor, justifiable changes in the final analysis.

(3) The analyses look at both global and local brain measures used as outcomes, thereby assessing a diverse range of brain phenotypes that could be implicated in a causal relationship with a person's level of education.

(4) The authors use multiple methodological approaches, including validation and sensitivity analyses, to investigate the robustness of their findings and, in the case of correlational analysis, highlight differences with related work by others.

(5) The extensive discussion of findings and how they relate to the existing, somewhat contradictory literature gives a comprehensive overview of the current state of research in this area.

Weaknesses:

(1) This study investigates a well-posed but necessarily narrow question in a specific setting: 15-year-old British students born around 1957 who also participated in the UKB imaging study roughly 60 years later. Thus conclusions about the existence or absence of any general effect of the number of years of education on the brain's structure are limited to this specific scenario.

(2) The authors address potential concerns about the validity of modelling assumptions and the sensitivity of the regression discontinuity design approach. However, the possibility of selection and cohort bias remains and is not discussed clearly in the paper. Other studies (e.g. Davies et al 2018, https://www.nature.com/articles/s41562-017-0279-y) have used the same policy intervention to study other health-related outcomes and have established ROSLA as a valid naturalistic experiment. Still, quoting Davies et al. (2018), "This assumes that the participants who reported leaving school at 15 years of age are a representative sample of the sub-population who left at 15 years of age. If this assumption does not hold, for example, if the sampled participants who left school at 15 years of age were healthier than those in the population, then the estimates could underestimate the differences between the groups.". Recent studies (Tyrrell 2021, Pirastu 2021) have shown that UK Biobank participants are on average healthier than the general population. Moreover, the imaging sub-group has an even stronger "healthy" bias (Lyall 2022).

(3) The modelling approach used in this study requires that all covariates of no interest are equal before and after the cut-off, something that is impossible to test. Mentioned only briefly, the inclusion and exclusion of covariates in the model are not discussed in detail. Standard imaging confounds such as head motion and scanning site have been included but other factors (e.g. physical exercise, smoking, socioeconomic status, genetics, alcohol consumption, etc.) may also play a role.

Reviewer #3 (Public review):

Summary:

This manuscript describes an in-depth analysis of the effect of the AAA+ ATPase PCH-2 on meiotic crossover formation in C. elegant. The authors reach several conclusions, and attempt to synthesize a 'universal' framework for the role of this factor in eukaryotic meiosis.

Strengths:

The manuscript makes use of the advantages of the 'conveyor' belt system within the c.elegans reproductive tract, to enable a series of elegant genetic experiments.

Weaknesses:

A weakness of this manuscript is that it heavily relies on certain genetic/cell biological assays that can report on distinct crossover outcomes, without clear and directed control over other aspects and variables that might also impact the final repair outcome. Such assays are currently out of reach in this model system.

In general, this manuscript could be more generally accessible to non-C.elegans readers. Currently, the manuscript is hard to digest for non-experts (even if meiosis researchers). In addition, the authors should be careful to consider alternative explanations for certain results. At several steps in the manuscript, results could ostensibly be caused by underlying defects that are currently unknown (for example, can we know for sure that pch-2 mutants do not suffer from altered DSB patterning, and how can we know what the exact functional and genetic interactions between pch-2 and HORMAD mutants tell us?). Alternative explanations are possible and it would serve the reader well to explicitly name and explain these options throughout the manuscript.

Reviewer #3 (Public review):

Summary:

Childers et al. address a fundamental question about the complex relationship within the gut: the link between nutrient absorption, microbial presence, and intestinal physiology. They focus on the role of lysosome-rich enterocytes (LREs) and the microbiota in protein absorption within the intestinal epithelium. By using germ-free and conventional zebrafishes, they demonstrate that microbial association leads to a reduction in protein uptake by LREs. Through impressive in vivo imaging of gavaged fluorescent proteins, they detail the degradation rate within the LRE region, positioning these cells as key players in the process. Additionally, the authors map protein absorption in the gut using single-cell sequencing analysis, extensively describing LRE subpopulations in terms of clustering and transcriptomic patterns. They further explore the monoassociation of ex-germ-free animals with specific bacterial strains, revealing that the reduction in protein absorption in the LRE region is strain-specific.

Strengths:

The authors employ state-of-the-art imaging to provide clear evidence of the protein absorption rate phenotype, focusing on a specific intestinal region. This innovative method of fluorescent protein tracing expands the field of in vivo gut physiology.

Using both conventional and germ-free animals for single-cell sequencing analysis, they offer valuable epithelial datasets for researchers studying host-microbe interactions. By capitalizing on fluorescently labelled proteins in vivo, they create a new and specific atlas of cells involved in protein absorption, along with a detailed LRE single-cell transcriptomic dataset.

Weaknesses:

While the authors present tangible hypotheses, the data are primarily correlative, and the statistical methods are inadequate. They examine protein absorption in a specific, normalized intestinal region but do not address confounding factors between germ-free and conventional animals, such as size differences, transit time, and oral gavage, which may impact their in vivo observations. This oversight can lead to bold conclusions, where the data appear valuable but require more nuance.

The sections of the study describing the microbiota or attempting functional analysis are elusive, with related data being overinterpreted. The microbiome field has long used 16S sequencing to characterize the microbiota, but its variability due to experimental parameters limits the ability to draw causative conclusions about the link between LRE activity, dietary protein, and microbial composition. Additionally, the complex networks involved in dopamine synthesis and signalling cannot be fully represented by RNA levels alone. The authors' conclusions on this biological phenomenon based on single-cell data need support from functional and in vivo experiments.

Reviewer #3 (Public review):

Summary:

This study is focused on testing whether statistical learning (a mechanism for parsing the speech signal into smaller chunks) preferentially operates over certain features of the speech at birth in humans. The features under investigation are phonetic content and speaker identity. Newborns are tested in an EEG paradigm in which they are exposed to a long stream of syllables. In Experiment 1, newborns are familiarized with a sound stream that comprises regularities (transitional probabilities) over syllables (e.g., "pe" followed by "tu" in "petu" with 1.0 probability) while the voices uttering the syllables remain random. In Experiment 2, newborns are familiarized with the same sound stream but, this time, the regularities are built over voices (e.g., "green voice" followed by "red voice" with 1.0 probability) while the concatenation of syllables stays random. At the test, all newborns listened to duplets (individual chunks) that either matched or violated the structure of the familiarization. In both experiments, newborns showed neural entrainment to the regularities implemented in the stream, but only the duplets defined by transitional probabilities over syllables (aka word forms) elicited a N400 ERP component. These results suggest that statistical learning operates in parallel and independently on different dimensions of the speech already at birth and that there seems to be an advantage for processing statistics defining word forms rather than voice patterns.

Strengths:

This paper presents an original experimental design that combines two types of statistical regularities in a speech input. The design is robust and appropriate for EEG with newborns. I appreciated the clarity of the Methods section. There is also a behavioral experiment with adults that acts like a control study for newborns. The research question is interesting, and the results add new information about how statistical learning works at the beginning of postnatal life, and on which features of the speech. The figures are clear and helpful in understanding the methods, especially the stimuli and how the regularities were implemented.

Weaknesses:

(1) I'm having a hard time understanding the link between the results of the study and the universality of statistical learning. The main goal of the study was testing whether statistical learning is a general mechanism for newborns that operates on any speech dimension, or whether it operates over linguistic features only. To test that, statistical regularities (TPs) were built over syllables (e.g., pe followed by tu in petu with 1.0 probability) or voices (e.g., green voice followed by red voice with 1.0 probability). Voices were considered as the non-linguistic dimension.

While it's true that voice is not essential for language (i.e., sign languages are implemented over gestures; the use of voices to produce non-linguistic sounds, like laughter), it is a feature of spoken languages. Thus I'm not sure if we can really consider this study as a comparison between linguistic and non-linguistic dimensions. In turn, I'm not sure that these results show that statistical learning at birth operates on non-linguistic features, being voices a linguistic dimension at least in spoken languages. I'd like to hear the authors' opinions on this.

Along the same line, in the Discussion section, the present results are interpreted within a theoretical framework showing statistical learning in auditory non-linguistic (string of tones, music) and visual domains as well as visual and other animal species. I'm not sure if that theoretical framework is the right fit for the present results.

(2) I'm not sure whether the fact that we see parallel and independent tracking of statistics in the two dimensions of speech at birth indicates that newborns would be able to do so in all the other dimensions of the speech. If so, what other dimensions are the authors referring to?

(3) Lines 341-345: Statistical learning is an evolutionary ancient learning mechanism but I do not think that the present results are showing it. This is a study on human neonates and adults, there are no other animal species involved therefore I do not see a connection with the evolutionary history of statistical learning. It would be much more interesting to make claims on the ontogeny (rather than philogeny) of statistical learning, and what regularities newborns are able to detect right after birth. I believe that this is one of the strengths of this work.

(4) The description of the stimuli in Lines 110-113 is a bit confusing. In Experiment 1, e.g., "pe" and "tu" are both uttered by the same voice, correct? ("random voice each time" is confusing). Whereas in Experiment 2, e.g., "pe" and "tu" are uttered by different voices, for example, "pe" by yellow voice and "tu" by red voice. If this is correct, then I recommend the authors to rephrase this section to make it more clear.

(5) Line 114: the sentence "they should compute a 36 x 36 TPs matrix relating each acoustic signal, with TPs alternating between 1/6 within words and 1/12 between words" is confusing as it seems like there are different acoustic signals. Can the authors clarify this point?

Reviewer #3 (Public review):

Summary:

The authors describe a valuable method to find gene sets that may correlate with a patient's survival. This method employs iterative tests of significance across randomised samples with a range of proportions of the original dataset. Those genes that show significance across a range of samples are chosen. Based on these gene sets, hub genes are determined from similarity scores.

Strengths:

MEMORY allows them to assess the correlation between a gene and patient prognosis using any available transcriptomic dataset. They present several follow-on analyses and compare the gene sets found to previous studies.

Weaknesses:

Unfortunately, the authors have not included sufficient details for others to reproduce this work or use the MEMORY algorithm to find future gene sets, nor to take the gene findings presented forward to be validated or used for future hypotheses.

Reviewer #3 (Public review):

In this report, Keenen et al. present a thoroughly characterized platform for identifying potential molecular mechanisms regulating syncytiotrophoblast cell functions in placental biology. The application of single-cell assessments to identify developmental trajectories of this lineage has been challenging due to the complex, multinucleated structure of the syncytium. The authors provide a comprehensive comparative assessment of term placental tissue and three independent trophoblast organoid models. They use single-cell and single-nucleus RNA sequencing followed by differential gene expression and pseudotime analyses to identify subpopulations and differentiation trajectories. They further compare the datasets generated in this study to publicly available datasets from first-trimester placental tissue. The work is timely as optimization of trophoblast organoids is an evolving topic in placental research. Careful characterization of in vitro models has been noted as essential for model selection and result interpretation in the field.

The study elucidates syncytiotrophoblast nucleus subtypes and proportions in three different organoid models and compares subtypes and gene expression signatures to placental tissues. This work advances the field by demonstrating the utility of different trophoblast organoids to model syncytiotrophoblast differentiation. The in-depth characterization of cell types comprising the different organoid models and how they compare to placental tissue will help to inform model selection for future experimentation in the field. Defining cell composition and cell differentiation trajectories will also aid in data interpretation for data generated by these tissue and model sources. Overall, the conclusions presented in the manuscript are well supported by the data. The figures, as presented, are informative and striking.

The authors present outstanding progress toward their aim of identifying, "the underlying control of the syncytiotrophoblast". They identify the chromatin remodeler, RYBP, as well as other regulatory networks that they propose are critical to syncytiotrophoblast development. This study is limited in fully addressing the aim, however, as functional evidence for the contributions of the factors/pathways to syncytiotrophoblast cell development is needed. Future experimentation testing the hypotheses generated by this work will define the essentiality of the identified factors to syncytiotrophoblast development and function. Localization and validation of the identified factors within tissue and at the protein level will also provide further contextual evidence to address the hypotheses generated.

Reviewer #3 (Public review):

Summary:

The manuscript presents computational modelling of the behaviour of mice during encounters with novel and familiar objects, originally reported by Akiti et al. (Neuron 110, 2022). Mice typically perform short bouts of approach followed by a retreat to a safe distance, presumably to balance exploration to discover possible rewards with the potential risk of predation. However, there is considerable heterogeneity in this exploratory behaviour, both across time as an individual subject becomes more confident in approaching the object, and across subjects; with some mice rapidly becoming confident to closely explore the object, while other timid mice never become fully confident that the object is safe. The current work aims to explain both the dynamics of adaptation of individual animals over time, and the quantitative and qualitative differences in behaviour between subjects, by modelling their behaviour as arising from model-based planning in a Bayes adaptive Markov Decision Process (BAMDP) framework, in which the subjects maintain and update probabilistic estimates of the uncertain hazard presented by the object, and rationally balance the potential reward from exploring the object with the potential risk of predation it presents.

In order to fit these complex models to the behaviour the authors necessarily make substantial simplifying assumptions, including coarse-graining the exploratory behaviour into phases quantified by a set of summary statistics related to the approach bouts of the animal. Inter-individual variation between subjects is modelled both by differences in their prior beliefs about the possible hazard presented by the object and by differences in their risk preference, modelled using a conditional value at risk (CVaR) objective, which focuses the subject's evaluation on different quantiles of the expected distribution of outcomes. Interestingly these two conceptually different possible sources of inter-subject variation in brave vs timid exploratory behaviour turn out not to be dissociable in the current dataset as they can largely compensate for each other in their effects on the measured behaviour. Nonetheless, the modelling captures a wide range of quantitative and qualitative differences between subjects in the dynamics of how they explore the object, essentially through differences in how subject's beliefs about the potential risk and reward presented by the object evolve over the course of exploration, and are combined to drive behaviour.

Exploration in the face of risk is a ubiquitous feature of the decision-making problem faced by organisms, with strong clinical relevance, yet remains poorly understood and under-studied, making this work a timely and welcome addition to the literature.

Strengths:

(1) Individual differences in exploratory behaviour are an interesting, important, and under-studied topic.

(2) Application of cutting-edge modelling methods to a rich behavioural dataset, successfully accounting for diverse qualitative and qualitative features of the data in a normative framework.

(3) Thoughtful discussion of the results in the context of prior literature.

Limitations:

(1) The model-fitting approach used of coarse-graining the behaviour into phases and fitting to their summary statistics may not be applicable to exploratory behaviours in more complex environments where coarse-graining is less straightforward.

(2) Some aspects of the work could be more usefully clarified within the manuscript.

Reviewer #3 (Public review):

Summary:

Chan et al. evaluated the role of RNase III, encoded by the rnc gene, in Salmonella virulence. Chan et al. first identified rnc among the genes with upregulated mRNA levels in virulent Salmonella isolates. The authors further showed that deletion of rnc resulted in increased double-stranded RNA (dsRNA) and reduced invasion rate and replication rate in an in vitro macrophage model. The authors then showed that transfection of total RNA of rnc knock-out strains upregulates (with respect to a WT Salmonella strain) expression levels of immune-related genes (e.g., TNF-a, IL-1B, etc.) in a dsRNA-dependent manner. The authors reported reduced SodA protein accumulation in the rnc knock-out strains, despite higher levels of sodA mRNA, suggesting a role of SodA in the protection against reactive oxygen species. Finally, the authors showed, using a mice model, the partial contribution of sodA in the restoration of virulence levels in the rnc knock-out strains.

Strengths:

(1) The manuscript is well written.

(2) The authors evaluated the impact of rnc deletion in both in vitro and mice infection models. Both experiment setups supported the contribution of rnc to Salmonella virulence.

(3) The authors tested the effect of rnc deletion in different genetic backgrounds (i.e., different bacterial isolates) offering additional support to their claims.

(4) Measurement of SodA protein levels nicely complemented and informed initial findings at the mRNA level.

Weaknesses:

(1) The authors failed to discuss how their work differentiates from recent studies of rnc deletion strains in Salmonella (NIH PMID: 38182942) and Escherichia coli (NIH PMID: 35456749). Remarkably, the first publication performed genome-wide transcriptional profiling of a rnc deletion Salmonella strain. The second publication explored the link between rnc and sodA in E. coli.

(2) The authors should explain what the criteria for selecting food and clinical isolates for molecular characterization were. This information is valuable for the reader as they may wonder about the impact of isolate selection in the study's conclusions. Similarly, the authors need to explain how they selected their controls for baseline gene expression, virulence, etc.. Furthermore, I wondered if they could use an avirulent Salmonella strain as an additional control.

(3) The authors do not perform any analysis of the differentially expressed genes (DEGs) identified in their study. They should leverage DEGs to expand their mechanistic insights of other genes or functional processes putatively linked to rnc activity and virulence. Additionally, authors should make transcriptional data and the output of their differential expression analysis (and the list of differentially expressed genes-DEGs) available to the readers. In fact, it is not clear how the DEGS were defined.

Reviewer #3 (Public review):

Summary:

This manuscript claims to provide a new null hypothesis for testing the effects of biodiversity on ecosystem functioning. It reports that the strength of biodiversity effects changes when this different null hypothesis is used. This main result is rather inevitable. That is, one expects a different answer when using a different approach. The question then becomes whether the manuscript's null hypothesis is both new and an improvement on the null hypothesis that has been in use in recent decades.

Strengths:

In general, I appreciate studies like this that question whether we have been doing it all wrong and I encourage consideration of new approaches.

Weaknesses:

Despite many sweeping critiques of previous studies and bold claims of novelty made throughout the manuscript, I was unable to find new insights. The manuscript fails to place the study in the context of the long history of literature on competition and biodiversity and ecosystem functioning. The Introduction claims the new approach will address deficiencies of previous approaches, but after reading further I see no evidence that it addresses the limitations of previous approaches noted in the Introduction. Furthermore, the manuscript does not reproducibly describe the methods used to produce the results (e.g., in Table 1) and relies on simulations, claiming experimental data are not available when many experiments have already tested these ideas and not found support for them. Finally, it is unclear to me whether rejecting the 'new' null hypothesis presented in the manuscript would be of interest to ecologists, agronomists, conservationists, or others.

Comments on revised version:

Please see review comments on the previous version of this manuscript. The authors have not revised their manuscript to address most of the issues previously raised by reviewers.

Reviewer #3 (Public review):

Summary:

In this study, Peterson et al. longitudinally record and document the vocal repertoires of three Mongolian gerbil families. Using unsupervised learning techniques, they map the variability across these groups, finding that while overall statistics of, e.g., vocal emission rates and bout lengths are similar, families differed markedly in their distributions of syllable types and the transitions between these types within bouts. In addition, the large and rich data are likely to be valuable to others in the field.

Strengths:

- Extensive data collection across multiple days in multiple family groups.<br /> - Thoughtful application of modern analysis techniques for analyzing vocal repertoires.<br /> - Careful examination of the statistical structure of vocal behavior, with indications that these gerbils, like naked mole rats, may differ in repertoire across families.<br /> - Estimation of the stability of the effects across days.

Weaknesses:

- The work is largely descriptive, documenting behavior rather than testing a specific hypothesis.<br /> - The number of families (N=3) is somewhat limited, though the authors have taken some care to examine the robustness of the findings.

Reviewer #3 (Public review):

This paper has high significance because it addresses a prevalent parasitic infection of the nervous system, Neurocysticercosis (NCC). The infection is caused by larvae of the parasitic cestode Taenia solium It is a leading cause of epilepsy in adults worldwide

To address the effects of cestode larvae, homogenates and excretory/secretory products of larvae were added to organotypic brain slice cultures of rodents or layer 2/3 of human cortical brain slices from patients with refractory epilepsy.

A self-made pressure ejection system was used to puff larvae homogenate (20 ms puff) onto the soma of patched neurons. The mechanical force could have caused depolarizaton so a vehicle control is critical. On line 150 they appear to have used saline in this regard, and clarification would be good. Were the controls here (and aCSF elsewhere) done with the low Mg2+o aCSF like the larvae homogenates?

They found that neurons depolarized after larvae homogenate exposure and the effect was mediated by glutamate but not nicotinic receptors for acetylcholine (nAChRs), acid-sensing channels or substance P.

They also showed the elevated K+ in the homogenate (~11 mM) could not account for the depolarization. They also confirmed that only small molecules led to the depolarization after filtering out very large molecules. That supports the conclusion that glutamate - which is quite small - could be responsible.

They suggest the effects could underlie seizure generation in NCC.

Using Glutamate-sensing fluorescent reporters they found the larvae contain glutamate and can release it, a strength of the paper.

Reviewer #3 (Public review):

Significance of the Findings:

The study by Liu et al. presents a novel method, DNA-O-MAP, which combines locus-specific hybridisation with proximity biotinylation to isolate specific genomic regions and their associated proteins. The potential significance of this approach lies in its purported ability to target genomic loci with heightened specificity by enabling extensive washing prior to the biotinylation reaction, theoretically improving the signal-to-noise ratio when compared with other methods such as dCas9-based techniques. Should the method prove successful, it could represent a notable advancement in the field of chromatin biology, particularly in establishing the proteomes of individual chromatin regions - an extremely challenging objective that has not yet been comprehensively addressed by existing methodologies.

Strength of the Evidence:

The evidence presented by the authors is somewhat mixed, and the robustness of the findings appears to be preliminary at this stage. While certain data indicate that DNA-O-MAP may function effectively for repetitive DNA regions, a number of the claims made in the manuscript are either unsupported or require further substantiation. There are significant concerns about the resolution of the method, with substantial biotinylation signals extending well beyond the intended target regions (megabases around the target), suggesting a lack of specificity and poor resolution, particularly for smaller loci. Furthermore, comparisons with previous techniques are unfounded since the authors have not provided direct comparisons with the same mass spectrometry (MS) equipment and protocols. Additionally, although the authors assert an advantage in multiplexing, this claim appears overstated, as previous methods could achieve similar outcomes through TMT multiplexing. Therefore, while the method has potential, the evidence requires more rigorous support, comprehensive benchmarking, and further experimental validation to demonstrate the claimed improvements in specificity and practical applicability.

Reviewer #3 (Public review):

Summary:

The paper by Li et al. describes the crystal structure of a complex of Sld3-Cdc45-binding domain (CBD) with Cdc45 and a model of the dimer of an Sld3-binding protein, Sld7, with two Sld3-CBD-Cdc45 for the tethering. In addition, the authors showed the genetic analysis of the amino acid substitution of residues of Sld3 in the interface with Cdc45 and biochemical analysis of the protein interaction between Sld3 and Cdc45 as well as DNA binding activity of Sld3 to the single-strand DNAs of the ARS sequence.

Strengths:

The authors provided a nice model of an intermediate step in the assembly of an active Cdc45-MCM-GINS (CMG) double hexamers at the replication origin, which is mediated by the Sld3-Sld7 complex. The dimer of the Sld3-Sld7 complexes tethers two MCM hexamers together for the recruitment of GINS-Pol epsilon on the replication origin.

Weaknesses:

The biochemical analysis should be carefully evaluated with more quantitative ways to strengthen the authors' conclusion.

Reviewer #3 (Public review):

Summary:

The study explores the cellular and circuit features that distinguish dentate gyrus semilunar granule cells and granule cells activated during contextual memory formation. The authors tag memory and enriched environment-activated dentate granule cells and semilunar granule cells and show their reactivation in an appropriate context a week later. They perform patch clamp recordings from activated and surrounding neurons to understand cellular driving the selective activation of semilunar granule cells and granule cells. Authors perform dual patch clamp recordings from various pairs of labeled semilunar granule cells, labeled granule cells, unlabeled granule cells, and unlabeled semilunar granule cells. The sustained firing of semilunar granule cells explained their preferential activation. In addition, activated neurons received correlated inputs.

Strengths:

The authors confirmed engram cell properties of activated semilunar granule cells and granule cells in two different paradigms, validated using an enriched environment paradigm.

The authors carefully separate semilunar granule cells from granule cells, using electrophysiology and morphology. Cell filling to confirm morphology further strengthens confidence.

The dual patch recordings, which are technically challenging, are carefully performed, and the presence of synaptic activity is confirmed.

Finally, the correlation analysis of EPSCs on labeled neurons is rigorous.

Weaknesses:

(1) Engram cells are (i) activated by a learning experience, (ii) physically or chemically modified by the learning experience, and (iii) reactivated by subsequent presentation of the stimuli present at the learning experience (or some portion thereof), resulting in memory retrieval. The authors show that exposure to Barnes Maze and the enriched environment-activated semilunar granule cells and granule cells preferentially in the superior blade of the dentate gyrus, and a significant fraction were reactivated on re-exposure. However, physical or chemical modification by experience was not tested. Experience modifies engram cells, and a common modification is the Hebbian, i.e., potentiation of excitatory synapses. The authors recorded EPSCs from labeled and unlabeled GCs and SGCs. Was there a difference in the amplitude or frequency of EPSCs recorded from labeled and unlabeled cells?

(2) The authors studied five sequential sections, each 250 μm apart across the septotemporal axis, which were immunostained for c-Fos and analyzed for quantification. Is this an adequate sample? Also, it would help to report the dorso-ventral gradient since more engram cells are in the dorsal hippocampus. Slices shown in the figures appear to be from the dorsal hippocampus.

(3) The authors investigated the role of surround inhibition in establishing memory engram SGCS and GCs. Surprisingly, they found no evidence of lateral inhibition in the slice preparation. Interneurons, e.g., PV interneurons, have large axonal arbors that may be cut during slicing. Similarly, the authors point out that some excitatory connections may be lost in slices. This is a limitation of slice electrophysiology.

Reviewer #3 (Public review):

Summary:

This paper is focused on gonad development, with an examination of the role of the Drosophila somatic sex determination hierarchy, sex chromosomes, and the interaction between the sex determination hierarchy and sex chromosome composition. The authors use bulk RNA-seq, long-read RNA-seq, and additional published single-cell RNA-seq data sets to examine gene expression in wild-type male and female gonads and in sex-transformed gonads that have functional alterations of the sex determination hierarchy gene, transformer. In these latter genotypes, the authors generate animals that are chromosomally XX with testes, and chromosomally XY with ovaries. The data were collected from larval gonads, as adults have substantial germ cell loss when sex is transformed. In addition, the authors characterize the cell biology of the gonads using well-established antibody markers and expression patterns. The authors show that there is no simple pathway controlling why the sex of the somatic tissue and germline need to match. Their data clearly show that both sex chromosome karyotype and somatic transformer status regulate gene expression together, with fewer germline gene expression patterns regulated by karyotype alone.

This a complete study where the authors go beyond gene expression and examine impacts on splicing, with one interesting focus on the sex hierarchy splicing factor sex-lethal, and also on the role of the sex hierarchy gene doublesex. Gonad development in sex-transformed animals has been challenging to understand, in terms of the interactions between somatic sex determination, germline sex determination, and karyotype. This paper adds an important step, with high-resolution genomic, molecular, and cellular understanding.

Strengths:

The genomic experiments are rigorously performed, with appropriate replication and statistical analyses. The authors do high-resolution cell biological quantification, with some validation of the genomic results. The authors also provide a webpage for dynamic viewing of feature plots, which will be a valuable resource for colleagues. Overall, the authors do a good job providing context for their readers, especially providing older literature reports and findings.

Weaknesses:

A minor weakness is that they did not provide validation of their newly developed gene-specific reporter tools.

Reviewer #3 (Public review):

Summary:

This manuscript introduces POST-IT (Pup-On-target for Small molecule Target Identification Technology), a novel non-diffusive proximity tagging system for identifying target proteins in live cells and organisms. This technology preserves cellular context essential for capturing specific drug-protein interactions, including transient complexes and membrane-associated proteins. Using an engineered fusion of proteasomal accessory factor A (PafA) and HaloTag, POST-IT specifically labels proximal proteins upon binding to a small molecule, with extensive optimization to enhance specificity and efficiency.

Strengths:

The study successfully identifies known targets and discovers new binders, such as SEPHS2 for dasatinib and VPS37C for hydroxychloroquine, advancing our understanding of their mechanisms. Additionally, its application in live zebrafish embryos demonstrates POST-IT's potential for widespread use in biological research and drug development.

Weaknesses:

Despite these promising results, several areas require further clarification or expansion to strengthen the manuscript:

(1) Target Specificity: It is crucial for the authors to differentiate between the primary targets of the POST-IT system and those identified as side effects. This distinction is essential for assessing the specificity and utility of the technology.

(2) In Vivo Target Identification: The manuscript lacks detailed clarity on which specific targets were successfully identified in the in vivo experiments. Expanding on this information would provide a clearer view of the system's effectiveness and scope in complex biological settings.

(3) Reproducibility and Scalability: Discussion on the reproducibility of the POST-IT system across various experimental setups and biological models, as well as its scalability for larger-scale drug discovery programs, would be beneficial.

(4) Quantitative Analysis: A more detailed quantitative analysis of the protein interactions identified by POST-IT, including statistical significance and comparative data against other technologies, would enhance the manuscript.

(5) Technological Limitations: The authors should discuss any limitations or potential pitfalls of the POST-IT system, which would be crucial for future users and for guiding subsequent improvements.

(6) Long-Term Stability and Activity: Information on the long-term stability and activity of the POST-IT components in different biological environments would ensure the reliability of the system in prolonged experiments.

(7) Comparison with Existing Technologies: A detailed comparison with existing proximity tagging and target identification technologies would help position POST-IT within the current landscape, highlighting its unique advantages and potential drawbacks.

(8) Concerns Regarding Overexposed Bands: Several figures in the manuscript, specifically Figure 3A, 3B, 3C, 3F, 3G, Figure 4D, and the second panels in Figure 7C as well as some figures in the supplementary file, exhibit overexposed bands.

(9) Innovation Concern: There is a previous paper describing a similar approach: Liu Q, Zheng J, Sun W, Huo Y, Zhang L, Hao P, Wang H, Zhuang M. A proximity-tagging system to identify membrane protein-protein interactions. Nat Methods. 2018 Sep;15(9):715-722. doi: 10.1038/s41592-018-0100-5. Epub 2018 Aug 13. PMID: 30104635. It is crucial to explicitly address the novel aspects of POST-IT in contrast to this earlier work.

Reviewer #3 (Public review):

Summary:

This paper described a new tool called "Image Correlation Spectroscopy; ICS) to detect clustering fluorescence signals such as foci in the nucleus (or any other cellular structures). The authors compared ICS DA (degree of aggregation) data with Imaris Spots data (and ImageJ Find Maxima data) and found a comparable result between the two analyses and that the ICS sometimes produced a better quantification than the Imaris. Moreover, the authors extended the application of ICS to detect cell-cycle stages by analyzing the DAPI image of cells. This is a useful tool without the subjective bias of researchers and provides novel quantitative values in cell biology.

Strengths:

The authors developed a new tool to detect and quantify the aggregates of immuno-fluorescent signals, which is a center of modern cell biology, such as the fields of DNA damage responses (DDR), including DNA repair. This new method could detect the "invisible" signal in cells without pre-extraction, which could prevent the effect of extracted materials on the pre-assembled ensembles, a target for the detection. This would be an alternative method for the quantification of fluorescent signals relative to conventional methods.

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

Another area in which this paper could improve its clarity is in the description of caveats of the assay. The exact math used to define resistance mutants and its dependence on the DMSO control is interesting, it is worth discussing where the failure modes of this procedure might be. Could it be that the resistance mutants identified in this assay would differ significantly from those found in patients? That results here are consistent with those seen in the clinic is promising, but discrepancies could remain. Furthermore a more in depth discussion of the MetdelEx14 results is warranted. For example, why is the DMSO signature in Figure 1 - supplement 4 so different from that of Figure 1? And finally, there is a lot of emphasis put on the unexpected results of this assay for the tivantinib "type III" inhibitor - could this in fact be because the molecule "is highly selective for the inactive or unphosphorylated form of c-Met" according to Eathiraj et al JBC 2011?

While this paper is crisply written with beautiful figures, the complexity of the data warrants a bit more clarity in how the results are visualized. Namely, clearly highlighting mutants that have previously reported and those identified by this study across all figures could help significantly in understanding the more novel findings of the work.

Finally, the potential impacts and follow-ups of this excellent study could be communicated better - it is recommended that they advertise better this paper as a resource for the community both as a dataset and as a proof of concept. In this realm I would encourage the authors to emphasize the multiple potential uses of this dataset by others to provide answers and insights on a variety of problems. Related to this, the decision to include the MetdelEx14 results, but not discuss them at all is interesting, do the authors expect future analyses to lead to useful insights? Is it surprising that trends are broadly the same to the data discussed? And finally it could be valuable to have a small addition of introspection from the authors on how this approach could be altered and/or improved in the future to facilitate the general application of this approach for combination therapies for other targets.

Reviewer #3 (Public review):

Summary:

The authors report that tracheal terminal cells (TTCs) in Drosophila do not activate innate immunity following bacterial infection. They attribute this to the lack of expression of PGRP-LCx in these cells. Forced activation of the Imd pathway in TTCs leads to cell death and a reduction in tracheal branching. The authors propose a mechanism for cell death induction via pathways involving JNK, AP-1, and foxo. They suggest that the suppression of innate immunity in TTCs may serve to maintain their plasticity, preparing them for responses to hypoxic conditions.

Strengths:

(1) The study addresses the understudied area of immune privilege in innate immunity, providing a potentially important example in Drosophila TTCs.

(2) The molecular characterization of the cell death pathway induced by forced Imd activation is well-executed and provides solid mechanistic insights.

(3) The authors draw interesting parallels between Drosophila TTCs and mammalian endothelial cells, suggesting broader implications for their findings.

Weaknesses:

(1) The core premise of the study - that TTCs do not activate innate immunity following bacterial infection - relies heavily on a single readout (Drs reporter). Additional markers of immune activation would strengthen this crucial claim.

(2) The evidence for the lack of PGRP-LCx expression in TTCs is based on a single GAL4 reporter line. Given the importance of this observation to the authors' model, validation using alternative methods would be beneficial.

(3) The phenotypes observed upon forced activation of the Imd pathway in TTCs, while intriguing, may be influenced by non-physiological levels of pathway activation. The authors should address this potential caveat and consider examining the effects of more moderate pathway activation.

Reviewer #3 (Public review):

Summary:

This is an interesting paper by Lechler and colleagues describing the transcriptomic signature and fate of intermediate cells (ICs), a transient and poorly defined embryonic cell type in the skin. ICs are the first suprabasal cells in the stratifying skin and unlike later-developing suprabasal cells, ICs continue to divide. Using bulk RNA seq to compare ICs to spinous and granular transcriptomes, the authors find that IC-specific gene signatures include hallmarks of granular cells, such as genes involved in lipid metabolism and skin barrier function that are not expressed in spinous cells. ICs were assumed to differentiate into spinous cells, but lineage tracing convincingly shows ICs differentiate directly into granular cells without passing through a spinous intermediate. Rather, basal cells give rise to the first spinous cells. They further show that transcripts associated with contractility are also shared signatures of ICs and granular cells, and overexpression of two contractility inducers (Spastin and ArhGEF-CA) can induce granular and repress spinous gene expression. This contractility-induced granular gene expression does not appear to be mediated by the mechanosensitive transcription factor, Yap. The paper also identifies new markers that distinguish IC and spinous layers and shows the spinous signature gene, MafB, is sufficient to repress proliferation when prematurely expressed in ICs.

Strengths:

Overall this is a well-executed study, and the data are clearly presented and the findings convincing. It provides an important contribution to the skin field by characterizing the features and fate of ICs, a much-understudied cell type, at high levels of spatial and transcriptomic detail. The conclusions challenge the assumption that ICs are spinous precursors through compelling lineage tracing data. The demonstration that differentiation can be induced by cell contractility is an intriguing finding and adds a growing list of examples where cell mechanics influence gene expression and differentiation.

Weaknesses:

A weakness of the study is an over-reliance on overexpression and sufficiency experiments to test the contributions of MafB, Yap, and contractility in differentiation. The inclusion of loss-of-function approaches would enable one to determine if, for example, contractility is required for the transition of ICs to granular fate, and whether MafB is required for spinous fate. Second, whether the induction of contractility-associated genes is accompanied by measurable changes in the physical properties or mechanics of the IC and granular layers is not directly shown. The inclusion of physical measurements would bolster the conclusion that mechanics lies upstream of differentiation.

Finally, whether the expression of granular-associated genes in ICs provides them with some sort of barrier function in the embryo is not addressed, so the role of ICs in epidermal development remains unclear. Although not essential to support the conclusions of this study, insights into the function of this transient cell layer would strengthen the overall impact.

Reviewer #3 (Public review):

Petty and Bruno ask whether activity in secondary thalamic nuclei depends on the behavioral relevance of stimulus modality. They recorded from POm and LP, but the weight of the paper is skewed toward POm. They use two cohorts of mice (N=11 and 12), recorded in both nuclei using multi-electrode arrays, while being trained to lick to either a tactile stimulus (air puff against whiskers, first cohort) or a visual stimulus (drifting grating, second cohort), and ignore the respective other. They find that both nuclei, while primarily responsive to their 'home' modality, are more responsive to the relevant modality (i.e. the modality predicting reward).

Strengths:

The paper asks an important question, it is timely and is very well executed. The behavioral method using a delayed lick index (excluding impulsive responses) is well worked out. Electrophysiology methods are state-of-the-art with information about spike quality in Fig. S1. The main result is novel and important, convincingly conveying the point that encoding of secondary thalamic nuclei is flexible and clearly includes aspects of the behavioral relevance of a stimulus. The paper explores the mapping of responses within POm, pointing to a complex functional structure, something that has been reported/suggested in earlier studies.

Weaknesses:

Coding: It does not become clear to which aspect of the task POm/LP are responding. There is a motor-related response (whisking, licking, pupil), which, however, after regressing it out leaves a remaining response that the authors speculate could be sensory.

Learning: The paper talks a lot about 'learning', although it is only indirectly addressed. The authors use two differently (over-)trained mice cohorts rather than studying e.g. a rule switch in one and the same mouse, which would allow to directly assess whether it is the same neurons that undergo rule-dependent encoding

Mapping: The authors present electrode tracks with marked selectivity indices of recordings in POm and LP. This is a great start, but to finally understand the functional composition of POm and LP, a more detailed and systematic mapping effort is needed in the future.

Frankreichs dritter nationaler Plan zur Klimaanpassung enthält 51 Maßnahmen. Sie gehen von 4° Erhitzung bis 2100 aus - in Frankreich die Vorgabe für alle offiziellen Dokumente zur „ökologischen Planung“. Viele Fachleute halten diese Einschätzung für zu optimistisch. Die meisten der Massnahmen sind wenig konkret und nicht mit einer Finanzierung unterlegt. Die besondere Vulnerabilität bestimmter Gruppen wird nicht berücksichtigt https://www.liberation.fr/environnement/climat/changement-climatique-un-nouveau-plan-national-dadaptation-au-regime-sec-20241025_E5E4GSMOBJEPVGEU3EGXEJBZRY/

Reviewer #3 (Public review):

Summary:

In this paper, Chikermane et al. leverage a large open dataset of intracranial recordings (sEEG or ECoG) to analyze resting state (eyes closed) oscillatory activity from a variety of human brain areas. The authors identify a dominant proportion of channels in which beta band activity (12-30Hz) is most prominent, and subsequently seek to relate this to anatomical connectivity data by using the sEEG/ECoG electrodes as seeds in a large set of MRI data from the human connectome project. This reveals separate regions and white matter tracts for alpha (primarily occipital) and beta (prefrontal cortex and basal ganglia) oscillations. Finally, using a third available dataset of PET imaging, the authors relate the parcellated signals to dopamine signaling as estimated by spatial uptake patterns of dopamine, and reveal a significant correlation between the functional connectivity maps and the dopamine reuptake maps, suggesting a functional relationship between the two.

Strengths:

Overall, I found the paper well justified, focused on an important topic and interesting. The authors' use of 3 different open datasets was creative and informative, and it significantly adds to our understanding of different oscillatory networks in the human brain, and their more elusive relation with neuromodulator signaling networks by adding to our knowledge of the association between beta oscillations and dopamine signaling. Even my main comments about the lack of a theta network analysis and discussion points are relatively minor, and I believe this paper is valuable and informative.

Weaknesses:

The analyses were adequate, and the authors cleverly leverage these different datasets to build an interesting story. The main aspect I found missing (in addition to some discussion items, see below) was an examination of the theta network. Theta oscillations have been involved in a number of cognitive processes including spatial navigation and memory, and have been proposed to have different potential originating brain regions, and it would be informative to see how their anatomical networks (e.g. as in Fig. 2) look like under the author's analyses.

The authors devote a significant portion of the discussion to relating their findings to a popular hypothesis for the function of beta oscillations, the maintenance of the "status quo", mostly in the context of motor control. As the authors acknowledge, given the static nature of the data and lack of behavior, this interpretation remains largely speculative and I found it a bit too far-reaching given the data shown in the paper. In contrast, I missed a more detailed discussion on the growing literature indicating a role for beta in mood (e.g. in Kirkby et al. 2018), especially given the apparent lack of hippocampal and amygdala involvement in the paper, which was surprising.

Reviewer #3 (Public review):

Summary:

This manuscript presents a series of experiments aimed at investigating orientation to polarized lunar skylight in a nocturnal ant, the first report of its kind that I am aware of.

Strengths:

The study was conducted carefully and is clearly explained here.

Comments on revised version:

The manuscript is much improved and will make an excellent contribution to the field.

Reviewer #3 (Public review):

Summary:

Loewinger et al. extend a previously described framework (Cui et al., 2021) to provide new methods for statistical analysis of fiber photometry data. The methodology combines functional regression with linear mixed models, allowing inference on complex study designs that are common in photometry studies. To demonstrate its utility, they reanalyze datasets from two recent fiber photometry studies into mesolimbic dopamine. Then, through simulation, they demonstrate the superiority of their approach compared to other common methods.

Strengths:

The statistical framework described provides a powerful way to analyze photometry data and potentially other similar signals. The provided package makes this methodology easy to implement and the extensively worked examples of reanalysis provide a useful guide to others on how to correctly specify models.

Modeling the entire trial (function regression) removes the need to choose appropriate summary statistics, removing the opportunity to introduce bias, for example in searching for optimal windows in which to calculate the AUC. This is demonstrated in the re-analysis of Jeong et al., 2022, in which the AUC measures presented masked important details about how the photometry signal was changing. There is an appropriate level of discussion of the interpretation of the reanalyzed data that highlights the pitfalls of other methods and the usefulness of their methods.

The authors' use of linear mixed methods, allows for the estimation of random effects, which are an important consideration given the repeated-measures design of most photometry studies.

The authors provide a useful guide for how to practically use and implement their methods in an easy-to-use package. These methods should have wide applicability to those who use photometry or similar methods. The development of this excellent open-source software is a great service to the wider neuroscience community.

Reviewer #3 (Public review):

Summary:

Tubert et al. investigate the mechanisms underlying the pause response in striatal cholinergic interneurons (SCINs). The authors demonstrate that optogenetic activation of thalamic axons in the striatum induces burst activity in SCINs, followed by a brief pause in firing. They show that the duration of this pause correlates with the number of elicited action potentials, suggesting a burst-dependent pause mechanism. The authors demonstrated this burst-dependent pause relied on Kv1 channels. The pause is blocked by an SKF81297 and partially by sulpiride and mecamylamine, implicating D1/D5 receptor involvement. The study also shows that the ZD7288 does not reduce the duration of the pause and that lesioning dopamine neurons abolishes this response, which can be restored by clozapine.

Weaknesses:

While this study presents an interesting mechanism for SCIN pausing after burst activity, there are several major concerns that should be addressed:

(1) Scope of the Mechanism:

It is important to clarify that the proposed mechanism may apply specifically to the pause in SCINs following burst activity. The manuscript does not provide clear evidence that this mechanism contributes to the pause response observed in behavioral animals. While the thalamus is crucial for SCIN pauses in behavioral contexts, the exact mechanism remains unclear. Activating thalamic input triggers burst activity in SCINs, leading to a subsequent pause, but this mechanism may not be generalizable across different scenarios. For instance, approximately half of TANs do not exhibit initial excitation but still pause during behavior, suggesting that the burst-dependent pause mechanism is unlikely to explain this phenomenon. Furthermore, in behavioral animals, the duration of the pause seems consistent, whereas the proposed mechanism suggests it depends on the prior burst, which is not aligned with in vivo observations. Additionally, many in vivo recordings show that the pause response is a reduction in firing rate, not complete silence, which the mechanism described here does not explain. Please address these in the manuscript.

(2) Terminology:

The use of "pause response" throughout the manuscript is misleading. The pause induced by thalamic input in brain slices is distinct from the pause observed in behavioral animals. Given the lack of a clear link between these two phenomena in the manuscript, it is essential to use more precise terminology throughout, including in the title, bullet points, and body of the manuscript.

(3) Kv1 Blocker Specificity:

It is unclear how the authors ruled out the possibility that the Kv1 blocker did not act directly on SCINs. Could there be an indirect effect contributing to the burst-dependent pause? Clarification on this point would strengthen the interpretation of the results.

(4) Role of D1 Receptors:

While it is well-established that activating thalamic input to SCINs triggers dopamine release, contributing to SCIN pausing (as shown in Figure 3), it would be helpful to assess the extent to which D1 receptors contribute to this burst-dependent pause. This could be achieved by applying the D1 agonist SKF81297 after blocking nAChRs and D2 receptors.

(5) Clozapine's Mechanism of Action:

The restoration of the burst-dependent pause by clozapine following dopamine neuron lesioning is interesting, but clozapine acts on multiple receptors beyond D1 and D5. Although it may be challenging to find a specific D5 antagonist or inverse agonist, it would be more accurate to state that clozapine restores the burst-dependent pause without conclusively attributing this effect to D5 receptors.

Reviewer #3 (Public review):

Summary:

The authors propose a method for estimation of the spatial spectra of cortical activity from irregularly sampled data and apply it to publicly available intracranial EEG data from human patients during a delayed free recall task. The authors' main findings are that the spatial spectra of cortical activity peak at low spatial frequencies and decrease with increasing spatial frequency. This is observed over a broad range of temporal frequencies (2-100 Hz).

Strengths:

A strength of the study is the type of data that is used. As pointed out by the authors, spatial spectra of cortical activity are difficult to estimate from non-invasive measurements (EEG and MEG) due to signal mixing and from commonly used intracranial measurements (i.e. electrocorticography or Utah arrays) due to their limited spatial extent. In contrast, iEEG measurements are easier to interpret than EEG/MEG measurements and typically have larger spatial coverage than Utah arrays. However, iEEG is irregularly sampled within the three-dimensional brain volume and this poses a methodological problem that the proposed method aims to address.

Weaknesses:

The used method for estimating spatial spectra from irregularly sampled data is weak in several respects.

First, the proposed method is ad hoc, whereas there exist well-developed (Fourier-based) methods for this. The authors don't clarify why no standard methods are used, nor do they carry out a comparative evaluation.

Second, the proposed method lacks a theoretical foundation and hinges on a qualitative resemblance between Fourier analysis and singular value decomposition.

Third, the proposed method is not thoroughly tested using simulated data. Hence it remains unclear how accurate the estimated power spectra actually are.

In addition, there are a number of technical issues and limitations that need to be addressed or clarified (see recommendations to the authors).

My assessment is that the conclusions are not completely supported by the analyses. What would convince me, is if the method is tested on simulated cortical activity in a more realistic set-up. I do believe, however, that if the authors can convincingly show that the estimated spatial spectra are accurate, the study will have an impact on the field. Regarding the methodology, I don't think that it will become a standard method in the field due to its ad hoc nature and well-developed alternatives.

Reviewer #3 (Public review):

Summary:

This is an important paper using a novel paradigm to examine how observation affects the social contagion of risk preferences. There is a lot of interest in the field about the mechanisms of social influence, and adding in the factor of whether observation also influences these contagion effects is intriguing.

Strengths:

(1) There is an impressive combination of a multi-stage behavioural task with computational modelling and neuroimaging.

(2) The analyses are well conducted and the sample size is reasonable.

Weaknesses:

(1) Anatomically it would be helpful to more explicitly distinguish between dmPFC and vmPFC. Particularly at the end of the introduction when mPFC and vmPFC are distinguished, as the vmPFC is in the mPFC.

(2) The authors' definition of ROIs could be elaborated on further. They suggest that peaks are selected from neurosynth for different terms, but were there not multiple peaks identified within a functional or anatomical brain area? This section could be strengthened by confirming with anatomical ROIs where available, such as the atlases here http://www.rbmars.dds.nl/lab/CBPatlases.html and the Harvard-Oxford atlases.

(3) How did the authors ensure there were enough trials to generate a reliable BOLD signal? The scanned part of the study seems relatively short.

(4) It would be helpful to add whether any brain areas survived whole-brain correction.

(5) There is a concern that mediation cannot be used to make causal inferences and much larger samples are needed to support claims of mediation. The authors should change the term mediation in order to not imply causality (they could talk about indirect effects instead) and highlight that the mediation analyses are exploratory as they would not be sufficiently powered (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC2843527/).

(6) The authors may want to speculate on lifespan differences in this susceptibility to risk preferences given recent evidence that older adults are relatively more susceptible to impulsive social influence (Zhu et al, 2024, comms psychology).

Reviewer #3 (Public review):

Summary:

This manuscript describes how antibiotics influence genetic stability and survival in Mycobacterium smegmatis. Prolonged treatment with first-line antibiotics did not significantly impact mutation rates. Instead, adaptation to these drugs appears to be mediated by upregulation of DNA repair enzymes. While this study offers robust data, findings remain correlative and fall short of providing mechanistic insights.

Strengths:

The strength of this study is the use of genome-wide approaches to address the specific question of whether or not mycobacteria induce mutagenic potential upon antibiotic exposure.

Comments on revised version:

The authors responded adequately to my comments, and I have no further suggestions for the revised manuscript.

Reviewer #3 (Public review):

Summary:

This manuscript by Mac et al addresses the causes of pituitary dysfunction in patients with DAVID syndrome which is caused by mutations in the NFKB2 gene and leads to ACTH deficiency. The authors seek to determine whether the mutation directly leads to altered pituitary development, as opposed to an autoimmune defect, by using mutating human iPSCs and then establishing organoids that differentiate into pituitary tissue. They first seek to validate the system using a well-characterised mutation of the transcription factor TBX19, which also results in ACTH deficiency in patients. Then they characterise altered pituitary cell differentiation in mutant NFKB2 organoids and show that these lack corticotrophs, which would lead to ACTH deficiency. Importantly, the findings here suggest the effects of mutant NFKB2 on pituitary organoid differentiation are direct and not a result of altered noncanonical NF-κB signalling, which has been shown to be a mechanism leading to immunodeficiency in DAVID patients.

Strengths:

The conclusion of the paper that ACTH deficiency in DAVID syndrome is independent of an autoimmune input is strong.

Weaknesses:

(1) The authors correctly emphasise the importance of establishing the validity of an iPSC-based model in being able to recapitulate in vivo dysfunctional pituitary development through characterisation of a TBX19 knock-in mutation. Whilst this leads to the expected failure of functional corticotroph differentiation, other aspects of the normal pituitary differentiation pathway upstream of cortocotroph commitment seem to have been affected in surprising ways. In particular, the loss of LHX3 and PITX1 in TBX19 mutant organoids compared with wild type requires explanation, especially as the mutant protein would only be expected to be expressed in a small proportion of anterior pituitary lineage cells. This may identify a difference between human and mouse pituitary development and emphasises the importance of further establishing the developmental programme in human pituitary.

(2) It is notable that the manipulation of iPSC cells used to generate mutants through CRISPR/Cas9 editing is not applied to the control iPSC line. It is possible that these manipulations, including electroporation and puromycin selection may lead to changes to the iPSC cells that is independent of the mutations introduced and this may change the phenotype of the cells. The authors have established that there are no off-target mutations through whole genome sequencing but the iPSC manipulation could have led to changes through epigenetic mechanisms or through non-genomic alterations of developmental potential. A better control in all experiments would have been an iPSC line with a benign knock-in (such as GFP into the ROSA26 locus) or use of a selected line where editing failed. The authors also ackowledge that use of a single clone is not ideal in these studies and characterisation of multiple clones would strengthen the conclusions of the study.

Reviewer #3 (Public review):

The authors convincingly show that SLC35G1 mediates uptake of citrate which is dependent on pH and chloride concentration. Putting their initial findings in a physiological context, they present human tissue expression data of SLC35G. Their Transwell assay indicates that SLC35G1 is a citrate exporter at the basolateral membrane.

Weaknesses:

The manuscript would benefit from the inclusion of the antibody validation results. Related to the localization of SLC35G1, the polyclonal antibody was not validated in the knockdown cells used in the study. This would strengthen the antibody validation, the localization results as well as the transport assay in 2C.

Also, it is unclear why the Transwell assay was not performed upon knockdown of SLC35G1 to support the conclusions.

Reviewer #3 (Public review):

Summary:

The authors used the model organism Drosophila melanogaster to show that the neurotrophin Toll-6 and its ligands, DNT-2 and kek-6, play a role in maintaining the number of dopaminergic neurons and modulating their synaptic connectivity. This supports previous findings on the structural plasticity of dopaminergic neurons and suggests a molecular mechanism underlying this plasticity.

Strengths:

The experiments are overall very well designed and conclusive. Methods are in general state-of-the-art, the sample sizes are sufficient, the statistical analyses are sound, and all necessary controls are in place. The data interpretation is straightforward, and the relevant literature is taken into consideration. Overall, the manuscript is solid and presents novel, interesting, and important findings.

Weaknesses:

There are three technical weaknesses that could perhaps be improved.

First, the model of reciprocal, inhibitory feedback loops (Figure 2F) is speculative. On the one hand, glutamate can act in flies as an excitatory or inhibitory transmitter (line 157), and either situation can be the case here. On the other hand, it is not clear how an increase or decrease in cAMP level translates into transmitter release. One can only conclude that two types of neurons potentially influence each other.

Second, the quantification of bouton volumes (no y-axis label in Figure 5 C and D!) and dendrite complexity are not convincingly laid out. Here, the reader expects fine-grained anatomical characterizations of the structures under investigation, and a method to precisely quantify the lengths and branching patterns of individual dendritic arborizations as well as the volume of individual axonal boutons.

Third, Figure 1C shows two neurons with the goal of demonstrating between-neuron variability. It is not convincingly demonstrated that the two neurons are actually of the very same type of neuron in different flies or two completely different neurons.

Reviewer #3 (Public review):

Summary:

This manuscript reports a role for the mitochondrial calcium uniporter gene (mcu-1) in regulating associative learning behavior in C. elegans. This regulation occurs by mcu-1-dependent secretion of the neuropeptide NLP-1 from the sensory neuron AWC. The authors report a post-developmental role for mcu-1 in AWC to promote learning. The authors further show that odor conditioning leads to increases in NLP-1 secretion from AWC, and that interfering with mcu-1 function reduces NLP-1 secretion. Finally, the authors show that NLP-1 secretion increases when ROS levels in AWC are genetically or pharmacologically elevated. The authors propose that mitochondrial calcium entry through MCU-1 in response to odor conditioning leads to the generation of ROS and the subsequent increase in neuropeptide secretion to promote conditioned behavior.

Strengths:

(1) The authors show convincingly that genetically or pharmacologically manipulating MCU function impacts chemotaxis in a conditioned learning paradigm.

(2) The demonstration that the secretion of a specific neuropeptide can be up-regulated by MCU, ROS and odor conditioning is an important and interesting advance that addresses mechanisms by which neuropeptide secretion can be regulated in vivo.

Weaknesses:

(1) The authors conclusion that mcu-1 functions in the AWC-on neuron is not adequately supported by their rescue experiments. The promoter they use for rescue drives expression in a number of additional neurons including AWC-on, that themselves are implicated in adaptation, leaving open the possibility that mcu-1 may function non-autonomously instead of autonomously in AWC to regulate this behavior.

(2) The authors conclude MCU promotes neuropeptide release from AWC by controlling calcium entry into mitochondria, but they did not directly examine the effects of altered MCU function on calcium dynamics either in mitochondria or in the soma, even though they conducted calcium imaging experiments in AWC of wild type animals. Examination of calcium entry in mitochondria would be a direct test of their model.

(3) The authors' conclusion that mitochondrial-derived ROS produced by MCU activation drives neuropeptide release does not appear to be experimentally supported. A major weakness of this paper is that experiments addressing whether mcu-1 activity indeed produces ROS are not included, leaving unanswered the question of whether MCU is the endogenous source of ROS that drives neuropeptide secretion.

Reviewer #3 (Public review):

The authors use a generic model framework to study the emergence of habituation and its functional role from information-theoretic and energetic perspectives. Their model features a receptor, readout molecules, and a storage unit, and as such, can be applied to a wide range of biological systems. Through theoretical studies, the authors find that habituation (reduction in average activity) upon exposure to repeated stimuli should occur at intermediate degrees to achieve maximal information gain. Parameter regimes that enable these properties also result in low dissipation, suggesting that intermediate habituation is advantageous both energetically and for the purpose of retaining information about the environment.

A major strength of the work is the generality of the studied model. The presence of three units (receptor, readout, storage) operating at different time scales and executing negative feedback can be found in many domains of biology, with representative examples well discussed by the authors (e.g. Figure 1b). A key takeaway demonstrated by the authors that has wide relevance is that large information gain and large habituation cannot be attained simultaneously. When energetic considerations are accounted for, large information gain and intermediate habituation appear to be a favorable combination.

While the generic approach of coarse-graining most biological detail is appealing and the results are of broad relevance, some aspects of the conducted studies, the problem setup, and the writing lack clarity and should be addressed:

(1) The abstract can be further sharpened. Specifically, the "functional role" mentioned at the end can be made more explicit, as it was done in the second-to-last paragraph of the Introduction section ("its functional advantages in terms of information gain and energy dissipation"). In addition, the abstract mentions the testing against experimental measurements of neural responses but does not specify the main takeaways. I suggest the authors briefly describe the main conclusions of their experimental study in the abstract.

(2) Several clarifications are needed on the treatment of energy dissipation.<br /> - When substituting the rates in Eq. (1) into the definition of δQ_R above Eq. (10), "σ" does not appear on the right-hand side. Does this mean that one of the rates in the lower pathway must include σ in its definition? Please clarify.<br /> - I understand that the production of storage molecules has an associated cost σ and hence contributes to dissipation. The dependence of receptor dissipation on , however, is not fully clear. If the environment were static and the memory block was absent, the term with would still contribute to dissipation. What would be the nature of this dissipation?<br /> - Similarly, in Eq. (9) the authors use the ratio of the rates Γ_{s → s+1} and Γ_{s+1 → s} in their expression for internal dissipation. The first-rate corresponds to the synthesis reaction of memory molecules, while the second corresponds to a degradation reaction. Since the second reaction is not the microscopic reverse of the first, what would be the physical interpretation of the log of their ratio? Since the authors already use σ as the energy cost per storage unit, why not use σ times the rate of producing S as a metric for the dissipation rate?

(3) Impact of the pre-stimulus state. The plots in Figure 2 suggest that the environment was static before the application of repeated stimuli. Can the authors comment on the impact of the pre-stimulus state on the degree of habituation and its optimality properties? Specifically, would the conclusions stay the same if the prior environment had stochastic but aperiodic dynamics?

(4) Clarification about the memory requirement for habituation. Figure 4 and the associated section argue for the essential role that the storage mechanism plays in habituation. Indeed, Figure 4a shows that the degree of habituation decreases with decreasing memory. The graph also shows that in the limit of vanishingly small Δ⟨S⟩, the system can still exhibit a finite degree of habituation. Can the authors explain this limiting behavior; specifically, why does habituation not vanish in the limit Δ⟨S⟩ -> 0?

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

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

One of the major advances in this article is the development of the laser ablation model for 'mild' retinal damage as an alternative to the more severe neovascularization models. While not directly shown in the article, this model would potentially allow for controlling the size, depth, and severity of the laser injury opening interesting avenues for future study.

Weaknesses:

(1) It is unclear based on the current data/study to what extent the mild laser damage phenotype is generalizable to disease phenotypes. The outer nuclear cell loss of 28% and a complete recovery in 2 months would seem quite mild, thus the generalizability in terms of immune-mediated response in the face of retinal remodeling is not certain, specifically whether the key finding regarding the lack of neutrophil recruitment will be maintained with a stronger laser ablation.

(2) Mice numbers and associated statistics are insufficient to draw strong conclusions in the paper on the activity of neutrophils, some examples are below :

a) 2 catchup mice and 2 positive control EAU mice are used to draw inferences about immune-mediated activity in response to injury. If the goal was to show 'feasibility' of imaging these mouse models for the purposes of tracking specific cell type behavior, the case is sufficiently made and already published by the authors earlier. It is possible that a larger sample size would alter the conclusion.

b) There are only 2 examples of extravasated neutrophils in the entire article, shown in the positive control EAU model. With the rare extravasation events of these cells and their high-speed motility, the chance of observing their exit from the vasculature is likely low overall, therefore the general conclusions made about their recruitment or lack thereof are not justified by these limited examples shown.

c) In Figure 3, the 3-day time point post laser injury shows an 18% reduction in the density of ONL nuclei (p-value of 0.17 compared to baseline). In the case of neutrophils, it is noted that "Control locations (n = 2 mice, 4 z-stacks) had 15 {plus minus} 8 neutrophils per sq.mm of retina whereas lesioned locations (n = 2 mice, 4 z-stacks) had 23 {plus minus} 5 neutrophils per sq.mm of retina (Figure 10b). The difference between control and lesioned groups was not statistically significant (p = 0.19)." These data both come from histology. While the p-values - 0.17 and 0.19 - are similar, in the first case a reduction in ONL cell density is concluded while in the latter, no difference in neutrophil density is inferred in the lesioned case compared to control. Why is there a difference in the interpretation where the same statistical test and methodology are used in both cases? Besides this statistical nuance, is there an alternate possibility that there is an increased, albeit statistically insignificant, concentration of circulating neutrophils in the lesioned model? The increase is nearly 50% (15 {plus minus} 8 vs. 23 {plus minus} 5 neutrophils per sq.mm) and the reader may wonder if a larger animal number might skew the statistic towards significance.

(2) The conclusions on the relative activity of neutrophils and microglia come from separate animals. The reader may wonder why simultaneous imaging of microglia and neutrophils is not shown in either the EAU mice or the fluorescently labeled catchup mice where the non-labeled cell type could possibly be imaged with phase-contrast as has been shown by the authors previously. One might suspect that the microglia dynamics are not substantially altered in these mice compared to the CX3CR1-GFP mice subjected to laser lesions, but for future applicability of this paradigm of in vivo imaging assessment of the laser damage model, including documenting the repeatability of the laser damage model and the immune cell behavior, acquiring these data in the same animals would be critical.

(3) Along the same lines as above, the phase contrast ONL images at time points from 3-day to 2-month post laser injury are not shown and the absence of this data is not addressed. This missing data pertains only to the in vivo imaging mice model but are conducted in histology that adequately conveys the time-course of cell loss in the ONL. It is suggested that the reason be elaborated for the exclusion of this data and the simultaneous imaging of microglia and neutrophils mentioned above. Also, it would be valuable to further qualify and check the claims in the Discussion that "ex vivo analysis confirms in vivo findings" and "Microglial/neutrophil discrimination using label-free phase contrast"

Reviewer #3 (Public review):

Summary:

The paper by Kim et al utilizes smFISH method to probe for six genes to understand the spatial distribution of the mRNAs in dendrites and identify the spatial relationships between the transcripts. While they have delved into a high-resolution characterization of the dendritic transcripts and compared their data with existing datasets, the analysis needs more robustness, and therefore the findings are inconclusive. The rationale of the study and choosing these genes is not clear - it appears more like a validation of some of the datasets without much biological significance.

Overall, several conclusions for spatial distribution of dendritic RNAs were based on correlations and it is difficult to understand whether this represents a true biological phenomenon or if it is an artifact of the imaging and morphological heterogeneity of neurons and difficulties in dendritic segmentation.

Strengths:

The authors have performed an extensive analysis of the smFISH datasets and quantified the precise localization patterns of the dendritic mRNAs in relation to the dendritic morphology. Their images and the analysis pipeline can be a resource for the community.

Weaknesses:

(1) The authors have attempted to identify general patterns of mRNA distribution as a function of distance, proximal vs distal, however, in many of the cases the results are a bit redundant and the size of the neurons or the length of the dendrites or image segmentation artifacts turn out to be the determining factors. A better method to normalize the morphological differences is needed to make meaningful conclusions about RNA distribution patterns.

(2) Another concerning factor is that there are many redundancies throughout the paper. For example, to begin with, all analysis should have been done as RNA density measurements (and not absolute numbers of mRNAs) and with proper normalization and accounting for differences in length. Some of these were done only in the latter half of the paper, for example in Figure 4.

(3) Images for the smFISH are missing. It is important to show the actual images, and the quality of the images is a crucial factor for all subsequent analyses.

(4) The parameters used for co-localization analysis are very relaxed (2 - 6 microns), particularly the distances of interactions far exceed feasible interactions between the biomolecules. Typically, transport granules are significantly smaller than the length scales used.

Reviewer #3 (Public review):

Summary:

In this study, the authors perform a meta-analysis of existing transcriptomic data describing the responses of cells in the mouse spinal cord to traumatic injury (SCI). They identify two subclasses of microglia, which they term 'innate' and 'reactive' microglia, in the dataset, with the majority of microglia in the uninjured spinal cord being 'innate' and the majority of microglia in the injured region being 'reactive'. The authors propose that, during injury, the population of innate microglia is depleted and replaced by the population of reactive microglia. Using DEG and gene ontology pipelines, the authors suggest that TGF signaling is a positive force that helps recruit healthy microglia to enhance recovery in the context of SCI. In contrast, the microglial phagocytic receptor Trem2 contributes to neuroinflammation and neuronal death. Finally, the authors suggest replacing reactive microglia with innate microglia as a potential therapeutic approach to treat SCI in humans.

Strengths:

The work utilizes numerous and multi-modal datasets describing transcriptomic changes in the mouse CNS following SCI.

The topic is translationally relevant.

Weaknesses:

There is not enough information about how each of the datasets re-analyzed by the authors was obtained and processed both by the group generating the data and by the group re-analyzing it.

The conclusions drawn by the authors are not sufficiently supported by the evidence.

Whether the study represents a significant conceptual advance in our understanding of microglial contributions to SCI is not clear.

My specific concerns and suggestions to address these weaknesses are provided below.

Major comments:

(1) Questions remain about the nature, quality, and features of the datasets re-analyzed in the study. For example, how were these datasets obtained? Were the same animal models and time points used in each? What modality of RNA sequencing was done? What criteria did the authors consider in deciding which datasets to include in the study? Since the study is entirely reliant on data generated elsewhere, a more thorough description of these datasets within the text is needed.

(2) Relatedly, the authors chose to filter out some cells from the datasets based on quality, but this information is incomplete. For example, the authors omit cells with 10% mitochondrial genes, but this value is higher than most investigators use (typically between 1%-5%). Why is 10% the appropriate limit in this particular study? Further, how did the authors ensure the removal of doublets from the dataset?

(3) A principal finding of the paper is that microglia in the uninjured CNS mostly have an 'innate' transcriptomic phenotype, while microglia in the injured CNS mostly have a 'reactive' phenotype. However, there are some issues here that require further discussion. First, while historically microglia were thought to possess distinct 'homeostatic' versus 'activated' profiles which would be consistent with the authors' interpretations here, these differences are now thought of more as changes in a given microglial cell's transcriptomic status. Thus, while the authors interpret their results as meaning that innate microglia are depleted and replaced by a different set of reactive microglia following SCI (or at least this is how the paper is written), it is equally if not more likely that the microglia within the injured regions themselves become more reactive as a result of the insult. The authors should clarify why their interpretation is more likely to be correct.

(4) Related to the above point, the authors base the manuscript on the idea that microglia are mostly 'innate' in the uninjured CNS and 'reactive' after injury, however, the UMAP plots in Figures 1A and 1C suggest that both classes of microglia cluster together and may not actually represent distinct subclasses. Have the authors tried sub-clustering just the myeloid clusters and seeing how well they separate? Even if they do technically represent distinct clusters, the UMAP could be interpreted to mean that their transcriptomic differences are not particularly robust.

(5) I appreciate the authors' use of loss-of-function data to explore the roles of microglial TGF and Trem2 signaling to glean some mechanistic insights into SCI. However, many of the conclusions reached by the authors in the manuscript are insufficiently supported by the data and would require additional experiments to rigorously confirm. A couple of examples are the following:<br /> 5a. Lines 160-162: "Hence, we conclude that the cascade of injury events in SCI significantly influences microglia, leading to the replacement of innate microglial cells by reactive microglia." That SCI influences microglia is well-supported by the study, but whether reactive microglia replace innate microglia, versus whether innate microglia in the region transition to a reactive state, needs to be tested experimentally.<br /> 5b. Lines 321-323: "Taken together, iPSC-derived microglia have the potential to replace the functions of naïve microglial cells, and they perform even more effectively in the in vivo CNS." Again, the first part of the sentence is supported, but whether iPSCs are more effective than other populations in vivo would need to be tested experimentally.

(6) As microglia have long been appreciated as contributors to the CNS injury response, the conceptual advance here isn't particularly clear to me. For example, Gao et al, 2023 (*cited by the authors) describe the role of Trem2+ microglia in SCI versus demyelinating disease with major conceptual overlap with the current study. It would be helpful for the authors to include a discussion of what we now know about SCI based on this study that we did not know (or strongly suspect) before.

Reviewer #3 (Public review):

Summary:

To understand the specificity of age-dependent changes in the human neocortex, this paper investigated the electrophysiological and morphological characteristics of pyramidal cells in a wide age range from infants to the elderly.

The results show that some electrophysiological characteristics change with age, particularly in early childhood. In contrast, the larger morphological structures, such as the spatial extent and branching frequency of dendrites, remained largely stable from infancy to old age. On the other hand, the shape of dendritic spines is considered immature in infancy, i.e., the proportion of mushroom-shaped spines increases with age.

Strengths:

Whole-cell recordings and intracellular staining of pyramidal cells in defined areas of the human neocortex allowed the authors to compare quantitative parameters of electrophysiological and morphological properties between finely divided age groups.

They succeeded in finding symmetrical changes specific to both infants and the elderly, and asymmetrical changes specific to either infants or the elderly. The similarity of pyramidal cell characteristics between areas is unexpected.

Weaknesses:

Human L2/3 pyramidal cells are thought to be heterogeneous, as L2/3 has expanded to a high degree during the evolution from rodents to humans. However, the diversity (subtyping) is not revealed in this paper.

Reviewer #3 (Public review):

Mäkelä et al. here investigate genome concentration as a limiting factor on growth. Previous work has identified key roles for transcription (RNA polymerase) and translation (ribosomes) as limiting factors on growth, which enable an exponential increase in cell mass. While a potential limiting role of genome concentration under certain conditions has been explored theoretically, Mäkelä et al. here present direct evidence that when replication is inhibited, genome concentration emerges as a limiting factor.

A major strength of this paper is the diligent and compelling combination of experiment and modeling used to address this core question. The use of origin- and ftsZ-targeted CRISPRi is a very nice approach that enables dissection of the specific effects of limiting genome dosage in the context of a growing cytoplasm. While it might be expected that genome concentration eventually becomes a limiting factor, what is surprising and novel here is that this happens very rapidly, with growth transitioning even for cells within the normal length distribution for E. coli. Fundamentally, it demonstrates the fine balance of bacterial physiology, where the concentration of the genome itself (at least under rapid growth conditions) is no higher than it needs to be. A further surprising finding of this study is that susceptibility to this genome-limiting effect is felt differently by different genes, with unstable transcripts more affected and rRNA and many essential genes being more robust to it.

It should be noted that the authors do not identify a "smoking gun" - a gene or small number of genes that mediate the effects of genome concentration-dependent growth limitation. However, what they do achieve is to develop plausible criteria for identifying such a gene - through investigating essential genes that decrease in their abundance more rapidly than others.

Overall, this study provides a fundamental contribution to bacterial physiology by illuminating the relationship between DNA, mRNA, and protein in determining growth rate. While coarse-grained, the work invites exciting questions about how the composition of major cellular components is fine-tuned to a cell's needs and which specific gene products mediate this connection. The work also suggests the presence of buffering mechanisms that allow essential proteins such as RNA polymerase to be robust to fluctuations in genome concentration, which is an exciting area for future exploration. This work has implications not only for biotechnology, as the authors discuss, but potentially also for our understanding of how DNA-targeted antibiotics limit bacterial growth.

Comments on revised version:

Nothing left to add - the authors did a fantastic job addressing my points. In some ways doing so opened up even more interesting questions, but I happily accept that those are best left to future investigations.

Reviewer #3 (Public review):

Summary:

In this study, Li et al. identified CAD96CA and FGF1 among 20 receptor tyrosine kinase receptors as mediators of JH signaling. By performing a screen in HaEpi cells with overactivated JH signaling, the authors pinpointed two main RTKs that contribute to the transduction of JH. Using the CRISPR/Cas9 system to generate mutants, the authors confirmed that these RTKs are required for normal JH activation, as precocious pupariation was observed in their absence. Additionally, the authors demonstrated that both CAD96CA and FGF1 exhibit a high affinity for JH, and their activation is necessary for the proper phosphorylation of Tai and Met, transcription factors that promote the transcriptional response. Finally, the authors provided evidence suggesting that the function of CAD96CA and FGF1 as JH receptors is conserved across insects.

Strengths:

The data provided by the authors are convincing and support the main conclusions of the study, providing ample evidence to demonstrate that phosphorylation of the transducers Met and Tai mainly depends on the activity of two RTKs. Additionally, the binding assays conducted by the authors support the function of CAD96CA and FGF1 as membrane receptors of JH. The study's results validate, at least in H. amigera, the predicted existence of membrane receptors for JH.

Weaknesses:

The authors have provided evidences that the Cad96Ca and FGF1 RTK receptors contribute to JH signaling through CRISPR/Cas9, inducing precocious metamorphosis, although not to the same extent as absence of JH. Therefore, it still remains unclear whether these RTKs are completely required for pathway activation or only necessary for high activation levels during the last larval stage.

While the authors have included some additional data, the mechanism by which different RTKs function in transducing JH signaling in a tissue specific manner is still unclear. As the authors note in the discussion, it is possible that other RTKs may also play a role in facilitating the transduction of JH signaling.

Lastly, the study does not yet explain how RTKs with known ligands could also bind JH and contribute to JH signaling activation. Although receptor promiscuity has been suggested as a possible mechanism, future studies could explore whether activation of RTK pathways by their known ligands induces certain levels of JH transducer phosphorylation, which, in the presence of JH, could contribute to full pathway activation without the need for direct JH-RTK binding.

Reviewer #3 (Public review):

The work extends earlier studies on the Drosophila Id protein EMC to uncover a potential pathway that explains several tissue-scale developmental abnormalities in emc mutants. It also describes a non-apoptotic role for caspases in cell biology.

Strengths:

The work adds to an emerging new set of functions for caspases beyond their canonical roles as cell death mediators. This novelty is a major strength as well as its reliance on genetic-based in vivo study. The study will be of interest to those who are curious about caspases in general.

Weaknesses:

The authors did an adequate job in dealing with the limitations of the reviewed preprint. Although they could have done more, they chose not to for reasons they adequately defended.

Reviewer #3 (Public review):

The authors aimed to improve single-nucleus RNA sequencing (snRNA-seq) to address current limitations and challenges with nuclei and RNA isolation quality. They successfully developed a protocol that enhances RNA preservation and yields high-quality snRNA-seq data from multiple tissues, including a challenging model of adipose tissue. They then applied this method to eWAT and iWAT from mice fed either a normal or high-fat diet, exploring depot-specific cellular dynamics and gene expression changes during obesity. Their analysis included subclustering of SVF cells and revealed that obesity promotes a transition in APCs from an early to a committed state and induces a pro-inflammatory phenotype in immune cells, particularly in eWAT. In addition to SVF cells, they discovered six adipocyte subpopulations characterized by a gradient of unique gene expression signatures. Interestingly, a novel subpopulation, termed Ad6, comprised stressed and dying adipocytes with reduced transcriptional activity, primarily found in eWAT of mice on a high-fat diet. Overall, the methodology is sound, and the data presented supports the conclusions drawn. Further research based on these findings could pave the way for potential novel interventions in obesity and metabolic disorders, or for similar studies in other tissues or conditions.

Strengths:

The authors have presented a compelling set of results. They have compared their data with two previously published datasets and provide novel insight into the biological processes underlying mouse adipose tissue remodeling during obesity. The results are generally consistent and robust. The revised Discussion is comprehensive and puts the work in the context of the field.

Weaknesses:

• The adipose tissues were collected after 10 weeks of high-fat diet treatment, lacking the intermediate time points for identifying early markers or cell populations during the transition from healthy to pathological adipose tissue.<br /> • The expansion of the Ad6 subpopulation in obese iWAT and gWAT is interesting. The author claims that Ad6 exhibited a substantial increase in eWAT and a moderate rise in iWAT (Figure 4C). However, this adipocyte subpopulation remains the most altered in iWAT upon obesity. Could the authors elaborate on why there is a scarcity of adipocytes with ROS reporter and B2M in obese iWAT?<br /> • While the study provides extensive data on mouse models, the potential translation of these findings to human obesity remains uncertain.

Revised version: The authors have properly revised the paper in response to the above questions, and I have no other concerns.

Reviewer #3 (Public review):

Summary:

In this manuscript, Bosch and colleagues describe an unexpected function of Flamingo, a core component of the planar cell polarity pathway, in cell competition in Drosophila wing and eye disc. While Flamingo depletion has no impact on tumour growth (upon induction of Ras and depletion of Scribble throughout the eye disc), and no impact when depleted in WT cells, it specifically tunes down winner clone expansion in various genetic contexts, including the overexpression of Myc, the combination of Scribble depletion with activation of Ras in clones or the early clonal depletion of Scribble in eye disc. Flamingo depletion reduces proliferation rate and increases the rate of apoptosis in the winner clones, hence reducing their competitiveness up to forcing their full elimination (hence becoming now "loser"). This function of Flamingo in cell competition is specific of Flamingo as it cannot be recapitulated with other components of the PCP pathway, does not rely on interaction of Flamingo in trans, nor on the presence of its cadherin domain. Thus, this function is likely to rely on a non-canonical function of Flamingo which may rely on downstream GPCR signaling.

This unexpected function of Flamingo is by itself very interesting. In the framework of cell competition, these results are also important as they describe, to my knowledge, one of the only genetic conditions that specifically affect the winner cells without any impact when depleted in the loser cells. Moreover, Flamingo do not just suppress the competitive advantage of winner clones, but even turn them in putative losers. This specificity, while not clearly understood at this stage, opens a lot of exciting mechanistic questions, but also a very interesting long term avenue for therapeutic purpose as targeting Flamingo should then affect very specifically the putative winner/oncogenic clones without any impact in WT cells.

The data and the demonstration are very clean and compelling, with all the appropriate controls, proper quantifications and backed-up by observations in various tissues and genetic backgrounds. I don't see any weakness in the demonstration and all the points raised and claimed by the authors are all very well substantiated by the data. As such, I don't have any suggestions to reinforce the demonstration.

While not necessary for the demonstration, documenting the subcellular localisation and levels of Flamingo in these different competition scenarios may have been relevant and provide some hints on a putative mechanism (specifically by comparing its localisation in winner and loser cells).

Also, on a more interpretative note, the absence of impact of Flamingo depletion on JNK activation does not exclude some interesting genetic interactions. JNK output can be very contextual (for instance depending on Hippo pathway status), and it would be interesting in the future to check if Flamingo depletion could somehow alter the effect of JNK in the winner cells and promote downstream activation of apoptosis (which might normally be suppressed). It would be interesting to check if Flamingo depletion could have an impact in other contexts involving JNK activation or upon mild activation of JNK in clones.

Strengths:

- A clean and compelling demonstration of the function of Flamingo in winner cells during cell competition

- One of the rare genetic conditions that affects very specifically winner cells without any impact in losers, and then can completely switch the outcome of competition (which opens an interesting therapeutic perspective on the long term)

Weaknesses:

- The mechanistic understanding obviously remains quite limited at this stage especially since the signaling does not go through the PCP pathway.

Reviewer #3 (Public review):

Summary:

Boffi and colleagues sought to quantify the single-trial, azimuthal information in the dorsal cortex of the inferior colliculus (DCIC), a relatively understudied subnucleus of the auditory midbrain. They accomplished this by using two complementary recording methods while mice passively listened to sounds at different locations: calcium imaging that recorded large neuronal populations but with poor temporal precision and multi-contact electrode arrays that recorded smaller neuronal populations with exact temporal precision. DCIC neurons respond variably, with inconsistent activity to sound onset and complex azimuthal tuning. Some of this variably was explained by ongoing head movements. The authors used a naïve Bayes decoder to probe the azimuthal information contained in the response of DCIC neurons on single trials. The decoder failed to classify sound location better than chance when using the raw population responses but performed significantly better than chance when using the top principal components of the population. Units with the most azimuthal tuning were distributed throughout the DCIC, possessed contralateral bias, and positively correlated responses. Interestingly, inter-trial shuffling decreased decoding performance, indicating that noise correlations contributed to decoder performance. Overall, Boffi and colleagues, quantified the azimuthal information available in the DCIC while mice passively listened to sounds, a first step in evaluating if and how the DCIC could contribute to sound localization.

Strengths:

The authors should be commended for collection of this dataset. When done in isolation (which is typical), calcium imaging and linear array recordings have intrinsic weaknesses. However, those weaknesses are alleviated when done in conjunction - especially when the data is consistent. This data set is extremely rich and will be of use for those interested in auditory midbrain responses to variable sound locations, correlations with head movements, and neural coding.

The DCIC neural responses are complex with variable responses to sound onset, complex azimuthal tuning and large inter-sound interval responses. Nonetheless, the authors do a decent job in wrangling these complex responses: finding non-canonical ways of determining dependence on azimuth and using interpretable decoders to extract information from the population.

Weaknesses:

The decoding results are a bit strange, likely because the population response is quite noisy on any given trial. Raw population responses failed to provide sufficient information concerning azimuth for significant decoding. Importantly, the decoder performed better than chance when certain principal components or top ranked units contributed but did not saturate with the addition of components or top ranked units. So, although there is azimuthal information in the recorded DCIC populations - azimuthal information appears somewhat difficult to extract.

Although necessary given the challenges associated with sampling many conditions with technically difficult recording methods, the limited number of stimulus repeats precludes interpretable characterization of the heterogeneity across the population. Nevertheless, the dataset is public so those interested can explore the diversity of the responses.

The observations from Boffi and colleagues raises the question: what drives neurons in the DCIC to respond? Sound azimuth appears to be a small aspect of the DCIC response. For example, the first 20 principal components which explain roughly 80% of the response variance are insufficient input for the decoder to predict sound azimuth above chance. Furthermore, snout and ear movements correlate with the population response in the DCIC (the ear movements are particularly peculiar given they seem to predict sound presentation). Other movements may be of particular interest to control for (e.g. eye movements are known to interact with IC responses in the primate). These observations, along with reported variance to sound onsets and inter-sound intervals, question the impact of azimuthal information emerging from DCIC responses. This is certainly out of scope for any one singular study to answer, but, hopefully, future work will elucidate the dominant signals in the DCIC population. It may be intuitive that engagement in a sound localization task may push azimuthal signals to the forefront of DCIC response, but azimuthal information could also easily be overtaken by other signals (e.g. movement, learning).

Boffi and colleagues set out to parse the azimuthal information available in the DCIC on a single trial. They largely accomplish this goal and are able to extract this information when allowing the units that contain more information about sound location to contribute to their decoding (e.g., through PCA or decoding on their activity specifically). Interestingly, they also found that positive noise correlations between units with similar azimuthal preferences facilitate this decoding - which is unusual given that this is typically thought to limit information. The dataset will be of value to those interested in the DCIC and to anyone interested in the role of noise correlations in population coding. Although this work is first step into parsing the information available in the DCIC, it remains difficult to interpret if/how this azimuthal information is used in localization behaviors of engaged mice.

Reviewer #3 (Public review):

Summary:

In their manuscript entitled Kong and colleagues investigate the role of distinct populations of neurons in the central amygdala (CeA) in encoding valence and salience during both appetitive and aversive conditioning. The study expands on the work of Yang et al. (2023), which specifically focused on somatostatin (SST) neurons of the CeA. Thus, this study broadens the scope to other neuronal subtypes, demonstrating that CeA neurons in general are predominantly tuned to valence representations rather than salience.

Strengths:

One of the key strengths of the study is its rigorous quantitative approach based on the "circular-shift method", which carefully assesses correlations between neural activity and behavior-related variables. The authors' findings that neuronal responses to the unconditioned stimulus (US) change with learning are consistent with previous studies (Yang et al., 2023). They also show that the encoding of positive and negative valence is not influenced by prior training order, indicating that prior experience does not affect how these neurons process valence.

Weaknesses:

However, there are limitations to the analysis, including the lack of population-based analyses, such as clustering approaches. The authors do not employ hierarchical clustering or other methods to extract meaning from the diversity of neuronal responses they recorded. Clustering-based approaches could provide deeper insights into how different subpopulations of neurons contribute to emotional processing. Without these methods, the study may miss patterns of functional specialization within the neuronal populations that could be crucial for understanding how valence and salience are encoded at the population level.

Furthermore, while salience encoding is inferred based on responses to stimuli of opposite valence, the study does not test whether these neuronal responses scale with stimulus intensity-a hallmark of classical salience encoding. This limits the conclusions that can be drawn about salience encoding specifically.

In sum, while the study makes valuable contributions to our understanding of CeA function, the lack of clustering-based population analyses and the absence of intensity scaling in the assessment of salience encoding are notable limitations.

Reviewer #3 (Public review):

Summary:

In this study, the authors set out to profile small intestine neuroendocrine tumors (siNETs) using single-cell/nucleus RNA sequencing, an established method to characterize the diversity of cell types and states in a tumor. Leveraging this dataset, they identified distinct malignant subtypes (epithelial-like versus neuronal-like) and characterized the proliferative index of malignant neuroendocrine cells versus non-malignant microenvironment cells. They found that malignant neuroendocrine cells were far less proliferative than some of their non-malignant counterparts (e.g., B cells, plasma cells, epithelial cells) and there was a strong subtype association such that epithelial-like siNETs were linked to high B/plasma cell proliferation, potentially mediated by MIF signaling, whereas neuronal-like siNETs were correlated with low B/plasma cell proliferation. The authors also examined a single case of a mixed lung tumor (neuroendocrine and squamous) and found evidence of intermediate/mixed and stem-like progenitor states that suggest the two differentiated tumor types may arise from the same progenitor.

Strengths:

The strengths of the paper include the unique dataset, which is the largest to date for siNETs, and the potentially clinically relevant hypotheses generated by their analysis of the data.

Weaknesses:

The weaknesses of the paper include the relatively small number of independent patients (n = 8 for siNETs), lack of direct comparison to other published single-cell NET datasets, mixing of two distinct methods (single-cell and single-nucleus RNA-seq), lack of direct cell-cell interaction analyses and spatially-resolved data, and lack of in vitro or in vivo functional validation of their findings.

The analytical methods applied in this study appear to be appropriate, but the methods used are fairly standard to the field of single-cell omics without significant methodological innovation. As the authors bring forth in the Discussion, the results of the study do raise several compelling questions related to the possibility of distinct biology underlying the epithelial-like and neuronal-like subtypes, the origin of mixed tumors, drivers of proliferation, and microenvironmental heterogeneity. However, this study was not able to further explore these questions through spatially-resolved data or functional experiments.

Reviewer #3 (Public review):

Summary:

In their article "Range geographies, not functional traits, explain convergent range and phenology shifts under climate change," the authors rigorously investigate the temporal shifts in odonate species and their potential predictors. Specifically, they examine whether species shift their geographic ranges poleward or alter their phenology to avoid extreme conditions. Leveraging opportunistic observations of European and North American odonates, they find that species showing significant range shifts also exhibited earlier phenological shifts. Considering a broad range of potential predictors, their results reveal that geographical factors, but not functional traits, are associated with these shifts.

Strengths:

The article addresses an important topic in ecology and conservation that is particularly timely in the face of reports of substantial insect declines in North America and Europe over the past decades. Through data integration the authors leverage the rich natural history record for odonates, broadening the taxonomic scope of analyses of temporal trends in phenology and distribution to this taxon. The combination of phenological and range shifts in one framework presents an elegant way to reconcile previous findings improving our understanding of the drivers of biodiversity loss.

Weaknesses:

The introduction and discussion of the article would benefit from a stronger contextualization of recent studies on biological responses to climate change and the underpinning mechanism.

The presentation of the results (particularly in figures) should be improved to address the integrative character of the work and help readers extract the main results. While the writing of the article is generally good, particularly the captions and results contain many inconsistencies and lack important detail. With the multitude of the relationships that were tested (the influence of traits) the article needs more coherence.

Reviewer #3 (Public review):

Summary:

Chen and Phillips present intriguing work that extends our view on the C. elegans small RNA network significantly. While the precise findings are rather C. elegans specific there are also messages for the broader field, most notably the switching of small RNA populations bound to an argonaute, and RNA granules behavior depending on developmental stage. The work also starts to shed more light on the still poorly understood role of the CSR-1 argonaute protein and supports its role in the decay of maternal transcripts. Overall, the work is of excellent quality, and the messages have a significant impact.

Strengths:

Compelling evidence for major shift in activities of an argonaute protein during development, and implications for how small RNAs affect early development. Very balanced and thoughtful discussion.

Weaknesses:

Claims on col-localization of specific 'granules' are not well supported by quantitative data.

Reviewer #3 (Public review):

Summary:

Furman et al. investigated how exposure to prolonged pain impacts human alpha oscillations recorded by electroencephalography (EEG). Two experimental models of prolonged pain were employed in healthy participants, phasic heat pain (PHP) and capsaicin heat pain (CHP). 61 participants completed two identical study visits separated by at least 8 weeks. Peak alpha frequency was reliably slowed by exposure to prolonged pain, whereas overall alpha power was reliably reduced. Both effects appeared to reflect a specific decrease in higher frequency (10-12Hz) alpha activity. The authors suggest that slowing of alpha oscillations is a reliable neural correlate of pain exposure and that manipulation of alpha activity may hold promise for treating chronic pain.

Strengths:

The study uses a within-participants design to show that exposure to pain is associated with acute changes in both the power and frequency of alpha oscillations.

By employing two experimental models of pain exposure and two separate testing visits, the authors were able to show that the effects of pain exposure on alpha activity are replicable across models and time.

Rigorous analysis approaches are used throughout.

Weaknesses:

No a priori power analysis is presented and (due to exclusions) most of the analyses conducted included (sometimes considerably) fewer participants than the overall sample size.

It is not clear whether the power and frequency changes represent two sides of the same coin or whether they reflect distinct mechanisms. The authors suggest in the manuscript that both effects may be explained by decreased power in 'fast' (8-12 Hz) alpha activity, but at other times interpret the effects to potentially represent distinct mechanisms. It would be useful for the authors to further clarify their thoughts on this point.

The statistical significance of some of the effects was dependent on analysis choices such as the exact frequency range chosen to identify alpha peaks.

No control condition was used, and I was left wondering if the effects would be specific to painful stimuli, or would also see the same effects for pleasant or neutral somatosensory stimuli?

Reviewer #3 (Public review):

Asthma is a complex disease that includes endogenous epithelial, immune, and neural components that respond awkwardly to environmental stimuli. Small airborne particles with diameters in the range of 2.5 micrometers or less, so-called PM2.5, are generally thought to contribute to some forms of asthma. These forms of asthma may have increased numbers of neutrophils and/or eosinophils present in bronchoalveolar lavage fluid and are difficult to treat effectively as they tend to be poorly responsive to steroids. Here, Wang and colleagues build on a recent model that incorporated PM2.5 which was found to have a neutrophilic component. Wang altered the model to provide an extra kick via the incorporation of ovalbumin. Building on their prior expertise linking nociceptors and inflammation, they find that silencing TRPV1-expressing neurons either pharmacologically or genetically, abrogated inflammation and the accumulation of neutrophils. By examining bronchoalveolar lavage fluid, they found not only that levels of the number of cytokines were increased, but also that artemin, a protein that supports neuronal development and function, was elevated, which did not occur in nociceptor-ablated mice. They also found that alveolar macrophages exposed to PM2.5 particles had increased artemin transcription, suggesting a further link between pollutants, and immune and neural interactions.

There are substantial caveats that must be attached to the suggestions by the authors that targeting nociceptors might provide an approach to the treatment of neutrophilic airway inflammation in pollution-driven asthma in general and wildfire-associated respiratory problems in particular. These caveats include the uncertainty of the relevance of the conventional source of PM2.5, to pollution and asthma. According to the National Institute of Standards and Technology (NIST), the standard reference material (SRM) 2786 is a mix obtained from an air intake system in the Czech Republic. It is not clear exactly what is in the mix, and a recent bioRxiv preprint, https://www.biorxiv.org/content/10.1101/2023.08.18.553903v3.full.pdf reveals the presence of endotoxin. Care should thus be taken in interpreting data using particulate matter. Regarding wildfires, there is data that indicates that such exposure is toxic to macrophages. What impact might that then have on the production of cytokines, and artemin, in humans?

Reviewer #3 (Public review):

Summary:

Chemical communication is essential for the organization of eusocial insect societies. It is used in various important contexts, such as foraging and recruiting colony members to food sources. While such pheromones have been chemically identified and their function demonstrated in bioassays, little is known about their perception. Excellent candidates are the odorant receptors that have been shown to be involved in pheromone perception in other insects including ants and bees but not termites. The authors investigated the function of the odorant receptor PsimOR14, which was one of four target odorant receptors based on gene sequences and phylogenetic analyses. They used the Drosophila empty neuron system to demonstrate that the receptor was narrowly tuned to the trail pheromone neocembrene. Similar responses to the odor panel and neocembrene in antennal recordings suggested that one specific antennal sensillum expresses PsimOR14. Additional protein modeling approaches characterized the properties of the ligand binding pocket in the receptor. Finally, PsimOR14 transcripts were found to be significantly higher in worker antennae compared to soldier antennae, which corresponds to the worker's higher sensitivity to neocembrene.

Strengths:

The study presents an excellent characterization of a trail pheromone receptor in a termite species. The integration of receptor phylogeny, receptor functional characterization, antennal sensilla responses, receptor structure modeling, and transcriptomic analysis is especially powerful. All parts build on each other and are well supported with a good sample size.

Weaknesses:

The manuscript would benefit from a more detailed explanation of the research advances this work provides. Stating that this is the first deorphanization of an odorant receptor in a clade is insufficient. The introduction primarily reviews termite chemical communication and deorphanization of olfactory receptors previously performed. Although this is essential background, it lacks a good integration into explaining what problem the current study solves.

Selecting target ORs for deorphanization is an essential step in the approach. Unfortunately, the process of choosing these ORs has not been described. Were the authors just lucky that they found the correct OR out of the 50, or was there a specific selection process that increased the probability of success?

The authors assigned antennal sensilla into five categories. Unfortunately, they did not support their categories well. It is not clear how they were able to differentiate SI and SII in their antennal recordings.

The authors used a large odorant panel to determine receptor tuning. The panel included volatile polar compounds and non-volatile non-polar hydrocarbons. Usually, some heat is applied to such non-volatile odorants to increase volatility for receptor testing. It is unclear how it is possible that these non-volatile compounds can reach the tested sensilla without heat application.

Reviewer #3 (Public review):

Summary:

This work presents the development, characterization, and use of new thin microendoscopes (500µm diameter) whose accessible field of view has been extended by the addition of a corrective optical element glued to the entrance face. Two micro endoscopes of different lengths (6.4mm and 8.8mm) have been developed, allowing imaging of neuronal activity in brain regions >4mm deep. An alternative solution to increase the field of view could be to add an adaptive optics loop to the microscope to correct the aberrations of the GRIN lens. The solution presented in this paper does not require any modification of the optical microscope and can therefore be easily accessible to any neuroscience laboratory performing optical imaging of neuronal activity.

Strengths:

(1) The paper is generally clear and well-written. The scientific approach is well structured and numerous experiments and simulations are presented to evaluate the performance of corrected microendoscopes. In particular, we can highlight several consistent and convincing pieces of evidence for the improved performance of corrected micro endoscopes:<br /> a) PSFs measured with corrected micro endoscopes 75µm from the centre of the FOV show a significant reduction in optical aberrations compared to PSFs measured with uncorrected micro endoscopes.<br /> b) Morphological imaging of fixed brain slices shows that optical resolution is maintained over a larger field of view with corrected micro endoscopes compared to uncorrected ones, allowing neuronal processes to be revealed even close to the edge of the FOV.<br /> c) Using synthetic calcium data, the authors showed that the signals obtained with the corrected microendoscopes have a significantly stronger correlation with the ground truth signals than those obtained with uncorrected microendoscopes.

(2) There is a strong need for high-quality micro endoscopes to image deep brain regions in vivo. The solution proposed by the authors is simple, efficient, and potentially easy to disseminate within the neuroscience community.

Weaknesses:

(1) Many points need to be clarified/discussed. Here are a few examples:

a) It is written in the methods: « The uncorrected microendoscopes were assembled either using different optical elements compared to the corrected ones or were obtained from the corrected probes after the mechanical removal of the corrective lens. »<br /> This is not very clear: the uncorrected microendoscopes are not simply the unmodified GRIN lenses?

b) In the results of the simulation of neuronal activity (Figure 5A, for example), the neurons in the center of the FOV have a very large diameter (of about 30µm). This should be discussed. Also, why is the optical resolution so low on these images?

c) It seems that we can't see the same neurons on the left and right panels of Figure 5D. This should be discussed.

d) It is not very clear to me why in Figure 6A, F the fraction of adjacent cell pairs that are more correlated than expected increases as a function of the threshold on peak SNR. The authors showed in Supplementary Figure 3B that the mean purity index increases as a function of the threshold on peak SNR for all micro endoscopes. Therefore, I would have expected the correlation between adjacent cells to decrease as a function of the threshold on peak SNR. Similarly, the mean purity index for the corrected short microendoscope is close to 1 for high thresholds on peak SNR: therefore, I would have expected the fraction of adjacent cell pairs that are more correlated than expected to be close to 0 under these conditions. It would be interesting to clarify these points.

e) Figures 6C, H: I think it would be fairer to compare the uncorrected and corrected endomicroscopes using the same effective FOV.

f) Figure 7E: Many calcium transients have a strange shape, with a very fast decay following a plateau or a slower decay. Is this the result of motion artefacts or analysis artefacts? Also, the duration of many calcium transients seems to be long (several seconds) for GCaMP8f. These points should be discussed.

g) The authors do not mention the influence of the neuropil on their data. Did they subtract the neuropil's contribution to the signals from the somata? It is known from the literature that the presence of the neuropil creates artificial correlations between neurons, which decrease with the distance between the neurons (Grødem, S., Nymoen, I., Vatne, G.H. et al. An updated suite of viral vectors for in vivo calcium imaging using intracerebral and retro-orbital injections in male mice. Nat Commun 14, 608 (2023). https://doi.org/10.1038/s41467-023-36324-3; Keemink SW, Lowe SC, Pakan JMP, Dylda E, van Rossum MCW, Rochefort NL. FISSA: A neuropil decontamination toolbox for calcium imaging signals. Sci Rep. 2018 Feb 22;8(1):3493. doi: 10.1038/s41598-018-21640-2. PMID: 29472547; PMCID: PMC5823956)<br /> This point should be addressed.

h) Also, what are the expected correlations between neurons in the pyriform cortex? Are there measurements in the literature with which the authors could compare their data?

(2) The way the data is presented doesn't always make it easy to compare the performance of corrected and uncorrected lenses. Here are two examples:

a) In Figures 4 to 6, it would be easier to compare the FOVs of corrected and uncorrected lenses if the scale bars (at the centre of the FOV) were identical. In this way, the neurons at the centre of the FOV would appear the same size in the two images, and the distances between the neurons at the centre of the FOV would appear similar. Here, the scale bar is significantly larger for the corrected lenses, which may give the illusion of a larger effective FOV.

b) In Figures 3A-D it would be more informative to plot the distances in microns rather than pixels. This would also allow a better comparison of the micro endoscopes (as the pixel sizes seem to be different for the corrected and uncorrected micro endoscopes).

(3) There seems to be a discrepancy between the performance of the long lenses (8.8mm) in the different experiments, which should be discussed in the article. For example, the results in Figure 4 show a considerable enlargement of the FOV, whereas the results in Figure 6 show a very moderate enlargement of the distance at which the person's correlation with the first ground truth emitter starts to drop.

a) There is also a significant discrepancy between measured and simulated optical performance, which is not discussed. Optical simulations (Figure 1) show that the useful FOV (defined as the radius for which the size of the PSF along the optical axis remains below 10µm) should be at least 90µm for the corrected microendoscopes of both lengths. However, for the long microendoscopes, Figure 3J shows that the axial resolution at 90µm is 17µm. It would be interesting to discuss the origin of this discrepancy: does it depend on the microendoscope used? Are there inaccuracies in the construction of the aspheric corrective lens or in the assembly with the GRIN lens? If there is variability between different lenses, how are the lenses selected for imaging experiments?

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors apply tissue expansion and tiling light sheet microscopy to study allometric growth and regeneration in planaria. They developed image analysis pipelines to help them quantify different neuronal subtypes and muscles in planaria of different sizes and during regeneration. Among the strengths of this work, the authors provide beautiful images that show the potential of the approaches they are taking and their ability to quantify specific cell types in relatively large numbers of whole animal samples. Many of their findings confirm previous results in the literature, which helps validate the techniques and pipelines they have applied here. Among their new observations, they find that the body wall muscles at the anterior and posterior poles of the worm are organized differently and show that the muscle pattern in the posterior head of beta-catenin RNAi worms resembles the anterior muscle pattern. They also show that glial cell processes appear to be altered in beta-catenin or insulin receptor-1 RNAi worms. Weaknesses include some over-interpretation of the data and lack of consideration or citation of relevant previous literature, as discussed below.

Strengths:

This method of tissue expansion will be useful for researchers interested in studying this experimental animal. The authors provide high-quality images that show the utility of this technique. Their analysis pipeline permits them to quantify cell types in relatively large numbers of whole animal samples.

The authors provide convincing data on changes in total neurons and neuronal sub-types in different-sized planaria. They report differences in body wall muscle pattern between the anterior and posterior poles of the planaria, and that these differences are lost when a posterior head forms in beta-catenin RNAi planaria. They also find that glial cell projections are reduced in insulin receptor-1 RNAi planaria.

Weaknesses:

The work would have been strengthened by a more careful consideration of previous literature. Many papers directly relevant to this work were not cited. Such omissions do the authors a disservice because in some cases, they fail to consider relevant information that impacts the choice of reagents they have used or the conclusions they are drawing.

For example, when describing the antibody they use to label muscles (monoclonal 6G10), they do not cite the paper that generated this reagent (Ross et al PMCID: PMC4307677), and instead, one of the papers they do cite (Cebria 2016) that does not mention this antibody. Ross et al reported that 6G10 does not label all body wall muscles equivalently, but rather "predominantly labels circular and diagonal fibers" (which is apparent in Figure S5A-D of the manuscript being reviewed here). For this reason, the authors of the paper showing different body wall muscle populations play different roles in body patterning (Scimone et al 2017, PMCID: PMC6263039, also not cited in this paper) used this monoclonal in combination with a polyclonal antibody to label all body wall muscle types. Because their "pan-muscle" reagent does not label all muscle types equivalently, it calls into question their quantification of the different body wall muscle populations throughout the manuscript. It does not help matters that their initial description of the body wall muscle types fails to mention the layer of thin (inner) longitudinal muscles between the circular and diagonal muscles (Cebria 2016 and citations therein).

Ipsilateral and contralateral projections of the visual axons were beautifully shown by dye-tracing experiments (Okamoto et al 2005, PMID: 15930826). This paper should be cited when the authors report that they are corroborating the existence of ipsilateral and contralateral projections.

The proportional decrease of neurons with growth in S. mediterranea was shown by counting different cell types in macerated planarians (Baguna and Romero, 1981; https://link.springer.com/article/10.1007/BF00026179) and earlier histological observations cited there. These results have also been validated by single-cell sequencing (Emili et al, bioRxiv 2023, https://www.biorxiv.org/content/10.1101/2023.11.01.565140v). Allometric growth of the planaria tail (the tail is proportionately longer in large vs small planaria) can explain this decrease in animal size. The authors never really discuss allometric growth in a way that would help readers unfamiliar with the system understand this.

In some cases, the authors draw stronger conclusions than their results warrant. The authors claim that they are showing glial-muscle interactions, however, they do not provide any images of triple-stained samples labeling muscle, neurons, and glia, so it is impossible for the reader to judge whether the glial cells are interacting directly with body wall muscles or instead with the well-described submuscular nerve plexus. Their conclusion that neurons are unaffected by beta-cat or inr-1 RNAi based on anti-phospho-Ser/Thr staining (Fig. 6E) is unconvincing. They claim that during regeneration "DV muscles initially regenerate into longitudinal fibers at the anterior tip" (line 373). They provide no evidence for such switching of muscle cell types, so it is unclear why they say this.

The authors show how their automated workflow compares to manual counts using PI-stained specimens (Figure S1T). I may have missed it, but I do not recall seeing a similar ground truth comparison for their muscle fiber counting workflow. I mention this because the segmented image of the posterior muscles in Figure 4I seems to be missing the vast majority of circular fibers visible to the naked eye in the original image.

It is unclear why the abstract says, "We found the rate of neuron cell proliferation tends to lag..." (line 25). The authors did not measure proliferation in this work and neurons do not proliferate in planaria.

It is unclear what readers are to make of the measurements of brain lobe angles. Why is this a useful measurement and what does it tell us?

The authors repeatedly say that this work lets them investigate planarians at the single-cell level, but they don't really make the case that they are seeing things that haven't already been described at the single-cell level using standard confocal microscopy.

Reviewer #3 (Public review):

Summary:

This paper demonstrates that membrane depolarization induces a small increase in cell entry into mitosis. Based on previous work from another lab, the authors propose that ERK activation might be involved. They show convincingly using a combination of assays that ERK is activated by membrane depolarization. They show this is Ca2+ independent and is a result of activation of the whole K-Ras/ERK cascade which results from changed dynamics of phosphatidylserine in the plasma membrane that activates K-Ras. Although the activation of the Ras/ERK pathway by membrane depolarization is not new, linking it to an increase in cell proliferation is novel.

Strengths

A major strength of the study is the use of different techniques - live imaging with ERK reporters, as well as Western blotting to demonstrate ERK activation as well as different methods for inducing membrane depolarization. They also use a number of different cell lines. Via Western blotting the authors are also able to show that the whole MAPK cascade is activated.

Weaknesses

A weakness of the study is the data in Figure 1 showing that membrane depolarization results in an increase of cells entering mitosis. There are very few cells entering mitosis in their sample in any condition. This should be done with many more cells to increase confidence in the results. The study also lacks a mechanistic link between ERK activation by membrane depolarization and increased cell proliferation.

The authors did achieve their aims with the caveat that the cell proliferation results could be strengthened. The results for the most part support the conclusions.

This work suggests that alterations in membrane potential may have more physiological functions than action potential in the neural system as it has an effect on intracellular signalling and potentially cell proliferation.

Reviewer #3 (Public Review):

Strengths:<br /> The study used optogenetics together with in vivo electrophysiology to monitor CGRP neuron activity in response to various aversive stimuli including robot chasing to determine whether they encode noxious stimuli differentially. The study used an interesting conditioning paradigm to investigate the role of CGRP neurons in the PBN in both freezing and flight behaviors.

Weakness:<br /> The major weakness of this study is that the chasing robot threat conditioning model elicits weak unconditioned and conditioned flight responses, making it difficult to interpret the robustness of the findings. Furthermore, the conclusion that the CGRP neurons are capable of inducing flight is not substantiated by the data. No manipulations are made to influence the flight behavior of the mouse. Instead, the manipulations are designed to alter the intensity of the unconditioned stimulus.

Reviewer #3 (Public Review):

The authors have performed well designed experiments that elucidate the protective role of Dapa in sepsis model of LPS. This model shows that Dapa works, in part, by increasing expression of the receptor LRP2 in the kidney, that maintains circulating ApoM levels. ApoM binds to S1P which then interacts with the S1P receptor stimulating cardiac function, epithelial and endothelial barrier function, thereby maintaining intravascular volume and cardiac output in the setting of severe inflammation. The authors used many experimental models, including transgenic mice, as well as several rigorous and reproducible techniques to measure the relevant parameters of cardiac, renal, vascular, and immune function. Furthermore, they employ a useful inhibitor of S1P function to show pharmacologically the essential role for this agonist in most but not all the benefits of Dapa. A strength of the paper is the identification of the pathway responsible for the cardioprotective effects of SGLT2is that may yield additional therapeutic targets. There are some weaknesses in the paper, such as, studying only male mice, as well as providing a power analysis to justify the number of animals used throughout their experimentation. Overall, the paper should have a significant impact on the scientific community because the SGLT2i drugs are likely to find many uses in inflammatory diseases and metabolic diseases. This paper provides support for an important mechanism by which they work in conditions of severe sepsis and hemodynamic compromise.

Reviewer #3 (Public Review):

The author proposed the minimum variance principle in the memory representation in addition to two alternative theories of the minimum energy and the maximum smoothness. The strength of this paper is the matching between the prediction data computed from the explicit equation and the behavioral data taken in different conditions. The idea of the weighting of multiple coordinate systems is novel and is also able to reconcile a debate in previous literature.

The weakness is that although each model is based on an optimization principle, but the derivation process is not written in the method section. The authors did not write about how they can derive these weighting factors from these computational principles. Thus, it is not clear whether these weighting factors are relevant to these theories or just hacking methods. Suppose the author argues that this is the result of the minimum variance principle. In that case, the authors should show a process of how to derive these weighting factors as a result of the optimization process to minimize these cost functions.

In addition, I am concerned that the proposed model can cancel the property of the coordinate system by the predicted variance, and it can work for any coordinate system, even one that is not used in the human brain. When the applied force is given in Cartesian coordinates, the directionality in the generalization ability of the memory of the force field is characterized by the kinematic relationship (Jacobian) between the Cartesian coordinate and the coordinate of interest (Cartesian, joint, and object) as shown in Equation 3. At the same time, when a displacement (epsilon) is considered in a space and a corresponding displacement is linked with kinematic equations (e.g., joint displacement and hand displacement in 2 joint arms in this paper), the generated variances in different coordinate systems are linked with the kinematic equation each other (Jacobian). Thus, how a small noise in a certain coordinate system generates the hand force noise (sigma_x, sigma_j, sigma_o) is also characterized by the kinematics (Jacobian). Thus, when the predicted forcefield (F_c, F_j, F_o) was divided by the variance (F_c/sigma_c^2, F_j/sigma_j^2, F_o/sigma_o^2, ), the directionality of the generalization force which is characterized by the Jacobian is canceled by the directionality of the sigmas which is characterized by the Jacobian. Thus, as it has been read out from Fig*D and E top, the weight in E-top of each coordinate system is always the inverse of the shift of force from the test force by which the directionality of the generalization is always canceled. Once this directionality is canceled, no matter how to compute the weighted sum, it can replicate the memorized force. Thus, this model always works to replicate the test force no matter which coordinate system is assumed. Thus, I am suspicious of the falsifiability of this computational model. This model is always true no matter which coordinate system is assumed. Even though they use, for instance, the robot coordinate system, which is directly linked to the participant's hand with the kinematic equation (Jacobian), they can replicate this result. But in this case, the model would be nonsense. The falsifiability of this model was not explicitly written.

Reviewer #3 (Public Review):

The ENANI-2019 study provides valuable insights into child nutrition, development, and metabolomics in Brazil, highlighting both challenges and opportunities for improving child health outcomes through targeted interventions and further research.

Strengths of the methods and results:<br /> (1) The study utilizes data from the ENANI-2019 cohort, which was already existing. This cohort choice allows for longitudinal assessments and exploration of associations between metabolites and developmental outcomes. In addition, there was conservation of resources which are scanty in all settings in the current scenario.<br /> (2) The study aims to investigate the relationship between circulating metabolites (exposure) and early childhood development (outcome), specifically developmental quotient (DQ). The objectives are clearly stated, which facilitates focused research questions and hypotheses. The population that is studied is clearly mentioned.<br /> (3) The study accessed a large number of children under five years, with blood collected from a final sample size of 5,004 children. The exclusion of infants under six months due to venipuncture challenges and lack of reference values highlights practical considerations in research design.<br /> The study sample reflects a diverse range of children in terms of age, sex distribution, weight status, maternal education, and monthly family income. This diversity enhances the generalizability of findings across different sociodemographic groups within Brazil.<br /> (4) The study uses standardized measures (e.g., DQ assessments) and chronological age. Confounding variables, such as child's age, diet quality, and nutritional status, are carefully considered and incorporated into analyses through a Directed Acyclic Graph (DAG). The mean DQ of 0.98 indicates overall developmental norms among the studied children, with variations noted across different demographic factors such as age, region, and maternal education. The prevalence of Minimum Dietary Diversity (MDD) being met by 59.3% of children underscores dietary patterns and their potential impact on health outcomes. The association between nutritional status (weight-for-height z-scores) and developmental outcomes (DQ) provides insights into the interplay between nutrition and child development.<br /> The study identified key metabolites associated with developmental quotient (DQ):<br /> Component 1: Branched-chain amino acids (Leucine, Isoleucine, Valine).<br /> Component 2: Uremic toxins (Cresol sulfate, Phenylacetylglutamine).<br /> Component 3: Betaine and amino acids (Glutamine, Asparagine).<br /> The study focused on several serum metabolites like PAG (phenylacetylglutamine), CS (p-cresyl sulfate), HA (hippuric acid), TMAO (trimethylamine-N-oxide), MeHis (methylhistidine), and Crtn (creatinine). These metabolites are implicated in various metabolic pathways linked to gut microbiota activity, amino acid metabolism, and dietary factors.<br /> These metabolites explained a significant portion of both metabolite variance (39.8%) and DQ variance (4.3%). The study suggests that these metabolites can be used as proxy measures of the gut microbiome in children.<br /> (5) The use of partial least square regression (PLSR) with cross-validation (80% training, 20% testing) which is a robust approach to identify metabolites predictive of DQ, which minimizes overfitting. This model allows for outliers to remain outliers for transparency.<br /> The Directed Acyclic Graph (DAG) identifies and adjusts for confounding variables (e.g., child's diet quality, nutritional status) and strengthens the validity of findings by controlling for potential biases. Developmental and gender differences were studied by testing interactions with the age of the child and the sex.<br /> Mediation analysis exploring metabolites as potential mediators provides insights into underlying pathways linking exposures (e.g., diet, microbiome) with DQ.<br /> The use of Benjamini-Hochberg correction for multiple comparisons and bootstrap tests (5,000 iterations) enhances the reliability of results by controlling false discovery rates and assessing significance robustly.

Significant correlations between serum metabolites and DQ, particularly negative associations with certain metabolites like PAG and CS, suggest potential biomarkers or pathways influencing developmental outcomes. Notably, these associations varied with age, suggesting different metabolic impacts during early childhood development.

Weaknesses:<br /> (1) The data collected was incomplete especially those related to breastfeeding history and birth weight. These have been mentioned in the limitations of the study but yet might have been potential confounders or even factors leading to the particular identified metabolite state of the population.<br /> (2) Other tests than mediation analysis might have been used to ensure reliability and robustness of the data. How data was processed, data cleaning methods, how outliers were handled and sensitivity analyses would ensure robustness of the findings.<br /> (3) The generalizability of the data is not sound especially considering the children mostly belonged to a higher socioeconomic group in Brazil with mother or caregiver education being above a certain level. Comparative studies with children from other socio-economic groups and other cohorts might have been useful. Consideration of sample size adequacy and power analysis might have helped in generalizing the findings.<br /> (4) Caution is needed in interpreting causality from this data because of the nature of the study design Discussing alternative explanations and potential confounding factors in more depth could strengthen the conclusions.

Appraisal<br /> (1) The aims of the study were to identify associations between children's serum metabolome and Early Childhood development. This aim was met. The results do confirm their conclusions.<br /> Impact of the work on the field

(1) Unless actual gut microbiome of children in this age group from gut bacteria examination or gastrointestinal examination of the gut of children, the causality of gut metabolome on early childhood development cannot be established with certainty. Because this may not be possible in every situation, proxy methods such as the one elucidated here might be useful, considering the risk-benefit ratio.<br /> (2) More research is needed on this theme through longitudinal studies to validate these findings and explore underlying pathways involving gut-brain interactions and metabolic dysregulation.<br /> Other readings: Readers are advised to read other research from other countries and other languages to understand the connection between gut microbiome, metabolite spectra, and child development. In addition to study the effect of these factors on child mental development too.

Readers might consider the following questions:<br /> (1) Should investigators study the families through direct observation of diet and other factors to look for a connection between food taken in and gut microbiome and child development?<br /> (2) Can an examination of the mother's gut microbiome influence the child's microbiome? Can the mother or caregiver's microbiome influence early childhood development?<br /> (3) Is developmental quotient enough to study early childhood development? Is it comprehensive enough?

Reviewer #3 (Public Review):

El Amri et al conducted an analysis on the function of marcks and marcksl in Xenopus spinal cord development and regeneration. Their study revealed these proteins are crucial for neurite outgrowth and cell proliferation, including Sox2+ progenitors. Furthermore, they suggested these genes may act through the PLD pathway. The study is well-executed with appropriate controls and validation experiments, distinguishing it from typical regeneration research by including behavioral assays. The manuscript is commendable for its quantifications, literature referencing, careful conclusions, and detailed methods. Conclusions are well-supported by the experiments performed in this study. Overall, this manuscript contributes to the field of spinal cord regeneration and sets a good example for future research in this area.

Reviewer #3 (Public review):

Summary:

Xiong et al. investigated the debated mechanism of PKA activation using hippocampal CA1 neurons under pharmacological and synaptic stimulations. Examining all major PKA-R isoforms in these neurons, they found that a portion of PKA-C dissociates from PKA-R and translocate into dendritic spines following norepinephrine bath application. Additionally, their use of a non-dissociable form of PKA demonstrates its essential role in structural long-term potentiation (LTP) induced by two-photon glutamate uncaging, as well as in maintaining normal synaptic transmission, as verified by electrophysiology. This study presents a valuable finding on the activation-dependent re-distribution of PKA catalytic subunits in CA1 neurons, a process vital for synaptic functionality. The robust evidence provided by the authors makes this work particularly relevant for biologists seeking to understand PKA activation mechanisms, its downstream effects, and synaptic plasticity.

Strengths:

The study is methodologically robust, particularly in the application of two-photon imaging and electrophysiology. The experiments are well-designed with effective controls and a comprehensive analysis. The credibility of the data is further enhanced by the research team's previous works in related experiments. The study provides sufficient evidence to support the classical model of PKA activation via dissociation in neurons.

Weaknesses:

No specific weaknesses are noted in the current study; future research could provide additional insights by exploring PKA dissociation under varied physiological conditions, particularly in vivo, to further validate and expand upon these findings.

Reviewer #3 (Public review):

Summary:

This study investigates the salt-dependent phase separation of A1-LCD, an intrinsically disordered region of hnRNPA1 implicated in neurodegenerative diseases. The authors employ all-atom molecular dynamics (MD) simulations to elucidate the molecular mechanisms by which salt influences A1-LCD phase separation. Contrary to typical intrinsically disordered protein (IDP) behavior, A1-LCD phase separation is enhanced by NaCl concentrations above 100 mM. The authors identify two direct effects of salt: neutralization of the protein's net charge and bridging between protein chains, both promoting condensation. They also uncover an indirect effect, where high salt concentrations strengthen pi-type interactions by reducing water availability. These findings provide a detailed molecular picture of the complex interplay between electrostatic interactions, ion binding, and hydration in IDP phase separation.

Strengths:

• Novel Insight: The study challenges the prevailing view that salt generally suppresses IDP phase separation, highlighting A1-LCD's unique behavior.<br /> • Rigorous Methodology: The authors utilize all-atom MD simulations, a powerful computational tool, to investigate the molecular details of salt-protein interactions.<br /> • Comprehensive Analysis: The study systematically explores a wide range of salt concentrations, revealing a nuanced picture of salt effects on phase separation.<br /> • Clear Presentation: The manuscript is well-written and logically structured, making the findings accessible to a broad audience.

Weaknesses:

• Limited Scope: The study focuses solely on the truncated A1-LCD, omitting simulations of the full-length protein. This limitation reduces the study's comparative value, as the authors note that the full-length protein exhibits typical salt-dependent behavior. However, given the much larger size of the full-length protein, it is acceptable to omit it given the current computing resources available.

Overall, this manuscript represents a significant contribution to the field of IDP phase separation. The authors' findings provide valuable insights into the molecular mechanisms by which salt modulates this process, with potential implications for understanding and treating neurodegenerative diseases.

By what method are ballots counted in Illinois?

Reviewer #3 (Public review):

Summary:

The authors elucidated the role of USP8 in the endocytic pathway. Using C. elegans epithelial cells as a model, they observed that when USP8 function is lost, the cells have a decreased number and size in lysosomes. Since USP8 was already known to be a protein linked to ESCRT components, they looked into what role USP8 might play in connecting lysosomes and multivesicular bodies (MVB). They observed fewer ESCRT-associated vesicles but an increased number of abnormal enlarged vesicles (aberrant early endosomes) when USP8 function was lost. They showed that USP8 interacts with Rabx5 to dissociate it from early endosomes promoting the recruitment of the Rab7 GEF SAND-1/Mon1 and the maturation of the endosomes. The authors provided evidence that USP8 regulates endosomal maturation in a similar fashion in mammalian cells.

Strengths:

The use of two models, C. elegans and a mammalian cell line to describe a similar mechanism.

Reviewer #3 (Public review):

Summary:<br /> In this article, Hermannova et al catalog the changes in ribosome association with mRNAs when the multisubunit eukaryotic translation initiation factor 3 is disrupted by knocking down individual subunits. They find that RNAs relying on TOP motifs for translation, such as ribosomal protein RNAs, and RNAs encoding modification enzymes in the ER and components of the lysosome are upregulated. In contrast, proteins encoding components of MAP kinase cascades are downregulated when subunits of eIF3 are knocked down, but retain elevated levels of activity.

Strengths:<br /> The authors use ribosome profiling of well-characterized mutants lacking subunits of eIF3 and assess the changes in translation that take place. They supplement the ribosome association studies with western blotting to determine protein level changes of affected transcripts. They analyze what transcripts undergo translation changes, which is important for understanding more broadly how translation initiation factor levels affect cancer cell translatomes. Changes observed by both ribosome profiling and western blotting supports their claims that eIF3 functions in mRNA-specific control of translation.

Weaknesses:<br /> (1) The paper would be strengthened if there were a clear model tying the various effects together or linking individual subunit knockdown to cancerous phenotypes. It is noted that the authors plan to address such outcomes of eIF3 dysregulation in future work, which will be of interest.

(2) The paper could also be strengthened if some of the experiments were performed in at least one other cell type to determine whether changes observed are general or cell-type specific. The authors discuss this issue and provide a literature citation to support a more general mechanism.

Reviewer #3 (Public review):

Summary:

This paper aims to address the problem of exploring potentially rewarding environments that contain the danger, based on the assumption that an independent Pavlovian fear learning system can help guide an agent during exploratory behaviour such that it avoids severe danger. This is important given that otherwise later gains seem to outweigh early threats, and agents may end up putting themselves in danger when it is advisable not to do so.

The authors develop a computational model of exploratory behaviour that accounts for both instrumental and Pavlovian influences, combining the two according to uncertainty in the rewards. The result is that Pavlovian avoidance has a greater influence when the agent is uncertain about rewards.

Strengths:

The study does a thorough job of testing this model using both simulations and data from human participants performing an avoidance task. Simulations demonstrate that the model can produce "safe" behaviour, where the agent may not necessarily achieve the highest possible reward but ensures that losses are limited. Interestingly, the model appears to describe human avoidance behaviour in a task that tests for Pavlovian avoidance influences better than a model that doesn't adapt the balance between Pavlovian and instrumental based on uncertainty. The methods are robust, and generally, there is little to criticise about the study.

Weaknesses:

The extent of the testing in human participants is fairly limited but goes far enough to demonstrate that the model can account for human behaviour in an exemplar task. There are, however, some elements of the model that are unrealistic (for example, the fact that pre-training is required to select actions with a Pavlovian bias would require the agent to explore the environment initially and encounter a vast amount of danger in order to learn how to avoid the danger later). The description of the models is also a little difficult to parse.

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

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

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

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

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

Weaknesses:

(1) A better characterization of the nature of the small EV population is missing:

It is unclear why the authors chose to proceed to quantitative mass spectrometry with the bands in the Coomassie from size-separated EV samples, as there are other bands present in the small EV lane but not the large EV lane. This is important to clarify because it underlies how they were able to identify THSD7A as a unique regulator of exosome-mediated filopodia formation. Is there a reason why the total sample fractions were not compared? This would provide valuable information on the nature of the small and large EV populations.

(2) Data analysis and quantification should be performed with increased rigor:

a) Figure 1C - The optical and temporal resolution are insufficient to conclusively characterize the association between exosome secretion and filopodia. Specifically, the 10-second interval used in the image acquisitions is too close to the reported 20-second median time between exosome secretion and filopodia formation. Two-5 sec intervals should be used to validate this. It would also be important to correlate the percentage of filopodia events that co-occur with exosome secretion. Is this a phenomenon that occurs with most or only a small number of filopodia? Additionally, resolution with typical confocal microscopy is subpar for these analyses. TIRF microscopy would offer increased resolution to parse out secretion events. As the TIRF objective is listed in the Methods section, figure legends should mention which images were acquired using TIRF microscopy.

b) Figure 2 - It would be important to perform further analysis to concretely determine the relationship between exosome secretion and filopodia stability. Are secretion events correlated with the stability of filopodia? Is there a positive feedback loop that causes further filopodia stability and length with increased secretion? Furthermore, is there an association between the proximity of secretion with stability? Quantification of filopodia more objectively (# of filopodia/cell) would be helpful.

c) Figure 6 - Why use different gel conditions to detect THSD7A in small EVs from B16F1 cells vs HT1080 and neurons? Why are there two bands for THSD7A in panels C and E? It is difficult to appreciate the KD efficiency in E. The absence of a signal for THSD7A in the HT1080 shEng small EVs that show a signal for endoglin is surprising. The authors should provide rigorous quantification of the westerns from several independent experimental repeats.

(3) The study lacks data on the cellular distribution of endoglin and THSD7A:

a) Figure 6 - Is THSD7A expected to be present in the nucleus as shown in panel D (label D is missing in the Figure). It is not clear if this is observed in neurons. a Western of endogenous THSD7A on cell fractions would clarify this. The authors should further characterize the cellular distribution of THSD7A in both cell types. Similarly, the cellular distribution of endoglin in the cancer cells should be provided. This would help validate the proposed model in Figure 8.

b) Figure 7 - Although the western blot provides convincing evidence for the role of endoglin in THSD7A trafficking, the microscopy data lack resolution as well as key analyses. While differences between shSCR and shEng cells are clear visually, the insets appear to be zoomed digitally which decreases resolution and interferes with interpretation. It would be crucial to show the colocalization of endoglin and THSD7A within CD63-postive MVE structures. What are the structures in Figure 7E shSCR zoom1? It would be important to rule out that these are migrasomes using TSPAN4 staining. More information on how the analysis was conducted is needed (i.e. how extracellular areas were chosen and whether the images are representative of the larger population). A widefield image of shSCR and shEng cells and DAPI or HOECHST staining in the higher magnification images should be provided. Additionally, the authors should quantify the colocalization of external CD63 and mScarlet signals from many independently acquired images (as they did for the internal signals in panel F). Is there no external THSD7A signal in the shEng cells?

Reviewer #3 (Public review):

This manuscript studies the connection between neural activity collected through electrocorticography and hidden vector representations from autoregressive language models, with the specific aim of studying the influence of language model size on this connection. Neural activity was measured from subjects who listened to a segment from a podcast, and the representations from language models were calculated using the written transcription as the input text. The ability of vector representations to predict neural activity was evaluated using 10-fold cross-validation with ridge regression models.

The main results are that (as well summarized in section headings):

(1) Larger models predict neural activity better.

(2) The ability of language model representations to predict neural activity differs across electrodes and brain regions.

(3) The layer that best predicts neural activity differs according to model size, with the "SMALL" model showing a correspondence between layer number and the language processing hierarchy.

(4) There seems to be a similar relationship between the time lag and the ability of language model representations to predict neural activity across models.

Strengths:

(1) The experimental and modeling protocols generally seem solid, which yielded results that answer the authors' primary research question.

(2) Electrocorticography data is especially hard to collect, so these results make a nice addition to recent functional magnetic resonance imaging studies.

Weaknesses:

(1) The interpretation of some results seems unjustified, although this may just be a presentational issue.

a) Figure 2B: The authors interpret the results as "a plateau in the maximal encoding performance," when some readers might interpret this rather as a decline after 13 billion parameters. Can this be further supported by a significance test like that shown in Figure 4B?

b) Figure S1A: It looks like the drop in PCA max correlation is larger for larger models, which may suggest to some readers that the same trend observed for ridge max correlation may not hold, contra the authors' claim that all results replicate. Why not include a similar figure as Figure 2B as part of Figure S1?

(2) Discussion of what might be driving the main result about the influence of model size appears to be missing (cf. the authors aim to provide an explanation of what seems to drive the influence of the layer location in Paragraph 3 of the Discussion section). What explanations have been proposed in the previous functional magnetic resonance imaging studies? Do those explanations also hold in the context of this study?

(3) The GloVe-based selection of language-sensitive electrodes (at least to me) isn't explained/motivated clearly enough (I think a more detailed explanation should be included in the Materials and Methods section). If the electrodes are selected based on GloVe embeddings, then isn't the main experiment just showing that representations from larger language models track more closely with GloVe embeddings? What justifies this methodology?

(4) (Minor weakness) The main experiments are largely replications of previous functional magnetic resonance imaging studies, with the exception of the one lag-based analysis. Is there anything else that the electrocorticography data can reveal that functional magnetic resonance imaging data can't?