Reviewer #3 (Public Review):

Perrodin, Verzat and Bendor describe the response of female mice to the playback of male mouse ultrasonic songs. The experiments were performed in a Y-maze-like apparatus with two acoustically separate response chambers. Sounds were presented in 4 trials, alternating strictly between the left and right branches of the Y. Cumulative dwell time in the two chambers was measured, and used as an index of female preference. They first show, consistent with previous observations, that female mice will spend more time near a speaker playing a male mouse song than near a speaker playing nothing. They then performed several manipulations-time reversals, syllable order randomization, phase scrambled replacement, pure tone replacement, and 'hyper-regular' inter-syllable-intervals-which female mice did not discriminate from the normal song in this assay. Finally, they show that females spent more time near normal songs than near songs with more variable inter-syllable-intervals

The authors' approach to the problem was ethologically sensible -- females were tested in proestrus and estrus, the male odor was used to increase motivation, mouse handling was with tube transfers to reduce stress, mice were age-matched across conditions, and experiments were conducted in the dark (active) phase. In addition, animals were habituated to handling and to the apparatus.

The acoustics were very good. The acoustic structure of the vocal signals was well described. Specific ranges of dB SPL were reported, speaker flatness was evaluated, the sound amplitude was matched in manipulated and unmanipulated songs, and playback onset timing jittered randomly between manipulated and unmanipulated signals.

I think it is a reasonable result. My concerns are the following:

1) The authors use "approach" as it has been used in other publications, but what is actually measured is dwell time. Pomerantz et al, 1983 observed that female mice approached mute and singing males the same number of times (e.g. approached both at the same rate), but spent more time with the singing than the mute male. Their use of "approach" to describe dwell time was a bit confusing to me, but sticking with the way the literature is defensible. However, they also refer to the assay as a "place preference assay", which I found confusing.

2) I am a bit worried about their method of removing side bias (29% of trials). It certainly seems like a reasonable thing to exclude mice that simply picked one side or the other, but, because the stimulus always alternated between the sides, this exclusion of mice exhibiting a side bias is also excluding, specifically, behavior that would be incorrect.

3) Given the observation by Hammerschmidt et al, 2009, that female mice would only discriminate male songs in a playback assay on the first presentation, it is important to know whether females were used across the different manipulations. How many conditions did each female experience? How often did a female display positive discrimination in a condition after having displayed no discrimination?

Specific comments:

1) For Figure 2L

The heat map legend is labeled "Towards" indicating a motion towards either the speaker playing the song or the silent speaker. However, there is nothing in the methods that indicates that the direction of movement was ever measured. I may have missed it, but I can't figure out how this heat map was generated and what it represents. The figure legend states: "Normalized temporal profiles of approach behaviour to mouse songs vs silence over the course of 4 sound presentation trials (x-axis, coloured bars) for each of the behavioural sessions (y-axis, each animal is one line, n = 29), calculated as in I. Sessions (lines) are ordered by the amplitude of their last element." 2I states " I. Temporal profile of approach behaviour over the four sound presentation trials in the example session in C, calculated as the cumulative sum of time in the intact song playback (positively weighted) vs silent (negatively weighted) speaker zone." I interpret this to mean that "Towards" is an inaccurate description of what is being plotted, as there is no motion, only dwell time.

References

K. Hammerschmidt, K. Radyushkin, H. Ehrenreich & J. Fischer (2009) Female mice respond to male ultrasonic 'songs' with approach behavior. Biol. Lett. 5:589-592.

Pomerantz, S.M., Nunez, A.A. & Bean, J (1983) Female behavior is affected by male ultrasonic vocalizations in house mouse. Physiol. Behav. 31:91-96.

Reviewer #1 (Public Review):

Summary:

Given knowledge of the amino acid sequence and of some version of the 3D structure of two monomers that are expected to form a complex, the authors investigate whether it is possible to accurately predict which residues will be in contact in the 3D structure of the expected complex. To this effect, they train a deep learning model that takes as inputs the geometric structures of the individual monomers, per-residue features (PSSMs) extracted from MSAs for each monomer, and rich representations of the amino acid sequences computed with the pre-trained protein language models ESM-1b, MSA Transformer, and ESM-IF. Predicting inter-protein contacts in complexes is an important problem. Multimer variants of AlphaFold, such as AlphaFold-Multimer, are the current state of the art for full protein complex structure prediction, and if the three-dimensional structure of a complex can be accurately predicted then the inter-protein contacts can also be accurately determined. By contrast, the method presented here seeks state-of-the-art performance among models that have been trained end-to-end for inter-protein contact prediction.

Strengths:

The paper is carefully written and the method is very well detailed. The model works both for homodimers and heterodimers. The ablation studies convincingly demonstrate that the chosen model architecture is appropriate for the task. Various comparisons suggest that PLMGraph-Inter performs substantially better, given the same input than DeepHomo, GLINTER, CDPred, DeepHomo2, and DRN-1D2D_Inter. As a byproduct of the analysis, a potentially useful heuristic criterion for acceptable contact prediction quality is found by the authors: namely, to have at least 50% precision in the prediction of the top 50 contacts.

Weaknesses:

My biggest issue with this work is the evaluations made using *bound* monomer structures as inputs, coming from the very complexes to be predicted. Conformational changes in protein-protein association are the key element of the binding mechanism and are challenging to predict. While the GLINTER paper (Xie & Xu, 2022) is guilty of the same sin, the authors of CDPred (Guo et al., 2022) correctly only report test results obtained using predicted unbound tertiary structures as inputs to their model. Test results using experimental monomer structures in bound states can hide important limitations in the model, and thus say very little about the realistic use cases in which only the unbound structures (experimental or predicted) are available. I therefore strongly suggest reducing the importance given to the results obtained using bound structures and emphasizing instead those obtained using predicted monomer structures as inputs.

In particular, the most relevant comparison with AlphaFold-Multimer (AFM) is given in Figure S2, *not* Figure 6. Unfortunately, it substantially shrinks the proportion of structures for which AFM fails while PLMGraph-Inter performs decently. Still, it would be interesting to investigate why this occurs. One possibility would be that the predicted monomer structures are of bad quality there, and PLMGraph-Inter may be able to rely on a signal from its language model features instead. Finally, AFM multimer confidence values ("iptm + ptm") should be provided, especially in the cases in which AFM struggles.

Besides, in cases where *any* experimental structures - bound or unbound - are available and given to PLMGraph-Inter as inputs, they should also be provided to AlphaFold-Multimer (AFM) as templates. Withholding these from AFM only makes the comparison artificially unfair. Hence, a new test should be run using AFM templates, and a new version of Figure 6 should be produced. Additionally, AFM's mean precision, at least for top-50 contact prediction, should be reported so it can be compared with PLMGraph-Inter's.

It's a shame that many of the structures used in the comparison with AFM are actually in the AFM v2 training set. If there are any outside the AFM v2 training set and, ideally, not sequence- or structure-homologous to anything in the AFM v2 training set, they should be discussed and reported on separately. In addition, why not test on structures from the "Benchmark 2" or "Recent-PDB-Multimers" datasets used in the AFM paper?

It is also worth noting that the AFM v2 weights have now been outdated for a while, and better v3 weights now exist, with a training cutoff of 2021-09-30.

Another weakness in the evaluation framework: because PLMGraph-Inter uses structural inputs, it is not sufficient to make its test set non-redundant in sequence to its training set. It must also be non-redundant in structure. The Benchmark 2 dataset mentioned above is an example of a test set constructed by removing structures with homologous templates in the AF2 training set. Something similar should be done here.

Finally, the performance of DRN-1D2D for top-50 precision reported in Table 1 suggests to me that, in an ablation study, language model features alone would yield better performance than geometric features alone. So, I am puzzled why model "a" in the ablation is a "geometry-only" model and not a "LM-only" one.

Reviewer #2 (Public Review):

This work introduces PLMGraph-Inter, a new deep-learning approach for predicting inter-protein contacts, which is crucial for understanding protein-protein interactions. Despite advancements in this field, especially driven by AlphaFold, prediction accuracy and efficiency in terms of computational cost) still remains an area for improvement. PLMGraph-Inter utilizes invariant geometric graphs to integrate the features from multiple protein language models into the structural information of each subunit. When compared against other inter-protein contact prediction methods, PLMGraph-Inter shows better performance which indicates that utilizing both sequence embeddings and structural embeddings is important to achieve high-accuracy predictions with relatively smaller computational costs for the model training.

The conclusions of this paper are mostly well supported by data, but test examples should be revisited with a more strict sequence identity cutoff to avoid any potential information leakage from the training data. The main figures should be improved to make them easier to understand.

1) The sequence identity cutoff to remove redundancies between training and test set was set to 40%, which is a bit high to remove test examples having homology to training examples. For example, CDPred uses a sequence identity cutoff of 30% to strictly remove redundancies between training and test set examples. To make their results more solid, the authors should have curated test examples with lower sequence identity cutoffs, or have provided the performance changes against sequence identities to the closest training examples.

2) Figures with head-to-head comparison scatter plots are hard to understand as scatter plots because too many different methods are abstracted into a single plot with multiple colors. It would be better to provide individual head-to-head scatter plots as supplementary figures, not in the main figure.

3) The authors claim that PLMGraph-Inter is complementary to AlphaFold-multimer as it shows better precision for the cases where AlphaFold-multimer fails. To strengthen the point, the qualities of predicted complex structures via protein-protein docking with predicted contacts as restraints should have been compared to those of AlphaFold-multimer structures.

4) It would be interesting to further analyze whether there is a difference in prediction performance depending on the depth of multiple sequence alignment or the type of complex (antigen-antibody, enzyme-substrates, single species PPI, multiple species PPI, etc).

Reviewer #1 (Public Review):

Summary:<br /> This paper uses a high-throughput assay of transcription levels to (i) assess the potential of large numbers of Escherichia coli genomic sequences to function as promoters, and (ii) identify regulatory sequences in some of those promoters. This is a substantial undertaking, and while much of the work supports principles of transcription and transcription regulation described by many prior studies, there is considerable value in assessing promoters on such a large scale. The identification of putative regulatory sequences in larger numbers of promoters will likely be valuable to other groups studying transcription regulation in E. coli. And the analysis of antisense promoters provides some interesting new insight that goes beyond previous anecdotal studies.

Strengths:<br /> - The presentation of the work is very clear, and the conclusions are mostly well supported by the data.<br /> - The assays are rigorously controlled and analyzed.<br /> - Conclusions regarding the impact of antisense transcription on sense transcript levels provide new insight. While these data are consistent with previous anecdotal studies, to my knowledge this is the first large-scale analysis supporting a negative regulatory role for antisense transcription.<br /> - The putative regulatory elements mapped in the high-throughput mutagenesis experiments will be a valuable resource for the scientific community.

Weaknesses:<br /> (all minor)<br /> - There are some parts where the authors could clarify their arguments.<br /> - I'm not convinced that intragenic promoters impact codon usage rather than the other way around.<br /> - The authors should present a more nuanced discussion of promoters that avoids making yes/no calls (i.e., characterize sequences by promoter strength rather than a binary yes/no call of being a promoter).<br /> - Data relating to intragenic promoters should be presented and discussed for sense and antisense promoters separately.

Reviewer #2 (Public Review):

In this work, Urtecho et al. use genome-integrated massively parallel reporter assays (MPRAs) to catalog the locations of promoters throughout the E. coli genome. Their study uses four different MPRA libraries. First, they assayed a library containing 17,635 promoter regions having transcription start sites (TSSs) previously reported by three different sources. They found that 2,760 of these regions exhibited transcription above an experimentally determined threshold. Second, they assayed a library using sheared E. coli genome fragments. This library allowed the authors to systematically identify candidate promoter regions throughout the genome, some of which had not been identified before. Additionally, by performing experiments with this library under different growth conditions, the authors were able to identify promoters with condition-dependent activity. Third, to improve the resolution at which they were able to identify transcription start sites, the authors assayed a library that tiled all candidate promoter regions identified using the genomic fragments library. Data from the tiled library allowed the authors to identify minimal promoter regions. Fourth, the authors assayed a scanning mutagenesis library in which they systematically scrambled individual 10 bp windows within 2,057 previously identified active promoters at 5 bp intervals. After validation with known promoters, this approach allowed the authors to identify novel functional elements within regulatory regions. Finally, the authors fit multiple machine learning models to their data with the goal of predicting promoter activity from DNA sequences.

The work by Urtecho et al. provides an important resource for researchers studying bacterial transcriptional regulation. Despite decades of study, a comprehensive catalogue of E. coli promoters is still lacking. The results of Urtecho et al. provide a state-of-the-art atlas of promoters in the E. coli genome that is readily accessible through the website, http://ecolipromoterdb.com. The authors' work also provides an important demonstration of the power of genome-integrated MPRAs. Unlike many MPRA-based studies, the authors use the results of their initial MPRAs to design follow-up MPRAs, which they then carry out. Finally, the scanning mutagenesis MPRAs the authors perform provide valuable data that could lead to the discovery of novel transcription factor binding sites and other functional regulatory sequence elements.

Below I provide two major critiques and some minor critiques of the paper. The purpose of these critiques is simply to help the authors improve the quality of the manuscript.

Major points:<br /> 1. Ultimately, a comprehensive atlas of E. coli promoters should include nucleotide resolution TSS data, which is not present in the MPRA datasets reported by Urtecho et al.. The authors do use some methods to narrow down the positions of TSSs, but these methods do not provide the resolution one would ideally like to see in a TSS atlas. I understand that acquiring single-nucleotide-resolution data is beyond the scope of this manuscript, but it still might make sense for the authors to discuss this limitation in the Discussion section.

2. The authors should clarify which points in the Results section are novel conclusions or observations, and which points are simply statements that prior conclusions or observations were confirmed. This distinction can be unclear at times.

Minor points:<br /> 1. Line 200-203: "We conclude that inactive TSS-associated promoters lack -35 elements but may become active in growth conditions where additional transcription factors mobilize and facilitate RNAP positioning in the absence of a -35 motif." Making this type of mechanistic observations from the slight difference observed in the enrichment analysis seems too speculative to me. Also, I do not understand how the discrepancies can be explained in terms of transcription factor differences. If the previous studies from which the annotated TSS were extracted were also performed during the log phase in rich media, why would the transcription factors present be different?

2. Line 224-226: "Active TSSs not overlapping a candidate promoter region generally exhibited weak activity, which may indicate that greater sensitivity is achieved through testing of oligo-array synthesized regions (Figure S3)." The authors should clarify this statement. In particular, it is mechanistically unclear why one library would be more sensitive than another if they contain similar sequences.

3. Figure 2B. The authors should clarify that the heights of the arrows correspond to TSS activity as assayed by one library and that the pile-up plots represent promoter activity as assayed by a different library.

4. Line 255-257: "We also observed an enrichment for 150 bp minimal promoter regions, although these were generally weak indicating that our resolution is limited when tiling weaker promoters." The authors should clarify whether the peak at 150 bp is an artifact of using oligos containing 150 bp tiles to construct the library. Also, the authors should clarify why there are some minimal promoters with lengths > 150 bp when the length of the tiles was 150 bp.

5. Line 262 refers to "Supplementary Table 1", but I was not able to find this table in the supplement.

6. Line 324-325: "We used a σ70 PWM to identify the highest-scoring σ70 motifs within intragenic promoters and determined their relative coding frames". I find the term "relative coding frame" here to be unclear; the authors should clarify what they mean.

7. Figure 3 C , D: The authors should use the same terminology in the plots and the methods section describing them. They should also clarify how the values plotted in C and D were computed.

8. Line 329-332: "The observed depletion of -35 motifs positioned in the +2 reading frame and -10 motifs in the +1 reading frame is likely due to the fact that the canonical sequences for these motifs would create stop codons within the protein if placed at these positions." The definition of the reading frame here is unclear. Do the authors mean that the 0 frame is defined as occurring when the hexamer exactly overlaps 2 codons, the +1 frame is when the hexamer is shifted 1 nt downstream of that position, and the +2 frame is when the hexamer is shifted 2 nt downstream of that position?

9. Line 538-539: "We performed hyperparameter tuning for a three-layer CNN and achieved an AUPRC =0.44." The authors should explicitly describe the architecture used for the CNN, and perhaps include a diagram of this architecture. In addition, the authors should clarify the mathematical forms of the other methods tested.

10. Line 1204-1205: "We standardized all datasets as detailed above in 'Universal Promoter Expression Quantification and Activity Thresholding'". That title does not appear before in the text. I believe the appropriate subsection is called "Standardizing Promoter Expression Quantification and Activity Thresholding".

11. Line 1265-1266: "We include a k-mer if the absolute correlation with expression is greater than the 'random' k-mer frequency, resulting in 4800/5440 filtered k-mers." It is unclear to me which two correlations are being compared. Please clarify. For example, would this be accurate: "We include a k-mer if the absolute correlation of its frequency with expression is greater than the absolute correlation of its 'random' frequency with expression"?

Reviewer #3 (Public Review):

In this revised manuscript, Urtecho et al., present an updated version of their earlier submission. They characterized thousands of promoter sequences in E. coli using a massively-parallel reporter assay and built a number of computational models to classify active from inactive promoters or associate the sequence to promoter expression/strength. As eluded in the earlier review cycle, the amount of experimental, bioinformatics, and analytical work presented here is astounding.

Identifying promoters and associating genomic (or promoter) sequences to promoter strength is nontrivial. Authors report challenges in achieving this grand goal even with the state-of-the-art characterization technology used here. Nevertheless, the experimental work, analytic workflow, and data resource presented here will serve as a milestone for future researchers.

Reviewer #1 (Public Review):

In this work, Xie et al. developed SCA-seq, which is a multiOME mapping method that can obtain chromatin accessibility, methylation, and 3D genome information at the same time. SCA-seq first uses M.CviPI DNA methyltransferase to treat chromatin, then perform proximity ligation followed by long-read sequencing. This method is highly relevant to a few previously reported long read sequencing technologies. Specifically, NanoNome, SMAC-seq, and Fiber-seq have been reported to use m6A or GpC methyltransferase accessibility to map open chromatin, or open chromatin together with CpG methylation; Pore-C and MC-3C have been reported to use long read sequencing to map multiplex chromatin interactions, or together with CpG methylation. Therefore, as a combination of NanoNome/SMAC-seq/Fiber-seq and Pore-C/MC-3C, SCA-seq is one step forward. The authors tested SCA-seq in 293T cells and performed benchmark analyses testing the performance of SCA-seq in generating each data module (open chromatin and 3D genome). The QC metrics appear to be good and I am convinced that this is a valuable addition to the toolsets of multi-OMIC long-read sequencing mapping.

The revised manuscript addressed most of my questions except my concern about Fig. S9. This figure is about a theory that a chromatin region can become open due to interaction with other regions, and the author propose a mathematic model to compute such effects. I was concerned about the errors in the model of Fig. S9a, and I was also concerned about the lack of evidence or validation. In their responses, the authors admitted that they cannot provide biological evidence or validations but still chose to keep the figure and the text.

The revised Fig. S9a now uses a symmetric genome interaction matrix as I suggested. But Figure S9a still have a lot of problems. Firstly, the diagonal of the matrix in Fig. S9a still has many 0's, which I asked in my previous comments without an answer. The legend mentioned that the contacts were defined as 2, 0 or -2 but the revised Fig. S9a only shows 1,0, or -1 values. Furthermore, Fig. S9b,9c,9d all added a panel of CTCF+/- but there is no explanation in text or figure legend about these newly added panels. Given many unaddressed problems, I would still suggest deleting this figure.

In my opinion, this paper does not need Fig. S9 to support its major story. The model in this figure is independent of SCA-seq. I think it should be spinoff as an independent paper if the authors can provide more convincing analysis or experiments. I understand eLife lets authors to decide what to include in their paper. If the authors insist to include Fig. S9, I strongly suggest they should at least provide adequate explanation about all the figure panels. At this point, the Fig. S9 is not solid and clearly have many errors. The readers should ignore this part.

Reviewer #2 (Public Review):

In this manuscript, Xie et al presented a new method derived from PORE-C, SCA-seq, for simultaneously measuring chromatin accessibility, genome 3D and CpG DNA methylation. SCA-seq provides a useful tool to the scientific communities to interrogate the genome structure-function relationship.

The revised manuscript has clarified almost of the concerns raised in the previous round of review, though I still have two minor concerns,

1) In fig 2a, there is no number presented in the Venn diagram (although the left panel indeed showed the numbers of the different categories, including the numbers in the right panel would be more straightforward).

2) The authors clarified the discrepancy between sfig 7a and sfig 7g. However, the remaining question is, why is there a big difference in the percentage of the cardinality count of concatemers of the different groups between the chr7 and the whole genome?

Reviewer #1 Public Review

Anobile and colleagues present a manuscript detailing an account of numerosity processing with an appeal to a two-channel model. Specifically, the authors propose that the perception of numerosity relies on (at least) two distinct channels for small and large numerosities, which should be evident in subject reports of perceived numerosity. To do this, the authors had subjects reproduce visual dot arrays of numerosities ranging from 8 to 32 dots, by having subjects repetitively press a response key at a pre-instructed rate (fast or slow) until the number of presses equaled the number of perceived dots. The subjects performed the task remarkably well, yet with a general bias to overestimate the number of presented dots. Further, no difference was observed in the precision of responses across numerosities, providing evidence for a scalar system. No differences between fast and slow tapping were observed. For behavioral analysis, the authors examined correlations between the Weber fractions for all presented numerosities. Here, it was found that the precision at each numerosity was similar to that at neighboring numerosities, but less similar to more distant ones. The authors then went on to conduct PCA and clustering analyses on the weber fractions, finding that the first two components exhibited an interaction with the presented numerosity, such that each was dominant at distinct lower and upper ranges and further well-fit by a log-Gaussian model consistent with the channel explanation proposed at the beginning.

Overall, the authors provide compelling evidence for a two-channel system supporting numerosity processing that is instantiated in sensorimotor processes. A strength of the presented work is the principled approach the authors took to identify mechanisms, as well as the controls put in place to ensure adequate data for analysis. Some questions do remain in the data, and there are aspects of the presentation that could be adjusted.

-The use of a binary colormap for the correlation matrix seems unnecessary. Binary colormaps between two opposing colors (with white in the middle) are best for results spanning positive and negative values (say, correlation values between -1 and +1), but the correlations here are all positive, so a uniform colormap should be applied. I can appreciate that the authors were trying to emphasize that a 2+ channel system would lead to lower correlations at larger ratios, but that's emphasized better in the numerical ratio line plots.

-In Figure 1, the correlation matrices in Figure 1 appear blurred out. I am not sure if this was intentional but suspect it was not, and so they should appear like those presented in Figure 3.

-It's notable that the authors also collected data on a timing task to rule out a duration-based strategy in the numerosity task. If possible, it would be great to have the author also conduct the rest of the analyses on the duration task as well; that is, to look at WF correlation matrices/ratios as well as PCA. There is evidence that duration processing is also distinctly sensorimotor, and may also rely on similar channels. Evidence either for or against this would likely be of great interest.

-For the duration task, there was no fast tapping condition. Why not? Was this to keep the overall task length short?

-The number of subjects/trials seems a bit odd. Why did some subjects perform both and not others? The targets say they were presented "between 25 and 30 times", but why was this variable at all?

-For the PCA analysis, my read of the methods and results is that this was done on all the data, across subjects. If the data were run on individual subjects and the resulting PCA components averaged, would the same results be found?

-For the data presented in Figure 2, it would be helpful to also see individual subject data underlaid on the plots to get a sense of individual differences. For the reproduced number, these will likely be clustered together given how small the error bars are, but for the WF data it may show how consistently "flat" the data are. Indeed, in other magnitude reproduction tasks, it is not uncommon to see the WF decrease as a function of target magnitude (or even increase). It may be possible that the reason for the observed findings is that some subjects get more variable (higher WFs) with larger target numbers and others get less variable (lower WFs).

-Regarding the two-channel model, I wonder how much the results would translate to different ranges of numerosities? For example, are the two channels supported here specific to these ranges of low and high numbers, or would there be a re-mapping to a higher range (say, 32 to 64 dots) or to a narrower range (say 16 to 32 dots). It would be helpful to know if there is any evidence for this kind of remapping.

Reviewer #2 Public Review

The authors wish to apply established psychophysical methods to the study of number. Specifically, they wish to test the hypothesis - supported by their previous work - that human sensorimotor processes are tuned to specific number ranges. In a novel set of tasks, they ask participants to tap a button N times (either fast or slow), where N varies between 8 and 32 across trials. As I understood it, they then computed the Weber fraction (WF) for each participant for each number and correlated those values across participants and numbers. They find stronger correlations for nearby numbers than for distant numbers and interpret this as evidence of sensorimotor tuning functions. Two other analyses - cluster analyses and principal component analyses (PCA) - suggest that participants' performance relied on at least 2 mechanisms, one for encoding low numbers of taps (around 10) and another for encoding larger numbers (around 27).

Strengths

Individual differences can be a rich source of scientific insight and I applaud the authors for taking them seriously, and for exploring new avenues in the study of numerical cognition.

Weaknesses

Inter-subject-correlation<br /> The experiment "is based on the idea that interindividual variability conveys information that can reveal common sensory processes (Peterzell & Kennedy, 2016)" but I struggled to understand the logic of this technique. The authors explain it most clearly when they write "Regions of high intercorrelation between neighbouring stimuli intensity can be interpreted to imply that sets of stimuli are processed by the same (shared) underlying channel. This channel, while responding relatively more to its preferred stimulus, will also be activated by neighbouring stimuli that although slightly different from the preferred intensity, are nevertheless included in the same response distribution." As I understood it, the correlations are performed "between participants, for all targets values" - meaning that they are measuring the extent to which different participants' WFs vary together. But why is this a good measure of channels? This analysis seems to assume that if people have channels for numerical estimation, they will have the same channels, tuned to the same numerical ranges. But this is an empirical question - individual participants could have wildly different channels, and perhaps different numbers of channels (even in the tested range). If they do, then this between-subject analysis would mask these individual differences (despite the subtitle).

Different channels<br /> I had trouble understanding much of the analyses, and this may account for at least some of my confusion. That said, as I understand it, the results are meant to provide "evidence that tuned mechanisms exist in the human brain, with at least two different tunings" because of the results of the clustering analysis and PCA. However, as the authors acknowledge, "PCA aims to summarize the dataset with the minimal number of components (channels). We can therefore not exclude the possible existence of more than two (perhaps not fully independent) channels." So I believe this technique does not provide more evidence for the existence of 2 channels as for the existence of 4 or 8 or 11 channels, the upper bound for a task testing 11 different numbers. If we can conclude that people may have one channel per number, what does "channel" mean?

Several other questions arose for me when thinking through this technique. If people did have two channels (at least in this range), why would they be so broad? Why would they be centered so near the ends of the tested range? Can such effects be explained by binning on the part of the participants, who might have categorized each number (knowingly or not) as either "small" or "large"? Whereas the experiment tested numbers 8-32, numbers are infinite - How could a small number of channels cover an infinite set? Or even the set 8-10,000? More broadly, I was unsure what advantages channels would have - that is - how in principle would having distinct channels for processing similar stimuli improve (rather than impede) discrimination abilities?

No number perception<br /> I was uncertain about the analogy to studies of other continuous dimensions like spatial frequency, motion, and color. In those studies, participants view images with different spatial frequency, motion, or color - the analogy would be to see dot arrays containing different numbers of dots. Instead, here participants read written numerals (like "19"), symbols which themselves do not have any numerical properties to perceive. How does that difference change the interpretation of the effects? One disadvantage of using numerals is that they introduce a clear discontinuity: Our base-10 numerical system artificially chunks integers into decades, potentially causing category-boundary effects in people's reproductions.

Sensorimotor<br /> The authors wished to test for "sensorimotor mechanisms selective to numerosity" but it's not clear what makes their effects sensorimotor (or selective to numerosity, see below). It's true they found effects using a tapping task (which like all behavior is sensorimotor), but it's not clear that this effect is specific to sensorimotor number reproduction. They might find similar effects for numerical comparison or estimation tasks. Such findings would suggest the effect may be a general feature of numerical cognition across modalities.

Specific to numbers<br /> The authors argue that their effects are "number selective" but they do not provide compelling evidence for this selectivity. In principle, their main findings could be explained by the duration of tapping rather than the number of taps. They argue this is unlikely for two reasons. The first reason is that the overall pattern of results was unchanged across the fast and slow tapping conditions, but differences in duration were confounded with numerosity in both conditions, so the comparison is uninformative. (Given this, I am not sure what we stand to learn by comparing the two tapping speeds.) The second reason is that temporal reproduction was less precise in their control condition than numerical reproduction, but this logic is unclear: Participants could still use duration (or some combination of speed and duration) as a helpful cue to numerosity, even if their duration reproductions were imperfect.

If the authors wish to test the role of duration, they might consider applying the same analytical techniques they use for numbers to their duration data. Perhaps participants show similar evidence for duration-selective channels, in the absence of number, as they do for other non-numerical domains (like spatial frequency).

Theories of numerical cognition. An expansive literature on numerical cognition suggests that many animals, human children, and adults across cultures have two systems for representing numerosity without counting - one that can represent the exact cardinality of sets smaller than about 4 and another that represents the approximate number of larger sets (but see Cheyette & Piantadosi, 2020). The current paper would benefit from better relating its findings to this long lineage of theories and findings in numerical approximation across cultures, ages, and species.

Reviewer #1 (Public Review):

The study presents an extensive computational approach to identify the motor neuron input from the characteristics of single motor neuron discharge patterns during a ramp up/down contraction. This reverse engineering approach is relevant due to limitations in our ability to estimate this input experimentally. Using well-established models of single motor neurons, a (very) large number of simulations were performed that allowed identification of this relation. In this way, the results enable researchers to measure motor neuron behavior and from those results determine the underlying neural input scheme. Overall, the results are very convincing and represent an important step forward in understanding the neural strategies for controlling movement.

Reviewer #1 (Public Review):

Summary:<br /> In this study, Basha and colleagues aim to test whether the thalamic nucleus reuniens can facilitate the hippocampus/prefrontal cortex coupling during sleep. Considering the importance of sleep in memory consolidation, this study is important to understand the functional interaction between these three majorly involved regions. This work suggests that the thalamic nucleus reuniens has a functional role in synchronizing the hippocampus and prefrontal cortex.

Strengths:<br /> The authors performed recordings in naturally sleeping cats, and analysed the correlation between the main slow wave sleep oscillatory hallmarks: slow waves, spindles, and hippocampal ripples, and with reuniens' neurons firing. They also associated intracellular recordings to assess the reuniens-prefrontal connectivity, and computational models of large networks in which they determined that the coupling of oscillations is modulated by the strength of hippocampal-thalamic connections.

Weaknesses:<br /> The authors' main claim is made on slow waves and spindle coupling, which are recorded both in the prefrontal cortex and surprisingly in reuniens. Known to be generated in the cortex by cortico-thalamic mechanisms, the slow waves and spindles recorded in reuniens show no evidence of local generation in the reuniens, which is not anatomically equipped to generate such activities. Until shown differently, these oscillations recorded in reuniens are most likely volume-conducted from nearby cortices. Therefore, such a caveat is a major obstacle to analysing their correlation (in time or frequency domains) with oscillations in other regions.

Finally, the choice of the animal model (cats) is the best suited one, as too few data, particularly anatomical ones regarding reuniens connectivity, are available to support functional results.

Reviewer #2 (Public Review):

Summary:<br /> The interplay between the medial prefrontal cortex and ventral hippocampal system is critical for many cognitive processes, including memory and its consolidation over time. A prominent idea in recent research is that this relationship is mediated at least in part by the midline nucleus reuniens with respect to consolidation in particular. Whereas the bulk of evidence has focused on neuroanatomy and the effects of temproary or permanent lesions of the nucleus reuniens, the current work examined the electrophysiology of these three structures and how they inter-relate, especially during sleep, which is anticipated to be critical for consolidation. They provide evidence from intercellular recordings of the bi-directional functional connectivity among these structures. There is an emphasis on the interactions between these regions during sleep, especially slow-wave sleep. They provide evidence, in cats, that cortical slow waves precede reuniens slow waves and hippocampal sharp-wave ripples, which may reflect prefrontal control of the timing of thalamic and hippocampal events, They also find evidence that hippocampal sharp wave ripples trigger thalamic firing and precede the onset of reuniens and medial prefrontal cortex spindles. The authors suggest that the effectiveness of bidirectional connections between the reuniens and the (ventral) CA1 is particularly strong during non-rapid eye movement sleep in the cat. This is a very interesting, complex study on a highly topical subject.

Strengths:<br /> An excellent array of different electrophysiological techniques and analyses are conducted. The temporal relationships described are novel findings that suggest mechanisms behind the interactions between the key regions of interest. These may be of value for future experimental studies to test more directly their association with memory consolidation.

Weaknesses:<br /> Given the complexity and number of findings provided, clearer explanation(s) and organisation that directed the specific value and importance of different findings would improve the paper. Most readers may then find it easier to follow the specific relevance of key approaches and findings and their emphasis. For example, the fact that bidirectional connections exist in the model system is not new per se. How and why the specific findings add to existing literature would have more impact if this information was addressed more directly in the written text and in the figure legends.

Reviewer #1 (Public Review):

Summary: By elevating Ca influx and inducing PTP, the authors have maximised the release probability. In this condition, the release probability is nearly one. Under such a condition, the release site can release another vesicle in a short time. By analyzing mean, variance and covariance, the authors propose a release model that each release site contains a docking site and a replacement site. They excluded the LS-TS model (Neher and Brose) based on discrepancy between model and the data (mean and covariance).

Strengths: The authors have used a minimal stimulation and modelling nicely to look into stochastic nature of release sites with good resolution. This cannot be done at other synapses. Overall conclusions are reasonable and convincing.

Weaknesses: The interpretation is somewhat model-dependent, and it is unclear if the interpretation is unique. For example, it is unclear if the heterogeneous release probability among sites, silent sites, can explain the results. However, the authors discuss these potential caveats in a fair manner and argue that their model is very likely to be the best so far.

Reviewer #2 (Public Review):

Summary:<br /> Silva et al. describe an experimental study conducted on cerebellar parallel fiber-to-molecular interneuron synapses to investigate the size of the readily releasable pool (RRP) of synaptic vesicles (SVs) per docking site in response to trains of action potentials. The study aims to determine whether there are multiple binding sites for SVs at each docking site, which could lead to a higher RRP size than previously thought.

The researchers used this glutamatergic synapse to conduct their experiments. They employed various techniques and manipulations to enhance release probability, docking site occupancy, and synaptic depression. By counting the number of released SVs in response to action potential trains and normalizing the results based on the number of docking sites, they estimated the RRP size per docking site.

The key findings and observations in the manuscript are as follows:

Docking Site Occupancy and Release Probability Enhancement: The researchers used 4-amidopyridine (4-AP) and post-tetanic potentiation (PTP) protocols to enhance the release probability of docked SVs and the occupancy of docking sites, respectively.

Synchronous and Asynchronous Release: Synchronous release refers to SVs released in response to individual action potentials, while asynchronous release involves SVs released after the initial release response due to calcium elevation. The study observed changes in the balance between synchronous and asynchronous release under different conditions, revealing the degree of filling of the RRP.

Modeling of Release Dynamics: The researchers employed a modeling approach based on the "replacement site/docking site" (RS/DS) model, where SVs bind to a replacement site before moving to a docking site and eventually undergoing release. The model was adjusted to experimental conditions to estimate parameters like docking site occupancy and release probabilities.

Comparison of Different Models: The study compared the RS/DS model with an alternative model known as the "loosely docked/tightly docked" (LS/TS) model. The LS/TS model assumes that a docking site can only accommodate one SV at a time, while the RS/DS model considers the possibility of accommodating multiple SVs.

Maximum RRP Size: Through a combination of experimental results and model simulations, the study revealed that the maximum RRP size per docking site reached close to two SVs under certain conditions, supporting the idea that each docking site can accommodate multiple SVs.

Strengths:<br /> The study is rigorously conducted and takes into consideration previous work of RRP size and SV docking site estimation. The study addresses a long-standing question in synaptic physiology.

Weaknesses:<br /> It remains unclear how generalizable the findings are to other types of synapses.

Reviewer #1 (Public Review):

Activity has effects on the development of neural circuitry during almost any step of neuronal differentiation. In particular during specific time periods of circuit development, so called critical periods (CP), altered neural activity can induce permanent changes of neuronal and network excitability. In complex neural networks it is often difficult to pinpoint the specific network components that are permanently altered by activity, and it often remains unclear how activity is integrated during the CP to set mature network excitability. This study combines electrophysiology with pharmacological and optogenetic manipulation in the Drosophila genetic model system to pinpoint the neural substrate that is influenced by altered activity during a critical period (CP) of larval locomotor circuit development. Moreover, it is then tested whether and how different manipulations of synaptic input are integrated during the CP to tune network excitability.

Strengths: Based on previous work, during the CP network activity is increased by feeding the GABA-AR antagonist PTX. This results in permanent network activity changes as highly convincingly assayed by a prolonged recovery period following induced seizure and by altered intersegmental locomotor network coordination. This is then used to provide two important findings: First, compelling electro- and optophysiological as well as anatomical experiments track the site of network change down to the level of single neurons and pre- versus postsynaptic specializations. In short, increased activity during the CP increases both, the magnitude of excitatory and inhibitory synaptic transmission to the aCC motoneuron, but excitation is affected more strongly. This results in altered excitation inhibition ratios. Fine electrophysiology shows that excitatory synapse strengthening occurs postsynaptically. High quality anatomy shows that dendrite size and numbers of synaptic contacts remain unaltered. It is a major accomplishment to track the tuning of network excitability during the CP down to the physiology of specific synapses at identified neurons.<br /> Second, additional experiments with single neuron resolution demonstrate that during the CP different forms of activity manipulation are integrated so that opposing manipulations can rescue altered setpoints. This provides novel insight into how developing neural network excitability is tuned, and it indicates that during the CP training can rescue the effects of hyperactivity.

Weaknesses: There are no major weaknesses to the findings presented, but the molecular cause that underlies increased motoneuron postsynaptic responsiveness as well as the mechanism that integrates different forms of activity during the CP remain unknown. However, the discussion addresses this point adequately.

Reviewer #2 (Public Review):

SUMMARY: In this study, the authors use the tractable Drosophila embryonic/larval motor circuit to determine how manipulations to activity during a critical period (CP) modify the circuit in ways that persist into later developmental stages. Previously, this group demonstrated that manipulations to the aCC/MN-Ib neuron in embryonic stages enhance (or can rescue) susceptibility to seizures at later larval stages. Here, the authors demonstrate that following enhanced excitatory drive (by PTX feeding), the aCC neuron acquires increased sensitivity to cholinergic excitatory transmission, presumably due to increased postsynaptic receptor abundance and/or sensitivity, although this is not clarified. Although locomotion is not altered at later developmental larval stages, the authors suggest there is reduced "robustness" to induced seizures. The second part of the study then goes on to enhance inhibition during the CP in an attempt to counteract the enhanced excitation, and show that many aspects of the CP plasticity are rescued. The author conclude that "average" E/I activity is integrated during the CP to determine excitability of the mature locomotor network.

Overall, this study provides compelling mechanistic insight into how a final motor output neuron changes in response to enhanced excitatory drive during a CP to change functionality of the circuit at later mature developmental stages. The first part of this study is strong, clearly showing the changes in the aCC neuron that result from enhanced excitatory input. This includes very nice electrophysiology and imaging data that assess synaptic function and structure onto aCC neurons from pre-motor inputs resulting from PTX exposure during development. However, the later experiments in Figures 6 and 7 designed to counteract the CP plasticity are somewhat difficult to interpret. In particular, the specificity of the manipulations of the ch neuron intended to counteract the CP plasticity is unclear, given the complexities of how these changes impact excitability all neurons during development. It is clear that CP plasticity is largely rescued in later stages, but it is hard to know if downstream or secondary adaptations may be masking the PTX-induced plasticity normally observed. Nonetheless, this study provides an important advance in our understanding of what parameters change during CPs to calibrate network dynamics at later developmental stages.

Reviewer #3 (Public Review):

Summary:<br /> In Hunter, Coulson et al, the authors seek to expand our understanding of how neural activity during developmental critical periods might control the function of the nervous system later in life. To achieve increased excitation, the authors build on their previous results and apply picrotoxin 17-19 hours after egg-laying, which is a critical period of nervous system development. This early enhancement of excitation leads to multiple effects in third-instar larvae, including prolonged recovery from electroshock, increased synchronization of motor neuron networks, and increased AP firing frequency. Using optogenetics and whole-cell patch clamp electrophysiology, the authors elegantly show that picrotoxin-induced over-excitation leads to increased strength of excitatory inputs, and not loss of inhibitory inputs. To enhance inhibition, the authors chose an approach that involved stimulation of mechanosensory neurons; this counteracts picrotoxin-induced signs of increased excitation. This approach to enhancing inhibition requires further validation.

Strengths:<br /> • The authors confirm their previous results and show that 17-19 hours after egg laying is a critical period of nervous system development.<br /> • Using Ca2+/Sr2+ substitutions, the authors demonstrate that synaptic connections between A18a & aCC show increased mEPSP amplitudes. The authors show that this aCC input is what is driving enhanced excitation.<br /> • The authors demonstrate that the effects of over-excitation attributed to picrotoxin exposure are generalizable and also occur in bss mutant flies.

Weaknesses:<br /> • The authors build on their previous work and argue that the critical period (17-19h after egg-laying) is a uniquely sensitive period of development. Establishing the developmental window of the critical period is important for the present study. The present study would benefit from demonstrating that exposure to picrotoxin at L1 or L2 do not lead to changes in induced seizure at L3. This would further the authors hypothesis of the criticality of the 17-19h AEL period.<br /> • The ch-related experiments require further controls and explanation. Regarding experiments in Fig 6, what is the effect of ch neuron stimulation alone on time lag and AP frequency? The authors report related pilot experiments have been performed; the present study would be strengthened with inclusion of these data.

Reviewer #1 (Public Review):

Summary:<br /> Peterson et al., present a series of experiments in which the Pavlovian performance (i.e. time spent at a food cup/port) of male and female rats is assessed in various tasks in which context/cue/outcome relationships are altered. The authors find no sex differences in context-irrelevant tasks and no such differences in tasks in which the context signals that different cues will earn different outcomes. They do find sex differences, however, when a single outcome is given and context cues must be used to ascertain which cue will be rewarded with that outcome (Ctx-dep O1 task). Specifically, they found that males acquired the task faster, but that once acquired, the performance of the task was more resilient in female rats against exposure to a stressor. Finally, they show that these sex differences are reflected in differential rates of c-fos expression in all three subregions of rat OFC, medial, lateral, and ventral, in the sense that it is higher in females than males, and only in the animals subject to the Ctx-dep O1 task in which sex differences were observed.

Strengths:<br /> • Well-written.<br /> • Experiments elegantly designed.<br /> • Robust statistics.<br /> • Behaviour is the main feature of this manuscript, rather than any flashy techniques or fashionable lab methodologies, and luckily the behaviour is done really well.<br /> • For the most part I think the conclusions were well supported, although I do have some slightly different interpretations to the authors in places.

Weaknesses:<br /> 1. With regards to the claim (page 4 of pdf), I think I can see what the authors are getting at when they claim "Only Ctx-dep.01 engages context-gated reward predictions", because the same reward is available in each context, and the animal must use contextual information to determine which cue will be rewarded. In other words, it has a discriminative purpose. In Ctx-dep.O1/O2, however, although the context doesn't serve a discriminative purpose in the sense that one cue will always earn a unique outcome, regardless of context, the fact that these cues are differentially rewarded in the different context means that animals may well form context-gated cue-outcome associations (e.g. CtxA-(CS1-O1), CtxnoA-(CS2-O2)). Moreover, the context is informative in this group in telling the animal which cue will be rewarded, even prior to outcome delivery, such that I don't think contextual information will fade to the background of the association and attention be lost to it in the way, say Mackintosh (1975) might predict. Therefore, I don't think this statement is correct.

2. I think the results shown in Figure 1 are very interesting, and well supported by the statistics. It's so nice to see a significant interaction, as so many papers try to report these types of effects without it. However, I do wonder how specific the results are to contextual modulation. That is, should a discriminative discrete cue be used instead of each context (e.g. CS1 indicates CS2 earns O1, CS3 indicates CS4 earns O1), would female rats still be as slow to learn the discrimination?

3. Pages 8-9 of pdf, where the biological basis or the delayed acquisition of contextual control in females is considered, I find this to be written from a place of assuming that what is observed in the males is the default behaviour. That is, although the estrous cycle and its effects on synaptic plasticity/physiology may well account for the results, is there not a similar argument to be made for androgens in males? Perhaps the androgens also somehow alter synaptic plasticity/physiology, leading to their faster speed, reduced performance stability, and increased susceptibility to stress.

4. In addition, the OFC - which is the brain region found to have differential expression of c-fos in males and females in Figure 5 - is not explicitly discussed with regard to the biological mechanisms of differences, which seems odd.

Reviewer #3 (Public Review):

Summary:<br /> This manuscript reports an experiment that compared groups of rats acquisition and performance of a Pavlovian bi-conditional discrimination, in which the presence of one cue, A, signals that the presentation of one CS, X, will be followed by a reinforcer and a second CS, Y, will be nonreinforced. Periods of cue A alternated with periods of cue B, which signaled the opposite relationship, cue X is nonreinforced, and cue Y is reinforced. This is a conditional discrimination problem in which the rats learned to approach the food cup in the presence of each CS conditional on the presence of the third background cue. The comparison groups consisted of the same conditional discrimination with the exception that each CS was paired with a different reinforcer. This makes the problem easier to solve as the background is now priming a differential outcome. A third group received simple discrimination training of X reinforced and Y nonreinforced in cues A and B, and the final group was trained with X and Y reinforced on half the trials (no discrimination). The results were clear that the latter two discrimination learning procedures resulted in rapid learning in comparison to the first. Rats required about 3 times as many 4-session blocks to acquire the bi-conditional discrimination than the other two discrimination groups. Within the biconditional discrimination group, female and male rats spent the same amount of time in the food cup during the rewarded CS, but females spent more time in the food cup during CS- than males. The authors interpret this as a deficit in discrimination performance in females on this task and use a measure that exaggerates the difference in CS+ and CS_ responding (a discrimination ratio) to support their point. When tested after acute restraint stress, the male rats spent less time in the food cup during the reinforced CS in comparison to the female rats, but did not lose discrimination performance entirely. The was also some evidence of more fos-positive cells in the orbitofrontal cortex in females, but this difference was of degree.

Overall, I think the authors were successful in documenting performance on the biconditional discrimination task. Showing that it is more difficult to perform than other discriminations is valuable and consistent with the proposal that accurate performance requires encoding of conditional information (which the authors refer to as "context"). There is evidence that female rats spend more time in the food cup during CS-, but I hesitate to agree that this is an important sex difference. There is no cost to spending more time in the food cup during CS- and they spend much less time there than during CS+. Males and females also did not differ in their CS+ responses, suggesting similar levels of learning. A number of factors could contribute to more food cup time in CS-, such as smaller body size and more locomotor activity. The number of food cup entries during CS+ and CS- was not reported here. Nevertheless, I think the manuscript will make a useful contribution to the field and hopefully lead readers to follow up on these types of tasks.

One area for development would be to test the associative properties of the cues controlling the conditional discrimination, can they be shown to have the properties of Pavlovian occasion-setting stimuli? Such work would strengthen the justification/rationale for using the terms "context" and "occasion setter" to refer to these stimuli in this task in the way the authors do in this paper.

Strengths:<br /> - Nicely designed and conducted experiment.<br /> - Documents performance difference by sex.

Weaknesses:<br /> - Overstatement of sex differences.<br /> - Inconsistent, confusing, and possibly misleading use of terms to describe/imply the underlying processes contributing to performance.

Reviewer #1 (Public Review):

The authors presented a new MNase-based proximity ligation method called MChIP-C, allowing for the measurement of protein-mediated chromatin interactions at single-nucleosome resolution on a genome-wide scale. With improved resolution and sensitivity, they explored the spatial connectivity of active promoters and identified the potential candidates for establishing/maintaining E-P interactions. Finally, with published CRISPRi screens, they found that most functionally verified enhancers do physically interact with their cognate promoters, supporting the enhancer-promoter looping model.

The study's experimental approach and findings are interesting. However, several issues need to be addressed.

1. The authors described that "the lack of interaction between experimentally-validated enhancers and their cognate promoters in some studies employing C-methods has raised doubts regarding the classical promoter-enhancer looping model", so it's intriguing to see whether the MChIP-C could indeed detect the E-P interactions which were not identified by C-methods as they mentioned (Benabdallah et al., 2019; Gupta et al., 2017). I agree that they identified more E-P interactions using MChIP-C, but specifically, they should show at least 2-3 cases. It's important since this is the main conclusion the authors want to draw.

2. The authors compared their data to those of Chen et al. (Chen et al., 2022), who used PLAC-seq with anti-H3K4me3 antibodies in K562 cells and standard Micro-C data previously reported for K562, concluding that "MChIP-C achieves superior sensitivity and resolution compared to C-methods based on standard restriction enzymes.". This is not convincing since they only compared their data to one dataset. More datasets from other cell lines should be included.

3. The reasons for choosing Chen's data (Chen et al., 2022) and CRISPRi screens (Fulco et al., 2019; Gasperini et al., 2019) should be provided since there are so many out there.

4. The authors identify EP300 histone acetyltransferase and the SWI/SNF remodeling complex as potential candidates for establishing and/or maintaining enhancer-promoter interactions, but not RNA polymerase II, mediator complex, YY1, and BRD4. More explanation is needed for this point since they're previously suggested to be associated with E-P interactions.

5. The limitations of the method should be discussed.

Reviewer #2 (Public Review):

Summary:<br /> Golov et al performed the capture of MChIP-C using the H3K4me3 antibody. The new method significantly increases the resolution of Micro-C and can detect clear interactions which are not well described in the previous HiChIP/PLAC-seq method. Overall, the paper represents a significant technological advance that can be valuable to the 3D genomic field in the future.

Strengths:<br /> 1. The authors established a novel method to profile the promoter center genomic interactions based on the Micro-C method. Such a method could be very useful to dissect the enhancer promoter interaction which has long been an issue for the popular HiC method.

2. With the MChIP-C method the authors are able to find new genomic interactions with promoter regions enriched in CTCF. The author has significantly increased the detection sensitivity of such methods as PLAC-seq, Micro-C, and HiChIP.

3. The authors identified a new type of interaction between the CTCF-less promoter and the CTCF binding site. This particular type of interaction could explain the CTCF's function in regulating gene transcription activity as observed in many studies. I personally think the second stripe model of P-CTCF interaction is more likely as this has been proposed for the super-enhancer stripe model before. The author should also discuss this part of the story more.

Weaknesses:<br /> 1. The data presentation should include the contact heat map. The current data presentation makes it hard for the readers to have a comprehensive view of pair-wise interactions between promoters and the PIR. In particular, these maps may directly give answers to the proposed model of promoter-CTCF interactions by the authors in Figure 3a.

2. In Fig 3D, there seems a very limited increase of power predicting MChIP-C signal for DHS-promoter pairs beyond the addition of CTCF. This figure could be simplified with fewer factors.

3. The current method seems to have a big fraction of unusable reads. How the authors process the data should be included to allow for future reproduction. Ideally, the authors should generate a package on R or Bioconda for this processing.

Reviewer #3 (Public Review):

Summary:<br /> This manuscript represents a technological development- specifically a micrococcal nuclease chromatin capture approach, termed MChIP-C to identify promoter-centered chromatin interactions at single nucleosome resolution via a specific protein, similar to HiChIP, ChIA-PET, etc.. In general, the manuscript is technically well done. Two major issues raise concerns that need to be addressed. First, it does not appear that novel chromatin interactions identified by MChIP-C which were missed by other approaches such as HiChIP, were validated. This is central to the argument of "improved" sensitivity, which is one of the key factors to assess sensitivity. Second is the question of resolution. Because the authors focus on a histone mark (H3K4me3) it is unclear whether the resolution of the assay truly exceeds other approaches, especially microC. These two issues are not completely supported by the data provided.

Strengths:<br /> 1) The method appears to hold promise to improve both the sensitivity and resolution of protein-centered chromatin capture approaches.

Weaknesses:<br /> 1) Specific validation experiments to demonstrate the identification of previously missed novel interactions are missing.

2) It is unclear if the resolution is really superior based on the data provided.

3) It is unclear how much advantage the approach has, especially compared to existing approaches such as HiChIP< since sequencing depth as a variable is not adequately addressed.

Reviewer #1 (Public Review):

Summary:<br /> The manuscript considers a mechanistic extension of MacArthur's consumer-resource model to include chasing down food and potential encounters between the chasers (consumers) that lead to less efficient feeding in the form of negative feedback. After developing the model, a deterministic solution and two forms of stochastic solutions are presented, in agreement with each other. Finally, the model is applied to explain observed coexistence and rank-abundance data.

Strengths:<br /> - The application of the theory to natural rank-abundance curves is impressive.<br /> - The comparison with the experiments that reject the competitive exclusion principle is promising. It would be fascinating to see if in, e.g. insects, the specific interference dynamics could be observed and quantified and whether they would agree with the model.<br /> - The results are clearly presented; the methods adequately described; the supplement is rich with details.<br /> - There is much scope to build upon this expansion of the theory of consumer-resource models. This work can open up new avenues of research.

Weaknesses:<br /> - I am questioning the use of carrying capacity (Eq. 4) instead of using nutrient limitation directly through Monod consumption (e.g. Posfai et al. who the authors cite). I am curious to see how these results hold or are changed when Monod consumption is used.

- Following on the previous comment, I am confused by the fact that the nutrient consumption term in Eq. 1 and how growth is modeled (Eq. 4) are not obviously compatible and would be hard to match directly to experimentally accessible quantities such as yield (nutrient to biomass conversion ratio). Ultimately, there is a conservation of mass ("flux balance"), and therefore the dynamics must obey it. I don't quite see how conservation of mass is imposed in this work.

- These models could be better constrained by more data, in principle, thereby potential exists for a more compelling case of the relevance of this interference mechanism to natural systems.

- The underlying frameworks, B-D and MacArthur are not properly exposed in the introduction, and as a result, it is not obvious what is the specific contribution in this work as opposed to existing literature. One needs to dig into the literature a bit for that. The specific contribution exists, but it might be more clearly separated and better explained. In the process, the introduction could be expanded a bit to make the paper more accessible, by reviewing key features from the literature that are used in this manuscript.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript by Kang et al investigates how the consideration of pairwise encounters (consumer-resource chasing, intraspecific consumer pair, and interspecific consumer pair) influences the community assembly results. To explore this, they presented a new model that considers pairwise encounters and intraspecific interference among consumer individuals, which is an extension of the classical Beddington-DeAngelis (B-D) phenomenological model, incorporating detailed considerations of pairwise encounters and intraspecific interference among consumer individuals. Later, they connected with several experimental datasets.

Strengths:<br /> They found that the negative feedback loop created by the intraspecific interference allows a diverse range of consumer species to coexist with only one or a few types of resources. Additionally, they showed that some patterns of their model agree with experimental data, including time-series trajectories of two small in-lab community experiments and the rank-abundance curves from several natural communities. The presented results here are interesting and present another way to explain how the community overcomes the competitive exclusion principle.

Weaknesses:<br /> The authors only explore the case with interspecific interference or intraspecific interference exists. I believe they need to systematically investigate the case when both interspecific and intraspecific interference exists. In addition, the text description, figures, and mathematical notations have to be improved to enhance the article's readability. I believe this manuscript can be improved by addressing my comments, which I describe in more detail below.

1. In nature, it is really hard for me to believe that only interspecific interference or intraspecific interference exists. I think a hybrid between interspecific interference and intraspecific interference is very likely. What would happen if both the interspecific and intraspecific interference existed at the same time but with different encounter rates? Maybe the authors can systematically explore the hybrid between the two mechanisms by changing their encounter rates. I would appreciate it if the authors could explore this route.

2. In the first two paragraphs of the introduction, the authors describe the competitive exclusion principle (CEP) and past attempts to overcome the CEP. Moving on from the first two paragraphs to the third paragraph, I think there is a gap that needs to be filled to make the transition smoother and help readers understand the motivations. More specifically, I think the authors need to add one more paragraph dedicated to explaining why predator interference is important, how considering the mechanism of predator interference may help overcome the CEP, and whether predator interference has been investigated or under-investigated in the past. Then building upon the more detailed introduction and movement of predator interference, the authors may briefly introduce the classical B-D phenomenological model and what are the conventional results derived from the classical B-D model as well as how they intend to extend the B-D model to consider the pairwise encounters.

3. The notations for the species abundances are not very informative. I believe some improvements can be made to make them more meaningful. For example, I think using Greek letters for consumers and English letters for resources might improve readability. Some sub-scripts are not necessary. For instance, R^(l)_0 can be simplified to g_l to denote the intrinsic growth rate of resource l. Similarly, K^(l)_0 can be simplified to K_l. Another example is R^(l)_a, which can be simplified to s_l to denote the supply rate. In addition, right now, it is hard to find all definitions across the text. I would suggest adding a separate illustrative box with all mathematical equations and explanations of symbols.

4. What is the f_i(R^(F)) on line 131? Does it refer to the growth rate of C_i? I noticed that f_i(R^(F)) is defined in the supplementary information. But please ensure that readers can understand it even without reading the supplementary information. Otherwise, please directly refer to the supplementary information when f_i(R^(F)) occurs for the first time. Similarly, I don't think the readers can understand \Omega^\prime_i and G^\prime_i on lines 135-136.

Reviewer #3 (Public Review):

Summary:<br /> A central question in ecology is: Why are there so many species? This question gained heightened interest after the development of influential models in theoretical ecology in the 1960s, demonstrating that under certain conditions, two consumer species cannot coexist on the same resource. Since then, several mechanisms have been shown to be capable of breaking the competitive exclusion principle (although, we still lack a general understanding of the relative importance of the various mechanisms in promoting biodiversity).

One mechanism that allows for breaking the competitive exclusion principle is predator interference. The Beddington-DeAngelis is a simple model that accounts for predator interference in the functional response of a predator. The B-D model is based on the idea that when two predators encounter one another, they waste some time engaging with one another which could otherwise be used to search for resources. While the model has been influential in theoretical ecology, it has also been criticized at times for several unusual assumptions, most critically, that predators interfere with each other regardless of whether they are already engaged in another interaction. However, there has been considerable work since then which has sought either to find sets of assumptions that lead to the B-D equation or to derive alternative equations from a more realistic set of assumptions (Ruxton et al. 1992; Cosner et al. 1999; Broom et al. 2010; Geritz and Gyllenberg 2012). This paper represents another attempt to more rigorously derive a model of predator interference by borrowing concepts from chemical reaction kinetics (the approach is similar to previous work: Ruxton et al. 1992). The main point of difference is that the model in the current manuscript allows for 'chasing pairs', where a predator and prey engage with one another to the exclusion of other interactions, a situation Ruxton et al. (1992) do not consider. While the resulting functional response is quite complex, the authors show that under certain conditions, one can get an analytical expression for the functional response of a predator as a function of predator and resource densities. They then go on to show that including intraspecific interference allows for the coexistence of multiple species on one or a few resources, and demonstrate that this result is robust to demographic stochasticity.

Strengths:<br /> I appreciate the effort to rigorously derive interaction rates from models of individual behaviors. As currently applied, functional responses (FRs) are estimated by fitting equations to feeding rate data across a range of prey or predator densities. In practice, such experiments are only possible for a limited set of species. This is problematic because whether a particular FR allows stability or coexistence depends on not just its functional form, but also its parameter values. The promise of the approach taken here is that one might be able to derive the functional response parameters of a particular predator species from species traits or more readily measurable behavioral data.

Weaknesses:<br /> The main weakness of this paper is that it devotes the vast majority of its length to demonstrating results that are already widely known in ecology. We have known for some time that predator interference can relax the CEP (e.g., Cantrell, R. S., Cosner, C., & Ruan, S. 2004).

While the model presented in this paper differs from the functional form of the B-D in some cases, it would be difficult to formulate a model that includes intraspecific interference (that increases with predator density) that does not allow for coexistence under some parameter range. Thus, I find it strange that most of the main text of the paper deals with demonstrating that predator interference allows for coexistence, given that this result is already well known. A more useful contribution would focus on the extent to which the dynamics of this model differ from those of the B-D model.

The formulation of chasing-pair engagements assumes that prey being chased by a predator are unavailable to other predators. For one, this seems inconsistent with the ecology of most predator-prey systems. In the system in which I work (coral reef fishes), prey under attack by one predator are much more likely to be attacked by other predators (whether it be a predator of the same species or otherwise). I find it challenging to think of a mechanism that would give rise to chased prey being unavailable to other predators. The authors also critique the B-D model: "However, the functional response of the B-D model involving intraspecific interference can be formally derived from the scenario involving only chasing pairs without predator interference (Wang and Liu, 2020; Huisman and De Boer, 1997) (see Eqs. S8 and S24). Therefore, the validity of applying the B-D model to break the CEP is questionable.".

However, the way "chasing pairs" are formulated does result in predator interference because a predator attacking prey interferes with the ability of other predators to encounter the prey. I don't follow the author's logic that B-D isn't a valid explanation for coexistence because a model incorporating chasing pairs engagements results in the same functional form as B-D.

More broadly, the specific functional form used to model predator interference is of secondary importance to the general insight that intraspecific interference (however it is modeled) can allow for coexistence. Mechanisms of predator interference are complex and vary substantially across species. Thus it is unlikely that any one specific functional form is generally applicable.

Joint Public Review:

This paper explores how minimal active matter simulations can model tissue rheology, with applications to the in vivo situation of zebrafish morphogenesis. The authors explore the idea of active noise, particle softness and size heterogeneity cooperating to give rise to surprising features of experimental tissue rheologies (in particular an increase and then a plateau in viscosity with fluid fraction). In general, the paper is interesting from a theoretical standpoint, by providing a bridge between concepts from jamming of particulate systems and experiments in developmental biology. The idea of exploring a free space picture in this context is also interesting. It will be interesting in the future to see whether and how the findings change when considering 3D tissues with less size heterogeneity or how viscosity is impacted by the time scale of measurements.

Reviewer #1 (Public Review):

Gazula and co-workers presented in this paper a software tool for 3D structural analysis of human brains, using slabs of fixed or fresh brains. This tool will be included in Freesurfer, a well-known neuroimaging processing software. It is possible to reconstruct a 3D surface from photographs of coronal sliced brains, optionally using a surface scan as a model. A high-resolution segmentation of 11 brain regions is produced, independent of the thickness of the slices, interpolating information when needed. Using this method, the researcher can use the sliced brain to segment all regions, without the need for ex vivo MRI scanning.

The software suite is freely available and includes 3 modules. The first accomplishes preprocessing steps, for correction of pixel sizes and perspective. The second module is a registration algorithm that registers a 3D surface scan obtained prior to sectioning (reference) to the multiple 2D slices. It is not mandatory to scan the surface - a probabilistic atlas can also be used as a reference - however, the accuracy is lower. The third module uses machine learning to perform the segmentation of 11 brain structures in the 3D reconstructed volume. This module is robust, dealing with different illumination conditions, cameras, lenses, and camera settings. This algorithm ("Photo-SynthSeg") produces isotropic smooth reconstructions, even in high anisotropic datasets (when the in-plane resolution of the photograph is much higher than the thickness), interpolating the information between slices.

To verify the accuracy and reliability of the toolbox, the authors reconstructed 3 datasets, using real and synthetic data. Real data of 21 postmortem confirmed Alzheimer's disease cases from the Massachusetts Alzheimer's Disease Research Center (MADRC) and 24 cases from the AD Research at the University of Washington (who were MRI scanned prior to processing) were employed for testing. These cases represent a challenging real-world scenario. Additionally, 500 subjects of the Human Connectome project were used for testing error as a continuous function of slice thickness. The segmentations were performed with the proposed deep-learning new algorithm ("Photo-SynthSeg") and compared against MRI segmentations performed to "SAMSEG" (an MRI segmentation algorithm, computing Dice scores for the segmentations. The methods are sound and statistically showed correlations above 0.8, which is good enough to allow volumetric analysis. The main strengths of the methods are the datasets used (real-world challenging and synthetic) and the statistical treatment, which showed that the pipeline is robust and can facilitate volumetric analysis derived from brain sections and conclude which factors can influence the accuracy of the method (such as using or not 3D scan and using constant thickness).

Although very robust and capable of handling several situations, the researcher has to keep in mind that processing has to follow some basic rules in order for this pipeline to work properly. For instance, fiducials and scales need to be included in the photograph, and the slabs must be photographed against a contrasting background. Also, only coronal slices can be used, which can be limiting for certain situations.

The authors achieved their aims, and the statistical analysis confirms that the machine learning algorithm performs segmentations comparable to the state-of-the-art of automated MRI segmentations.

Those methods will be particularly interesting to researchers who deal with post-mortem tissue analysis and do not have access to ex vivo MRI. Quantitative measurements of specific brain areas can be performed in different pathologies and even in the normal aging process. The method is highly reproducible, and cost-effective since it allows the pipeline to be applied by any researcher with small pre-processing steps.

The paper is very interesting and well structured, adding an important tool for fixed and fresh brain analysis. The software tool is robust and demonstrated good and consistent results in the hard task of managing automated segmentation from brain slices. In the future, segmentation of the histological slices could be developed and histological structures added (such as small brainstem nuclei, for instance). Also, dealing with axial and sagittal planes can be useful to some labs.

Reviewer #2 (Public Review):

Summary:<br /> The authors developed a tool-set Photo-SynthSeg for the software FreeSurfer which performs 3D reconstruction and high-resolution 3D segmentation on a stack of dissection photographs of brain tissues. The tool-set consists of three modules: the pre-processing module, which performs dissection photography correction; the registration module, which registers corrected dissection photographs based on 3D surface scan, ex vivo MRI or probabilistic atlas; the segmentation module based on U-Net. To prove the performance of the tools, three experiments were conducted, including a volumetric comparison of brain tissues on AD and HC groups from MADRC, a quantitative evaluation of segmentation on UW-ADRC and a quantitative evaluation of 3D reconstruction on HCP digitally sliced MRI data.

Strengths:<br /> The quantitative evaluation of segmentation and reconstruction on synthetic and real data demonstrates the accuracy of the methodology. Also, the successful application of this toolset on two brain banks with different slice thicknesses, tissue processing, and photograph settings demonstrates its robustness. The toolset also benefits from its adaptability of different 3D references, such as surface scans, ex vivo MRI, and even probabilistic atlas, suiting the needs of different brain banks.

Weaknesses:<br /> 1) The current method could only perform accurate segmentation on subcortical tissues. It is of more interest to accurately segment cortical tissues, whose morphometrics are more predictive of neuropathology. The authors also mentioned that they would extend the toolset to allow for cortical tissue segmentation in the future.

2) Brain tissues are not rigid bodies, so dissected slices could be stretched or squeezed to some extent. Also, dissected slices that contain temporal poles may have several disjoined tissues. Therefore, each pixel in dissected photographs may go through slightly different transformations. The authors constrain that all pixels in each dissected photograph go through the same affine transform in the reconstruction step probably due to concerns of computational complexity. But ideally, dissected photographs should be transformed with some non-linear warping or locally linear transformations. Or maybe the authors could advise how to place different parts of dissected slices when taking dissection photographs to reduce such non-linearity of transforms.

3) For the quantitative evaluation of the segmentation on UW-ARDC, the authors calculated 2D Dice scores on a single slice for each subject. Could the authors specify how this single slice is chosen for each subject? Is it randomly chosen or determined by some landmarks? It's possible that the chosen slice is between dissected slices so SAMSEG cannot segment accurately. Also from Figure 3, it seems that SAMSEG outperforms Photo-SynthSeg on large tissues, WM/Cortex/Ventricle. Is there an explanation for this observation?

4) In the third experiment, quantitative evaluation of 3D reconstruction, each digital slice went through random affine transformations and illumination fields only. However, it's better to deform digital slices using random non-linear warping due to the non-rigidity of the brain as mentioned in 2). So, the reconstruction errors estimated here are quite optimistic. It would be more realistic if digital slices were deformed using random non-linear warping.

Overall, this is quite useful a toolset that could be widely used in many brain banks without MRI scanners.

Reviewer #1 (Public Review):

Gumaste et al studied if a parameter of odor plumes, the intermittency can be detected by an animal species, such as mice that heavily rely on olfaction to navigate and search for food and mates, among other behaviors. They also ask if the animals can extract information from this to gain knowledge about the odor source. Intermittency is defined as the fraction of time an odorant is present at a sampled point within the odor plume space. Their findings could be summarized as follows: they found that animals are capable of detecting differences in intermittency levels and suggest that this parameter of odor plumes is important for odor-based navigation in mammals, as it has been seen in other animals such as flying insects. The authors used a combination of behavioral training while concomitantly performing calcium imaging of olfactory receptor neurons (input to the olfactory bulb) and also mitral cells (output of the olfactory bulb). They found that mice are able to behaviorally discriminate between odor plumes of high and low intermittency. Interestingly, they found that the response of both input and output neurons of the olfactory bulb is capable to encode the intermittency experienced by the animals. The methods utilized in this work are very well suited for the kind of questions that the authors are asking. The combination of behavior and imaging, as opposed to only anesthetized imaging gives the authors a lot of power to interpret their data. A very relevant point is the generation of the olfactory stimuli that will be used to test the animals. The authors go to great lengths to generate more naturalistic odorant stimulations, as opposed to the typically used square pulses. Although there are some issues that can be addressed, the authors succeeded in answering the questions they set at the beginning of this work, and their conclusions are supported by their experiments. This work would generate interest among a relatively broad audience because the issue presented here (how the temporal structure of the odor plume affects the detection and encoding of an odorant) is novel in mice olfactory research.

Reviewer #2 (Public Review):

The study from Gumaste et al investigates whether mice can use changes of intermittency, a temporal odor feature, to locate an odor source. First, the study tries to demonstrate that mice can discriminate between low and high intermittency and that their performance is not affected by the odor used or the frequency of odor whiffs. Then, they show that there is a correlation between glomerular responses (OSNs and mitral cells) and intermittency. Finally, they conclude that sniffing frequency impacts the behavioral discrimination of intermittency as well as its neural representation. Overall, the authors seek to demonstrate that intermittency is an odor-plume property that can inform olfactory navigation.

The paper explored an interesting question, the use of intermittency of an odor plume as a behavioral cue, which is a new and intriguing hypothesis. However, it falls short in demonstrating that the animal is actually sensitive to intermittency but not other flow parameters, and is missing some important details.

Major concerns

1) One of the cornerstones of this paper consists in showing that mice are behaviorally able to distinguish among different intermittency values (high or low), across a variety of different stimuli and without confounds such as the number of whiffs or concentration. However, I could not find in the paper a convincing explanation of how these confounds were tested. It is clear that the authors repeat their measurements in different conditions (low or high concentration, and different whiff numbers) but it is not specified how: do the authors mix all stimuli in the same session, and so the animals simply generalize across all the stimuli and only consider intermittency for the behavioral choices? Or do authors repeat different sessions for different parameters? For example: do they perform two separate sessions with low concentration and high concentration? If this last one is the case, I would argue that this is not enough proof that animals generalize across concentrations, as the animals might simply use concentration as a cue and change the decision criteria at each session. Please clarify.

2) It looks to me that the measure of intermittency strongly depends on the set. What is the logic of setting a specific threshold? Do the results hold when this threshold changes within a reasonable range? The same questions (maybe even more important) go for the measure of glomerular intermittence. Unfortunately, a sensitivity analysis for both measures is missing, which makes it hard to interpret the results.

3) The logic of choosing the decision boundary for the discrimination task is not clear: low intermittency is considered to be below 0.15 and high intermittency is considered to be between 0.2 and 0.8. Do these values correspond to natural intermittency distribution? How were these values chosen?

4) Only 2 odors were used in the whole study and some results were in disagreement between the two odors. By looking at only two odors it is very difficult to make a general conclusion about intermittency encoding in the OB.

5) Assuming that all the above issues are resolved, one can conclude that intermittency can be perceived by an animal. The study puts a strong accent on the fact that this feature could be used for navigation. I understand that it is extremely hard to demonstrate that this feature is actually used for navigation, however, the analysis of relevance of this measure is missing. Even if it is used in navigation, most probably this would be in combination with other features, thus its relative importance needs to be discussed, or even better, established.

Reviewer #3 (Public Review):

In this study, Gumaste et al. aim to determine whether mice can discriminate odor intermittency and whether the olfactory bulb encodes intermittency. Using a Go/No-Go task, the study first showed that mice can be trained to discriminate odor stimuli with a low versus high intermittency value. Next, the authors demonstrated that early olfactory processing in the OSNs and mitral/tufted cells encodes intermittency. Through calcium imaging of olfactory bulb glomeruli, they obtained the glomerular response properties across intermittency and demonstrated the effects of sniff frequency on the glomerular representation of intermittency. Although the results are expected based on previous literature, they do lend support to the notion that intermittency can be used for odor-guided navigation.

Strengths:

The counterbalanced olfactometer used in this study keeps the air flow constant while odor concentration changes. This design is very useful for experiments in which odor delivery needs to be precisely controlled.

In a Go/No-Go task, mice were successfully trained to discriminate CS+ versus CS- odor stimuli with high versus low intermittency values in three different stimulus types (termed naturalistic, binary naturalistic, and square wave).

The olfactory bulb glomerular activity (from either olfactory sensory neurons or mitral/tufted cells) was monitored while mice performing the behavioral tasks, supporting that intermittency coding could arise from early olfactory processing.

Weaknesses:

Alternative interpretations of the behavioral outcome could be better discussed. For instance, the odors delivered with high intermittency values may lead to higher odor concentrations that olfactory sensory neurons encounter in the mucus. Mice might discriminate the total amount of odors present in the mucus rather than intermittency.

The conclusion that intermittency encoding is odor specific and depends on the spatial patterning/intrinsic glomerular properties is only based on two odorants used in this study.

Reviewer #1 (Public Review):

With MERGEseq, the authors sought to develop a scalable and accessible method for getting both projectome and transcriptome information at the single-cell level from multiple projection targets within a single animal. MERGEseq uses a retro rAAV2 to deliver a 15-nucleotide barcode driven by a CAG promoter with co-expression of eGFP to enrich barcoded cells using FACS. Injection of this rAAV2 in distinct regions (with each injection region distinguished by a unique barcode that is specific to the virus used) allows retrograde trafficking and expression of the barcodes in cells that project to the injected region. In this manuscript, rAAVs harboring 5 unique barcodes were stereotactically delivered to 5 targets of the mouse: dorsomedial striatum (DMS), mediodorsal thalamic nucleus (MD), basal amygdala (BLA), lateral hypothalamus (LH), and agranular insular cortex (AI). After a 6-week period to allow for viral transduction and expression, the ventromedial prefrontal cortex (vmPFC) was harvested for scRNAseq. vmPFC scRNAseq data were validated against previously published PFC datasets, demonstrating that MERGEseq does not disrupt transcript expression and identifies the same principal cell types as annotated in previous studies. Importantly, MERGEseq enabled the identification of cell types in the vmPFC that project to distinct areas, with separation occurring largely based on cell type and cortical layer. The application of stringent criteria for barcode index determination is rigorous and improves confidence that barcoded cells are correctly identified. The observation that all barcoded cells were excitatory is consistent with prior work, although it is not clear if viral tropism contributes to this in some way. In a parallel experiment, FAC-sorted cells (vmPFC cells expressing EGFP) were isolated as a comparison. Notably, EGFP+ cells were exclusively excitatory neurons, consistent with literature showing PFC projection neurons are excitatory. Next, barcode analysis was combined with transcriptional identification of neuronal subtypes to define general projection patterns and single-cell projection patterns, which were validated by the DMS and MD in situ using retrograde tracing in combination with RNA FISH. MERGEseq data were also used to identify transcriptional differences between neurons with dedicated and bifurcated projections. DMS+LH and DMS+MD projecting neurons had distinct transcriptional profiles, unlike cells with other targets. RNA FISH for marker gene Pou3f and retrograde tracing from DMS+LH projecting cells demonstrate enrichment of this gene in this projection population. Finally, machine-learning was used to predict projection targets based on transcriptional profiles. In this dataset, 50 highly variable genes (HVGs) were optimal for predicting projection patterns, though this might vary in different circuits. Overall, the results of this manuscript are well presented and include rigorous validation for select vmPFC targets with in situ techniques. The application of unique barcodes for retro-AAV delivery is an accessible tool that other labs can implement to study other brain circuits.

Ultimately, MERGEseq is a subtle conceptual advancement over VECTORseq (retro-AAV delivered transgenes rather than barcodes, in combination with scRNAseq) that offers higher confidence in the described projectome diversity in comparison. The use of a retrograde AAV inherently limits the number of projection areas that can be assessed, a weakness compared to anterograde approaches such as MAPseq/BARseq. However, BARseq demands more time and resources; further, the use of the highly toxic Sindbis virus limits the application of this technique. This manuscript builds upon previous work by utilizing machine learning to predict projection targets. BARseq2 could be used to rigorously validate predicted projectomes and gain single-cell information regarding target neurons. Overall, MERGEseq is an accessible technique that can be used across many animal models and serve as an important starting point to define circuits at the single-cell level.

Reviewer #2 (Public Review):

Investigating the relationship between transcriptomic profiles, their axonal projection and collateralization patterns will help define neuronal cell types in the mammalian central nervous system. The study by Xu et al. combined multiple retrograde viruses with barcodes and single-cell RNA-sequencing (MERGE-seq) to determine the projection and collateralization patterns of transcriptomically defined ventral medial prefrontal cortex (vmPFC) projection neurons. They found a complex relationship: the same transcriptomically defined cell types project to multiple target regions, and the same target region receives input from multiple transcriptomic types of vmPFC neurons. Further, collateralization patterns of vmPFC to the five target regions they investigated are highly non-random.

While many of the biological conclusions are not surprising given recent studies on the collateralization patterns of vmPFC neurons using single neuron tracing and other methods that integrate transcriptomics and projections, MERGE-seq provides validation, at the single cell level, collateralization patterns of individual vmPFC neurons, and thus offer new and valuable information over what has been published. The method can also be used to study collateralization patterns of other neuron types.

Some of the conclusions the authors draw depend on the efficiency of retrograde labeling, which was not determined. Without quantitative information on retrograde labeling efficiency, and unless such efficiency is close to 100%, these conclusions are likely misleading.

Reviewer #3 (Public Review):

This manuscript describes a multiplexed approach for the identification of transcriptional features of neurons projecting to specific target areas at the single-cell level. This approach, called MERGE-seq, begins with multiplexed retrograde tracing by injecting distinctly barcoded rAAV-retro viruses into different target areas. The transcriptomes and barcoding of neurons in the source area are then characterized by single-cell RNA sequencing (scRNAseq) on the 10xGenomics platform. The projection targets of barcoded neurons in the source area can be inferred by matching the detected barcodes to the barcode sequences to of rAAV-retro viruses injected into the target areas.

The authors validated their approach by injecting five rAAV-retro GFP viruses, each encoding a different barcode, into five known targets of the ventromedial prefrontal cortex (vmPFC). The transcriptomes and barcoding of vmPFC neurons were then analyzed by scRNA-seq with or without enrichment of retrogradely labeled neurons based on GFP fluorescence. The authors confirmed the previously described heterogeneity of vmPFC neurons. In addition, they showed that most transcriptionally defined cell types project to multiple targets and that the five targets received projections from multiple transcriptomic types. The authors further characterized the transcriptomic features of barcoded vmPFC neurons with different projection patterns and defined Pou3f1 as a marker gene of neurons extending collateral branches to the dorsomedial striatum and lateral hypothalamus.

Overall, the results of the manuscript are convincing: the transcriptomic vmPFC cell types defined by scRNAseq in this study appear to correlate well with previous studies, the bifurcated projection patterns inferred by barcoding are validated using dual-color retro-AAV tracing, and marker genes for projection-specific cell subclasses are validated in retrogradely labeled vmPFC using RNA FISH for marker detection.

The concept of combining retrograde tracing and scRNAseq is not new. Previous studies have applied recombinase-expressing viruses capable of retrograde labeling, such as CAV, rabies virus, and AAV2-Retro, to retrogradely label and induce the expression of fluorescence markers in projection neurons, therefore facilitating enrichment and analysis of neurons projecting to a specific target. Multiplexed analysis can be achieved with the combination of different reporter viruses or viruses expressing different recombinases and appropriate reporter mouse lines. The advantages of MERGE-seq include that no transgenic lines are required and that it could be applied at even higher levels of multiplexity.

However, previously existing datasets that have already profiled this region with scRNAseq have not been utilized to their full extent. Therefore, for the proper context with prior literature, bioinformatic integration of these scRNAseq and prior scRNAseq data is needed.

Moreover, robust detection of barcodes in neurons labeled by barcoded AAV-retro viruses remains a challenge. The authors should clearly discuss the difficulties with barcode detection in this approach, as well as discuss potential solutions, which are important for others interested in its approach.

While this study is limited to the five known targets of vmPFC, the results suggest that MERGE-seq is a valuable tool that could be used in the future to characterize projection targets and transcriptomes of neurons in a multiplexed manner. As MERGE-seq uses AAVs to deliver barcodes, this method has the potential for application in model organisms for which transgenic lines are not available. Further improvements in experimental design and data analysis should be considered when applying MERGE-seq to poorly characterized source areas or with increased multiplexity of target areas.

In summary, this is a valuable approach, but the authors should clearly provide the context for their study within the existing literature, transparently discuss the limitations of MERGE-seq, as well as suggest improvements for the future.

Reviewer #1 (Public Review):

This study characterized the role of the Drosophila odorant-binding protein Obp56g in mediating post-mating responses in females. The authors show that this Obp56g is expressed in the male ejaculatory bulb, use genetic approaches to disrupt Obp56g, and show that males with disrupted Obp56g fail to form mating plugs in their mates.

Despite the fact that Obp56g deficient males generate and transfer sperm normally, the lack of formation of a functional mating plug leads to sperm loss in females mated to these males and thus a failure to induce normal post-mating responses.

This study identifies an unexpected role for an Obp and raises new questions about the function of this class of protein and the variety of roles that they may play in sensory function and reproduction.

Reviewer #2 (Public Review):

Here, Brown and colleagues report a valuable finding on the function and evolution of the seminal odorant-binding protein Obp56g in Drosophila melanogaster. Previous studies have shown that this family of proteins is highly expressed in olfactory tissues like the antennae and maxillary palps. Some of these proteins have been shown to mediate behavioural responses to specific odorants-hence the general moniker odorant binding proteins. This slightly misleading historical naming convention implies an exclusive role in olfaction-however, many of these proteins are expressed in other tissues of the animal, including the male reproductive system. In addition, seminal fluid proteins exhibit a fascinating evolutionary history, with rapid evolution and turnover across taxa.

The authors suggest that the Obp56g protein may have been co-opted for a reproductive role in Drosophila melanogaster during evolution. The authors show that Obp56g is required for male fertility and the induction of the post-mating response in females. Mutant males lacking Obp56g fail to form a mating plug in the female reproductive tract-leading to ejaculate loss and reduced sperm storage. The experimental evidence supporting the claims of the authors is solid and compelling. The data were collected and analyzed using solid and validated methodologies. The author's findings can be used as a starting point for understanding the mechanistic roles of this family of proteins in mating plug coagulation. The work will interest biologists studying non-sperm seminal fluid protein function and evolution.

Reviewer #3 (Public Review):

Male seminal fluid proteins play a crucial role in fertility and influence female physiology and behavior after mating. Brown et al. have discovered a new reproductive function for odorant-binding proteins (Obps) in Drosophila. The study shows that Obp56g is expressed in male reproductive tissues that produce seminal fluid proteins and is required for the formation of the mating plug in the mated female. The study demonstrates that RNAi knockdown and CRISPR/Cas9-generated mutations in Obp56g result in a defective mating plug, reduced sperm storage, and subsequent effects on female post-mating responses. The research also suggests that Obp56g has been co-opted for a reproductive function over evolutionary time, as supported by functional and comparative RNAseq data across Drosophila species. Finally, the study reports expression shifts, duplication, and divergence in the evolution of these seminal protein genes.

Overall, the study represents a significant contribution to our understanding of seminal proteins and their reproductive function. The creation of novel Obp mutants using CRISPR/Cas9 technology is a valuable resource for future research in the Drosophila community. The manuscript successfully conveys the key findings and their potential implications for the field. However, to reinforce the study's conclusions, more quantitative data is necessary. Furthermore, improving the statistical analysis and incorporating additional genetic controls would enhance the quality of the study and provide a stronger foundation for its conclusions.

Reviewer #1 (Public Review):

In this paper, the authors develop new models of sequential effects in a simple Bernoulli learning task. In particular, the authors show evidence for both a "precision-cost" model (precise posteriors are costly) and an "unpredictability-cost" model (expectations of unpredictable outcomes are costly). Detailed analyses of experimental data partially support the model predictions.

Strengths:<br /> - Well-written and clear.<br /> - Addresses a long-standing empirical puzzle.<br /> - Rigorous modeling.

Weaknesses:<br /> - No model adequately explains all of the data.<br /> - New empirical dataset is somewhat incremental.<br /> - Aspects of the modeling appear weakly motivated (particularly the unpredictability model).<br /> - Missing discussion of some relevant literature.

Reviewer #2 (Public Review):

This paper argues for an explanation of sequential effects in prediction based on the computational cost of representing probability distributions. This argument is made by contrasting two cost-based models with several other models in accounting for first- and second-order dependencies in people's choices. The empirical and modeling work is well done, and the results are compelling.

The main weaknesses of the paper are as follows:

1. The main argument is against accounts of dependency based on sensitivity to statistics (ie. modeling the timeseries as having dependencies it doesn't have). However, such models are not included in the model comparison, which makes it difficult to compare these hypotheses.

2. The task is not incentivized in any way. Since incentives are known to affect probability-matching behaviors, this seems important. In particular, we might expect incentives would trade off against computational costs - people should increase the precision of their representations if it generates more reward.

3. The sample size is relatively small (20 participants). Even though a relatively large amount of data is collected from each participant, this does make it more difficult to evaluate the second-order dependencies in particular (Figure 6), where there are large error bars and the current analysis uses a threshold of p < .05 across a large number of tests hence creating a high false-discovery risk.

4. In the key analyses in Figure 4, we see model predictions averaged across participants. This can be misleading, as the average of many models can produce behavior outside the class of functions the models themselves can generate. It would be helpful to see the distribution of raw model predictions (ideally compared against individual data from humans). Minimally, showing predictions from representative models in each class would provide insight into where specific models are getting things right and wrong, which is not apparent from the model comparison.

Reviewer #3 (Public Review):

This manuscript offers a novel account of history biases in perceptual decisions in terms of bounded rationality, more specifically in terms of finite resources strategy. Bridging two works of literature on the suboptimalities of human decision-making (cognitive biases and bounded rationality) is very valuable per se; the theoretical framework is well derived, building upon the authors' previous work; and the choice of experiment and analysis to test their hypothesis is adequate. However, I do have important concerns regarding the work that do not enable me to fully grasp the impact of the work. Most importantly, I am not sure whether the hypothesis whereby inference is biased towards avoiding high precision posterior is equivalent or not to the standard hypothesis that inference "leaks" across time due to the belief that the environment is not stationary. This and other important issues are detailed below. I also think that the clarity and architecture of the manuscript could be greatly improved.

1. At this point it remains unclear what is the relationship between the finite resources hypothesis (the only bounded rationality hypothesis supported by the data) and more standard accounts of historical effects in terms of adaptation to a (believed to be) changing environment. The Discussion suggests that the two approaches are similar (if not identical) at the algorithmic level: in one case, the posterior belief is stretched (compared to the Bayesian observer for stationary environments) due to precision cost, in other because of possible changes in the environment. Are the two formalisms equivalent? Or could the two accounts provide dissociable predictions for a different task? In other words, if the finite resources hypothesis is not meant to be taken as brain circuits explicitly minimizing the cost (as stated by the authors), and if it produces the same type of behavior as more classical accounts: is the hypothesis testable experimentally?

2. The current analysis of history effects may be confounded by effects of the motor responses (independently from the correct response), e.g. a tendency to repeat motor responses instead of (or on top of) tracking the distribution of stimuli.

3. The authors assume that subjects should reach their asymptotic behavior after passively viewing the first 200 trials but this should be assessed in the data rather than hypothesized. Especially since the subjects are passively looking during the first part of the block, they may well pay very little attention to the statistics.

4. The experiment methods are described quite poorly: when is the feedback provided? What is the horizontal bar at the bottom of the display? What happens in the analysis with timeout trials and what percentage of trials do they represent? Most importantly, what were the subjects told about the structure of the task? Are they told that probabilities change over blocks but are maintained constant within each block?

Reviewer #3 (Public Review):

In this study, Yang et al. address a fundamental question of the role of dorsal striatum in neural coding of gait. The authors study the respective roles of D1 and D2 MSNs by linking their balanced activity to detailed gait parameters. In addition, they put in parallel the striatal activity related to whole-body measures such as initiation/cessation of movement or body speed. They are using an elegant combination of high-resolution single-limb motion tracking, identification of bouts of movements, and electrophysiological recordings of striatal neurons to correlate those different parameters. Subpopulations of striatal output neurons (D1 and D2 expressing neurons) are identified in neural recordings with optogenetic tagging. Those complementary approaches show that a subset of striatal neurons have phase-locked activity to individual limbs. In addition, more than a third of MSNs appear to encode all three aspects of motor behavior addressed here, initiation/cessation of movement, body speed, and gait. This activity is balanced between D1 and D2 neurons, with a higher activity of D1 neurons only for movement initiation. Finally, alterations of gait, and the associated striatal activity, are studied in a mouse model of Parkinson's Disease, using 6-OHDA lesions in the medial forebrain bundle (MFB). In the 6OHDA mice, there is an imbalance toward D2 activity.

Strengths:<br /> There is a long-standing debate on the respective role of D1 and D2 MSNs on the control of movement. This study goes beyond prior work by providing detailed quantification of individual limb kinematics, in parallel with whole-body motion, and showing a high proportion of MSNs to be phase-locked to precise gait cycle and also encoding whole-body motion. The temporal resolution used here highlights the preferential activity of D1 MSN at the movement starts, whereas previous studies described a more balanced involvement. Finally, they reveal neural mechanisms of dopamine depletion-induced gait alterations, with a preponderant phase-locked activity of D2 neurons. The results are convincing, and the methodology supports the conclusions presented here.

Weaknesses:<br /> Some more detailed explanations would improve the clarity of the results in the corresponding section. Analysis of the 6OHDA experiments could be expanded to extract more relevant information.

Reviewer #1 (Public Review):

Summary:<br /> Yang et al combine high-speed video tracking of the limbs of freely moving mice with in vivo electrophysiology to demonstrate how striatal neurons encode single-limb gait. They also examine encoding other well-known aspects of locomotion, such as movement velocity and the initiation/termination of movement. The authors show that striatal neurons exhibit rhythmic firing phase-locked with mouse gait, while mice engage in spontaneous locomotion in an open field arena. Moreover, they describe gait deficits induced by severe unilateral dopamine neuron degeneration and associate these deficits with a relative strengthening of gait-modulation in the firing of D2-expressing MSNs. Although the source and function of this gait-modulation remain unclear, this manuscript uncovers an important physiological correlate of striatal activity with gait, which may have implications for gait deficits in Parkinson's Disease.

Strengths:<br /> While some previous work has looked at the encoding of gait variables in the striatum and other basal ganglia nuclei, this paper uses more careful quantification of gait with video tracking. In addition, few if any papers do this in combination with optically-labeled recordings as were performed here.

Weaknesses:<br /> The data collected has a great richness at the physiological and behavioral levels, and this is not fully described or explored in the manuscript. Additional analysis and display of data would greatly expand the interest and interpretability of the findings.

There are also some caveats to the interpretation of the analyses presented here, including how to compare encoding of gait variables when animals have markedly different behaviors (eg comparing sham and unilaterally 6-OHDA treated mice), or how to interpret the loss of gait modulation when single unit activity is overall very low.

1. The authors use circular analysis to quantify the degree to which striatal neurons are phase-locked to individual limbs during gait. The result of this analysis is shown as the proportion of units phase-locked to each limb, vector length, and vector angle (Fig 2H-K; Fig 4E-F; Fig 6E-F). Given that gait is a cyclic oscillation of the trajectories of all four limbs, one could expect that if one unit is phase-locked to one limb, it will also be phase-locked to the other three limbs but at a different phase. Therefore, it is not clear in the manuscript how the authors determine to which limb each unit is locked, and how some units are locked to more than one limb (Fig 2H). More methodological/analytical detail would be especially helpful.

2. In Figures 2 and 3, the authors describe the modulation of striatal neurons by gait, velocity, and movement transitions (start/end), with most of their examples showing firing rates compatible with rates typical of striatal interneurons, not MSNs. In order to have a complete picture of the relationship between striatal activity and gait, a cell type-specific analysis should be performed. This could be achieved by classifying units into putative MSN, FS interneurons, and TANs using a spike waveform-based unit classification, as has been done in other papers using striatal single-unit electrophysiology. An example of each cell type's modulation with gait, as well as summary data on the % modulation, would be especially helpful.

3. By normalizing limb trajectories to the nose-tail axis, the analysis ignores whether the mouse is walking straight, or making left/right turns. Is the gait-modulation of striatal activity shaped by ipsi- and contralateral turning? This would be especially important to understand changes in the unilateral disease model, given the imbalance in turning of 6-OHDA mice.

4. It looks like the data presented in Figure 4 D-F comes from all opto-identified D1- and D2-MSNs. How many of these are gait-modulated? This information is missing (line 110). Pooling all units may dilute differences specific to gait-modulated units, therefore a similar analysis only on gait-modulated units should be performed.

5. Since 6-OHDA lesions are on the right hemisphere, we would expect left limbs to be more affected than right limbs (although right limbs may also compensate). It is therefore surprising that RF and RR strides seem slightly shorter than LF and LR (Fig 5G), and no differences in other stride parameters (Fig 5H-J). Could the authors comment on that? It may be that this is due to rotational behavior. One interesting analysis would be to compare activity during similar movements in healthy and 6-OHDA mice, eg epochs in which mice are turning right (which should be present in both groups) or walking a few steps straight ahead (which are probably also present in both groups).

6. Multiple publications have shown that firing rates of D1-MSN and D2-MSN are dramatically changed after dopamine neuron loss. Is it possible that changes observed in gait-modulation might be biased by changes in firing rates? For example, dMSNs have exceptionally low overall activity levels after dopamine depletion (eg Parker...Schnitzer, 2018; Ryan...Nelson, 2018; Maltese...Tritsch, 2021); this might reduce the ability to detect modulation in the firing of dMSNs as compared to iMSNs, which have similar or increased levels of activity in dopamine depleted mice. Does vector length correlate with firing rate? In addition, the normalization method used (dividing firing rate by minimum) may amplify very small changes in absolute rates, given that the firing rates for MSN are very low. The authors could show absolute values or Z-score firing rates (Figure 6 A, D).

7. The analysis shown in Fig 3C should also be done for opto-identified D1- and D2-MSNs (and for waveform-based classified units as noted above).

8. Discussion: the origin of the gait-modulation as well as the possible mechanisms driving the alterations observed in 6-OHDA mice should be discussed in more detail.

Reviewer #2 (Public Review):

Summary:<br /> Yang et al. recorded the activity of D1- and D2-MSNs in the dorsal striatum and analyzed their firing activity in relation to single-limb gait in normal and 6-OHDA lesioned mice. Although some of the observations of striatal encoding are interesting, the novelty and implications of this firing activity in relation to gait behavior remain unclear. More specifically, the authors made two major claims. First, the striatal D1- and D2-MSNs were phase-locked to the walking gait cycles of individual limbs. Second, dopamine lesions led to enhanced phase-locking between D2-MSN activity and walking gait cycles. The second claim was supported by the increase of vector length in D2-MSNs after unilateral 6-OHDA administration to the medial forebrain bundle. However, for the first claim, the authors failed to convincingly demonstrate that striatal MSNs were more phase-locked to gait with single-limb and step resolution than to the global gait cycles.

Strengths:<br /> It is a technically advanced study.

Weaknesses:<br /> 1. The authors focused on striatal encoding of gait information in current studies. However, it remains unclear whether the part of the striatum for which the authors performed neuronal recording is really responsible for or contributing to gait control. A lesion or manipulation experiment disrupting the part of the striatum recorded seems a necessary step to test or establish its relationship to gait control.

2. The authors attributed one of the major novelties to phase-locking of striatal neural activities with single-limb gait cycles. The claim was not clearly supported, as the authors did not demonstrate that phase-locking to single-limb gaits was more significant than phase-locking to global walking gait cycles. In rhythmic walking, the LR and RF limbs were roughly anti-phase with the LF and RR limbs (Fig. 1D, E). In line with this relationship, striatal neurons were mainly in-phase with LR and RF limbs and anti-phase with LF and RR limbs (Fig. 2J, K). One could instead interpret this as the striatal neurons spanned all the phases of the global walking gait cycles (Fig. 3D). To demonstrate phase-locking with individual limb movements, the authors need to show that neural activities were better correlated with a specific limb than to the global gait cycles.

3. The observation of the enhancement of coupling between D2 MSN firing and the gait cycles was interesting, but the physiological interpretation was not clear (as the authors also noted in the Discussion), which hampers the significance of the observation.

4. Due to the lack of causality experiments as mentioned in the first comment above, the observations of coupling between striatal neuronal activity and gait control might well result from a third brain region/factor serving as the common source to both, whether in normal or dopamine lesioned brain. If this is the case, the significance and implications of current findings will be greatly limited.

Reviewer #1 (Public Review)

This work challenges previously published results regarding the presence and abundance of 6mA in Drosophila genome, as well as the claim that the TET or DMAD enzyme serves as the "eraser" of this DNA methylation mark and its roles in development. This information is needed to clarify these questions in the field. Generally speaking, the methods for fly husbandry and treatment seem to be in accordance with those established ones in the field.

Here are a couple of suggestions that could be discussed with the current work and addressed in the future, in order to better understand the roles of 6mA and TET.

1. Regarding the estimated "200 to 400 methylated adenines per haplogenome", some insights regarding where they are enriched in the genome could inform the potential target sites regulated by 6mA.

2. The TET-GFP and TET-CD-GFP knock-in lines give proper nuclear localization and could be used to identify genomic regions bound with full-length TET and TET-CD using anti-GFP for ChIP-seq or CUT&RUN (or CUT&TAG).

Reviewer #2 (Public Review)

DNA adenine methylation (6mA) is a rediscovered modification that has been described in a wide range of eukaryotes. However, 6mA presence in eukaryote remains controversial due to low abundance of its modification in eukaryotic genome. In this manuscript, Boulet et al. re-investigate 6mA presence in drosophila using axenic or conventional fly to avoid contaminant from feeding bacteria. By using these flies, they find that 6mA is rare but present in drosophila genome by performing LC/MS/MS. They also find that the loss of TET (also known as DMAD) does not impact on 6mA levels in drosophila, contrary to previous studies. In addition, the authors find that TET is required for fly development in its enzymatic activity-independent manner.

The strength of this study is, compared to previous studies of 6mA in drosophila, the authors employ axenic or conventional fly for 6mA analysis. These fly strains make it possible to analyze 6mA presence in drosophila without bacterial contaminant. This established method is valuable in this field.

Reviewer #1 (Public Review):

Summary:

Using chromaffin cells as powerful model systems for studying secretion, the authors study the regulatory role of complexin in secretion. Complexin is still enigmatic in its regulatory role, as it both provides inhibitory and facilitatory functions in release. The authors perform an extensive structure-function analysis of both the C- and N-terminal regions of complexin. There are several interesting findings that significantly advance our understanding of cpx/SNARe interactions in regulating release. C-terminal amphipathic helix interferes with SNARE complex assembly and thus clamps fusion. There are acidic residues in the C-term that may be seen as putative interaction partners for Synaptotagmin. The N-terminus of Complexin promoting role may be associated with an interaction with Syt1. In particular, the putative interaction with Syt1 is of high interest and supported by quite strong functional and biochemical evidence. The experimental approaches are state-of-the-art, and the results are of the highest quality and convincing throughout. They are adequately and intelligently discussed in the rich context of the standing literature. Whilst there are some concerns about whether the facilitatory actions of complexion have to be tightly linked to Syt1 interactions, the proposed model will significantly advance the field by providing new directions in future research.

I have only minor comments related to the interpretation of the data:

Fig 5 While the data very nicely show that CPX and Syt1 have interdependent interactions in the chromaffin neurons, this seems to be not the case in neurons, where the loss of complexins and synaptotagmins have additive effects, suggesting independent mechanisms (eg Xue et al., 2010). This would be a good opportunity to discuss some possible differences between secretion in endocrine cells vs neurons.

Fig 8 Shows an apparent shift in Ca sensitivity in N-terminal mutants suggesting a modification of Ca sensitivity of Syt1. Could there be also an alternative mechanism, that explains this phenotype which is based on a role of the n-term lowering the energy barrier for fusion, that in turn shifts corresponding fusion rates to take place at lower Ca saturation levels?

Reviewer #2 (Public Review):

Summary:

Complexin (Cplx) is expressed at nearly all chemical synapses. Mammalian Cplx comes in four different paralogs which are differentially expressed in different neuron types, either selectively or in combination with one or two other Cplx isoforms. Cplx binds with high affinity to assembled SNARE complexes and promotes AP-evoked release by increasing vesicle fusogenicity. Cplx is assumed to preclude premature SV fusion by preventing full SNARE assembly, thereby arresting subsequent SNARE-driven fusion ("fusion-clamp" theory). The protein has multiple domains, the functions of which are controversially discussed. Cplx's function has been studied in a variety of model organisms including mice, flies, worms, and fish with seemingly conflicting results which led to partly contradicting conclusions.

Makee et al. study the function of mammalian Cplx2 by making use of chromaffin cells derived from Cplx2 ko mice as a system to overexpress and functionally characterize mutant Cplx2 forms. This work is an important extension of previous studies of the same lab using similar techniques. The main conclusion of the present study are:

The hydrophobic character of the amphipathic helix in Cplx's C-terminal domain is essential for inhibiting premature vesicle fusion at a [Ca2+]i of several hundreds of nM (pre-flash [Ca2+]i). The Cplx-mediated inhibition of fusion under these conditions does not rely on the expression of either Syt1 or Syt7.

Slow-down of exocytosis by N-terminally truncated Cplx mutants in response to a [Ca2+]i of several µM (peak flash [Ca2+]i) occurs regardless of the presence or absence of Syt7 demonstrating that Cplx2 does not act as a switch favoring preferential assembly of the release machinery with Syt1,2 rather than the "slow" sensor Syt7.

Cplx's N-terminal domain is required for the Cplx2-mediated increase in the speed of exocytosis and faster onset of exocytosis which likely reflect an increased apparent Ca2+ sensitivity and faster Ca2+ binding of the release machinery.

Strengths:

The authors perform systematic truncation/mutational analyses of Cplx2 by making use of chromaffin cells derived from Cplx2 ko mice. They analyze the impact of single and combined deficiencies for Cplx2 and Syt1 to establish interactions of both proteins.

State-of-the-art methods are employed: Vesicle exocytosis is assayed directly and with high resolution using capacitance measurements. Intracellular [Ca2+] is controlled by loading via the patch-pipette and by UV-light-induced flash-photolysis of caged [Ca2+]. The achieved [Ca2+ ] is measured with Ca2+ -sensitive dyes.

The data is of high quality and the results are convincing.

Weaknesses:

The authors provide a "chromaffin cell-centric" view of the function of mammalian Cplx in vesicle fusion. With the exception of mammalian retinal ribbon synapses (and some earlier RNAi knockdown studies that had off-target effects), there is very little evidence for a "fusion-clamp"-like function of Cplxs in mammalian synapses. At conventional mammalian synapses, genetic loss of Cplx (i.e. KO) consistently decreases AP-evoked release, and generally either also decreases spontaneous release rates or does not affect spontaneous release, which is inconsistent with a "fusion-clamp" theory. This is in stark contrast to invertebrate (D. m. and C. e.) synapses where genetic Cplx loss is generally associated with strong upregulation of spontaneous release, providing support for Cplx acting as a "fusion-clamp".

The authors use a Semliki Forest virus-based approach to express mutant proteins in chromaffin cells. This strategy leads to a strong protein overexpression (~7-8fold, Figure 3 Suppl. 1). Therefore, experimental findings under these conditions may not necessarily be identical to findings with normal protein expression levels.

Measurements of delta Cm in response to Ca2+ uncaging by ramping [Ca2+ ] from resting levels up to several µM over a time period of several seconds were used to establish changes in the release rate vs [Ca2+ ]i relationship. It is not clear to this reviewer if and how concurrently occurring vesicle endocytosis together with a possibly Ca2+-dependent kinetics of endocytosis may affect these measurements.

It should be pointed out that an altered "apparent Ca2+ affinity" or "apparent Ca2+ binding rate" does not necessarily reflect changes at Ca2+-binding sites (e.g. Syt1).

There are alternative models on how Cplx may "clamp" vesicle fusion (see Bera et al. 2022, eLife) or how Cplx may achieve its regulation of transmitter release without mechanistically "clamping" fusion (Neher 2010, Neuron). Since the data presented here cannot rule out such alternative models (in this reviewer's opinion), the authors may want to mention and briefly discuss such alternative models.

Some parts of the Discussion are quite general and not specifically related to the results of the present study. The authors may want to consider shortening those parts.

Last but not least, the presentation of the results could be improved to make the data more accessible to non-specialists, this concerns providing necessary background information, choice of colors, and labeling of diagrams.

Reviewer #1 (Public Review):

The brain's code is not static. Neuronal activity patterns change as a result of learning, aging, and disease. Reliable tracking of activity from individual neurons across long time periods would enable detailed studies of these important dynamics. For this reason, the authors' efforts to track electrophysiological activity across days without relying on matching neural receptive fields (which can change due to learning, aging, and disease) are very important.

By utilizing the tightly-spaced electrodes on Neuropixels probes, they are able to measure the physical distance and the waveform shape 'distance' between sorted units recorded on different days. To tune the matching algorithm and validate the results, they used the visual receptive fields of neurons in the mouse visual cortex (which tend to change little over time) as ground truth. Their approach performs quite well, with a high proportion of neurons accurately matched across multiple weeks. This suggests that the method may be useable in other cases where the receptive fields can't be used as ground truth to validate the tracking. This potential extendibility to tougher applications is where this approach holds the most promise.

The main caveat (and disappointment) is that this paper does not address generalizability to other experimental conditions. Because it only looks at one brain area (visual cortex), in one species (mouse), using one type of spike sorter (Kilosort), and one type of behavioral prep (head-fixed), it is not clear if this approach is overfit to those conditions or if it will perform equally well in other conditions. Most importantly, in brain areas where neuronal receptive fields are more dynamic and can't be used as a ground truth diagnostic, it isn't clear how to apply the technique outlined in this study, since many of the parameters are tuned to a very specific set of conditions using visual receptive fields as ground truth.

Reviewer #2 (Public Review):

The manuscript presents a method for tracking neurons recorded with neuropixels across days, based on the matching of cells' spatial layouts and spike waveforms at the population level. The method is tested on neuropixel recordings of the visual cortex carried over 47 days, with the similarity in visual receptive fields used to verify the matches in cell identity.

This is an important tool as electrophysiological recordings have been notoriously limited in terms of tracking individual neuron's fate over time, unlike imaging approaches. The method is generally sound and properly tested but I think some clarifications would be helpful regarding the implementation of the method and some of the results.

1) Page 6: I am not sure I understand the point of the imposed drift and how the value of 12µm is chosen.<br /> Is it that various values of imposed drift are tried, the EMDs computed to produce histograms as in Fig2c, values of rigid drifts estimated based on the histogram modes, and then the value associated with minimum cost selected? The corresponding manuscript section would need some clarification regarding this aspect.

2) The EMD is based on the linear sum, with identical weight, of cell distance and waveform similarity measures. How performance is affected by using a different weighting of the 2 measures (for instance, using only cell distance and no waveform similarity)? It is common that spike waveforms associated with a given neuron appear differently on different channels of silicon probes (i.e. the spike waveform changes depending on the position of recording sites relative to the neuron), so I wonder if that feature is helping or potentially impeding the tracking.

3) Fig.5: I assume the dots represent time gaps for which cell tracking is estimated. The 3 different groups of colors correspond to the 3 mice used. For a given mouse, I would expect to always see 3 dots (for ref, putative, and mixed) for a given tracking gap. However, for mouse AL036 for instance, at a tracking duration of 8 days, a dot is visible for mixed but not for ref and putative. How come this is happening?

4) Matched visual responses are measured by the sum of the correlation of visual fingerprints, which are vectors of cells' average firing rate across visual stimuli, and the correlation of PSTHs, which are implemented over all visual stimuli combined. I believe that some information is lost from combining all stimuli in the implementation of PSTHs (assuming that PSTHs show specificity to individual visual stimuli). The authors might consider, as an alternative measure of matched visual responses, a correlation of the vector concatenations of all stimulus PSTHs. Such a simpler measure would contain both visual fingerprint and PSTH information, and would not lose the information of PSTH specificity across visual stimuli.

Reviewer #1 (Public Review):

Summary:<br /> The authors have nicely demonstrated the efficiency of the HCR v.3.0 using hr38 mRNA expression as a marker of neuronal activity. This is very important in the Drosophila neuroscience field as in situ hybridization in adult Drosophila brains has been so far very challenging to do and replicate. However, this method has been described before [Choi et al., (2018)] and, if I understand correctly, is now the property of the non-profit organization molecular Technologies, who are the ones responsible for designing the probes (the sequences are not provided). Here the authors present their work as a description of a new method, called HI-FISH. However, I do not consider this as a new method but rather an application, a "proof of principle" that HCR v.3.0 can be done even on challenging tissues such as the adult Drosophila brain. Hence, if HCR v3.0 is sensitive enough and powerful enough to be used as a marker of neuronal activity, we can use it, for other neurobiological purposes, using other gene probes.<br /> To demonstrate the efficiency of HI-FISH, the authors have addressed two biological questions. The first one addressed whether specific groups of neurons, known to trigger specific behaviours (here courtship and/or aggression) are indeed activated by the behavioural context they can promote. In other words: is the behavioural output of these neurons also a trigger for their activation? The second question addressed whether this method is powerful enough to distinguish two subgroups of a class of neurons called P1 known to be involved in the two behaviours considered. In other words, are the same P1 neurons that promote aggression and courtship?

Strengths: The demonstration of the efficiency of the method is very convincing and well-performed. It gives the will for the reader to apply the method to their own subject.

Weakness: The pictures provided for HI-FISH and catFISH do not corroborate with the quantification and therefore I am not convinced about the author's biological interpretation of their data. See below for details.

Previously, using a split-gal4 line to restrict the Gal4 expression to a subset of P1 neurons, the authors have shown that these particular neurons when activated can trigger both aggressivity and courtship behaviour [Hoopfer et al., 2015]. The P1 neurons are composed of about 20 FruM neurons/hemibrain but are part of a bigger group that comprises about the same number of Fru- neurons that seem to be exclusively aggression-promoting neurons [Koganezawa et al., 2016]. Hence, this group of 40 neurons (pC1 neurons) contains aggressive-promoting neurons, courtship-promoting neurons, and perhaps neurons that can do both. Therefore, to address the first question, the authors compared hr38 expression in different groups of neurons, with a focus on subgroups, under different social contexts. While there is no ambiguity concerning the function of the Tk neurons as being exclusively aggressive-promoting neurons [Asahina et al., 2014], it is less clear when we look at the pC1 neurons. This is particularly evident for the P1a neurons which have been shown to be ambiguous as they can promote both aggression and courtship. For example, while optogenetic activation of these neurons promotes hr38 expression (Fig. 3D and fig sup. 4), it is less clear in the pictures to determine whether these specific P1a neurons labeled by the split-gal4 line are specifically activated by an aggressive behavioural context or a courtship behavioural context (Fig1, supp. 2 and fig. 4). Furthermore, the pictures chosen do not reflect the reality of the quantification (Fig. 2 B-D compared to sup. 2 or fig. 4C compared to fig. 4D) and therefore the authors conclusion. Because the drivers used are only expressed by a small subset of a larger population, I believe it would be more informative to separate in the quantification between the Gal4-expressing neurons and the non-expressing ones. Notably, based on the pictures provided, it looks like more P1 neurons (or rather pC1 neurons) are activated by a male-male encounter than by a male-female encounter. On the other hand, the splitGal4+ P1a seem to be more responsive to a courtship behavioural context (2/6 P1a neurons express hr38 in a courtship behavioural context while 0/9 _if we mentally abstract the increase of the background signal compared to the control picture_ seem to express hr38 in an aggression behavioural context). Hence, while activation of this P1asplit-Gal4 can promote both aggressive behaviour and courtship behaviour [Hoopfer et al., 2015], the authors didn't provide clear evidence (pictures not corroborating the quantification) that these specific small subpopulation of neurons are activated by one or the other or both behavioural conditions. Therefore my suggestion of differentiating in the quantification between the Gal4+ neurons from the others in the same local area.

Fig. 3, suppl. 3: In this section the authors addressed the question of whether the HI-FISH can be used to identify the downstream targets of this subpopulation. As positive controls of known downstream targets, the authors looked at the pCd population which they recently published as being an indirect downstream target of the P1a neurons [Jung et al., Neuron 2020]. They identified the Kenyon cells and a group of dopaminergic neurons, the PAM neurons as being activated by the P1a neurons. To confirm the increase of hr38 expression is indeed the result of a neuronal response of these neurons to the P1a activation, the authors used a different strategy used by them and others before. Using Gcamp signal to monitor the neuronal response of the presumably downstream targets the authors activated the P1a neurons using optogenetic (chrimson). It is important to note that they have previously shown that depending on the frequency of the light pulses activation of the P1a neurons can trigger only aggression, both aggression and wing extension or only wing extension [Hoopfer et al., eLife 2015]. Here the authors use 50Hz which is a frequency that leads to wing extension during the stimulation and aggressive behaviour at the offset of the stimulus [Hoopfer et al., eLife 2015]. Interestingly, the Gcamp experiment shows activation of the Kenyon cells and the PAM neurons but this activity is not maintained when the stimulus is turned off, suggesting that these neurons are activated during a courtship context rather than an aggressive behavioural context. I think it would be nice to see in which behavioural context the Kenyon cells and PAM neurons are activated (hr38 expression in the different behavioural context using the corresponding Gal4).<br /> Fig.4 and supp.4: The demonstration that the catFISH can now be done in Drosophila brain with a new in situ method was nicely performed. Notably, the intronic Hr38 probe appears to be an excellent marker for recent neuronal activation. However, while the optogenetic activation of the P1a neurons used to quantify the time lapse for both probes nicely distinguishes between nuclear and cytoplasmic exonic hr38, it is very difficult to use the localization of this probe in the experimental setup the authors used. Also, With their setup, I would simply use the frequency of intronic hr38 as a marker of recent activation correlating or not with the frequency of exonic hr38 marker (present in both conditions first and second encounter). This is important as this experiment addresses the second biological question. Once again, the pictures chosen absolutely do not corroborate the quantification. For example, the picture of the double encounter with the same gender male-male context clearly shows a higher number of cells that are hr38INT positive (and therefore nuclear) than the picture of the female-female context (Fig. 4C), and thus even if we only considered the P1asplit-Gal4 positive cells. In the male-male picture, 5/6 P1a cells have the Hr38INT marker while the presence of this marker is debatable in the female-female context. Especially, in some of the cells these magenta dots appear to be localized in the cytoplasm, suggesting a non-specific signal. Therefore, I would suggest to quantify the percentage of Hr38INT positive cells as the only marker for recent activation and the relative level of Hr38EXN immunostaining, and this among the P1asplit-Gal4 positive cells and the gal4- ones. A high Hr38EXN level associated with the presence of hr38INT would indicate that the cell has been activated during both encounters, while a lower hr38EXN with no hr38INT would suggest only an activation during the 1st behavioural context. Finally, a lower hr38EXN associated with the presence of hr38INT would suggest the opposite, an activation only during the 2nd behaviour.<br /> Overall, by only looking at the pictures provided, I would conclude that the HCR applied with the hr38 probes seems to efficiently work and is usable to address the question of whether a specific group of neurons are indeed activated by a specific social behavioural context. However, I would also conclude that this technique nicely demonstrated that flies are not robots and that even in a "simple" organism model such as Drosophila melanogaster individual variability is present among a group of neurons. Hence, only the quantification of the gal4-expressing neurons in comparison with their neighbor neurons known to belong to the same functional group, would allow a conclusion toward a specificity of contextual response. Therefore, although activation of a small group of neurons can be enough to trigger a specific behaviour that shouldn't happen under a certain environmental context [Hoopfer et al., eLife 2015], the results presented here suggest that we should, using this method, considering the response of the neighbour cells of the Gal4+ ones. Although currently, the quantification of the author's data does not allow such analysis, to strengthen the author's argumentation, I would distinguish in their quantification between gal4+ from the others (Fig. 2 and 4). Furthermore, I am not certain that the distinction between cytoplasmic and nuclear hr38EXN is 100% feasible (based on the pictures provided). I would instead for the hr38EXN marker only use the relative intensity (Fig. 4D).

Reviewer #2 (Public Review):

Summary:<br /> Watanabe et al establish a novel method for the activity-dependent labeling of neural circuits in flies. While activity mapping of neurons that are active during specific behaviors is widespread in rodents, the application of this method to fly circuit neuroscience is limited, mainly due to technological challenges. Thus, the present study addresses a timely problem. To do so, they apply the in situ hybridization amplification method called Hybridization Chain Reaction v. 3.0 (Choi et al. 2018) to the adult fly brain in order to visualize the expression changes of the immediate early gene (IEG) Hr38 under different types of social contexts. The conclusions of this paper are mostly very well supported by data but it would strongly benefit from additional methodological details as well as additional controls, in particular for the HI-catFISH experiments.

Strengths:<br /> The major strength of this method is its versatility and sensitivity. It can be applied to a wide variety of biological questions and assess the dynamic transcriptional regulation of an unlimited number of genes with a high signal-to-noise ratio. It will be therefore useful to many research labs working on different biological questions.

Weaknesses:<br /> Although the paper has great strengths in principle, the major weakness is the calibration of the temporal resolution of HI-CatFISH in Figure 4 and Figure Supplement 4. According to Figure Supplement 4C, close to 100% of the Hr38-positive cells are already labeled with the exonic probe 30min post-stimulation, which is not reflected in Figure 4B (there, the expression level of the exonic probe peaks 60min post-induction) and may have profound implications for the interpretation of the results. The present manuscript would strongly benefit from additional controls, such as the quantification of the intronic and exonic Hr38 probes after either only the 1st or 2nd social context but at the same timepoint than if two consecutive social contexts were tested.

Reviewer #2 (Public Review):

Summary:

The large-conductance Ca2+ activated K+ channel (BK) has been reported to promote breast cancer progression, but it is not clear how. The present study carried out in breast cancer cell lines, concludes that BK located in mitochondria reprograms cells towards the Warburg phenotype, one of the metabolic hallmarks of cancer.

Strengths:

The use of a wide array of modern complementary techniques, including metabolic imaging, respirometry, metabolomics, and electrophysiology. On the whole, experiments are astute and well-designed and appear carefully done. The use of BK knock-out cells to control for the specificity of the pharmacological tools is a major strength. The manuscript is clearly written. There are many interesting original observations that may give birth to new studies.

Weaknesses:

The main conclusion regarding the role of a BK channel located in mitochondria appears is not sufficiently supported. Other perfectible aspects are the interpretation of co-localization experiments and the calibration of Ca2+ dyes. These points are discussed in more detail in the following paragraphs:

1. May the metabolic effects be ascribed to a BK located in mitochondria? Unfortunately not, at least with the available evidence. While it is clear these cells have a BK in mitochondria (characteristic K+ currents detected in mitoplasts) and it is also well substantiated that the metabolic effects in intact cells are explained by an intracellular BK (paxilline effects absent in the BK KO), it does not follow that both observations are linked. Given that ectopic BK-DEC appeared at the surface, a confounding factor is the likely expression of BK in other intracellular locations such as ER, Golgi, endosomes, etc. To their credit, authors acknowledge this limitation several times throughout the text ("...presumably mitoBK...") but not in other important places, particularly in the title and abstract.

2. MitoBK subcellular location. Pearson correlations of 0.6 and about zero were obtained between the locations of mitoGREEN on one side, and mRFP or RFP-GPI on the other (Figs. 1G and S1E). These are nice positive and negative controls. For BK-DECRFP however, the Pearson correlation was about 0.2. What is the Z resolution of apotome imaging? Assuming an optimum optical section of 600 nm, as obtained by a 1.4 NA objective with a confocal, that mitochondria are typically 100 nm in diameter and that BK-DECRFP appears to stain more structures than mitoGREEN, the positive correlation of 0.2 may not reflect colocalization. For instance, it could be that BK-DECRFP is not just in mitochondria but in a close underlying organelle e.g. the ER. Along the same line, why did BK-RFP also give a positive Pearson? Isn´t that unexpected? Considering that BK-DEC was found by patch clamping at the plasma membrane, the subcellular targeting of the channel is suspect. Could it be that the endogenous BK-DEC does actually reside exclusively in mitochondria (a true mitoBK), but overflows to other membranes upon overexpression? Regarding immunodetection of BK in the mitochondrial Percoll preparation (Fig. S5), the absence of NKA demonstrates the absence of plasma membrane contamination but does not inform about contamination by other intracellular membranes.

3. Calibration of fluorescent probes. The conclusion that BK blockers or BK expression affects resting Ca2+ levels should be better supported. Fluorescent sensors and dyes provide signals or ratios that need to be calibrated if comparisons between different cell types or experimental conditions are to be made. This is implicitly acknowledged here when monitoring ER Ca2+, with an elaborate protocol to deplete the organelle in order to achieve a reading at zero Ca2+.

4. Line 203. "...solely by the expression of BKCa-DECRFP in MCF-7 cells". Granted, the effect of BKCa-DECRFP on the basal FRET ratio appears stronger than that of BK-RFP, but it appears that the latter had some effect. Please provide the statistics of the latter against the control group (after calibration, see above).

Reviewer #1 (Public Review):

Bischoff et al present a carefully prepared study on a very interesting and relevant topic: the role of ion channels (here a Ca2+-activated K+ channel BK) in regulating mitochondrial metabolism in breast cancer cells. The potential impact of these and similar observations made in other tumor entities has only begun to be appreciated. That being said, the authors pursue in my view an innovative approach to understanding breast cancer cell metabolism.

Considering the following points would further strengthen the manuscript:

Methods:

1. The authors use an extracellular Ca2+ concentration (2 mM) in their Ringer's solutions that is almost twice as high as the physiologically free Ca2+ concentration (ln 473). Moreover, the free Ca2+ concentration of their pipette solution is not indicated (ln 487).

2. Ca2+I measurements: The authors use ATP to elicit intracellular Ca2+ signals. Is this then a physiological stimulus for Ca2+ signaling in breast cancer? What is the rationale for using ATP? Moreover, it would be nice to see calibrated baseline values of Ca2+i.

3. Membrane potential measurements: It would be nice to see a calibration of the potential measurements; this would allow us to correlate the IV relationship with membrane potential. Without calibration, it is hard to compare unless the identical uptake of the dye is shown.

Does paxilline or IbTx also induce depolarization?

4. Mito-potential measurements: Why did the authors use such a long time course and preincubate cells with channel blockers overnight? Why did they not perform paired experiments and record the immediate effect of the BK channel blockers in the mito potential?

5. MTT assays are also based on mitochondrial function - since modulation of mito function is at the core of this manuscript, an alternative method should be used.

Results:

1. Fig. 5G: The number of BK "positive" mitoplasts is surprisingly low - how does this affect the interpretation? Did the authors attempt to record mitoBK current in the "whole-mitoplast" mode? How does the mitoBK current density compare with that of the plasma membrane? Is it possible to theoretically predict the number of mitoBK channels per mitochondrion to elicit the observed effects? Can these results be correlated with the immuno-localization of mitoBK channels?

2. There are also reports about other mitoK channels (e.g. Kv1.3, KCa3.1, KATP) playing an important role in mitochondrial function. Did the authors observe them, too? Can the authors speculate on the relative importance of the different channels? Is it known whether they are expressed organ-/tumor-specifically?

Reviewer #3 (Public Review):

The original research article, titled "mitoBKCa is functionally expressed in murine and human breast cancer cells and promotes metabolic reprogramming" by Bischof et al, has demonstrated the underlying molecular mechanisms of alterations in the function of Ca2+ activated K+ channel of large conductance (BKCa) in the development and progression of breast cancer. The authors also proposed that targeting mitoBKCa in combination with established anti-cancer approaches, could be considered as a novel treatment strategy in breast cancer treatment.

The paper is clearly written, and the reported results are interesting.

Strengths:

Rigorous biophysical experimental proof in support of the hypothesis.

Weaknesses:

A combinatorial synergistic study is missing.

Reviewer #2 (Public Review):

Singh and colleagues employ a methodic approach to reveal the function of the transcription factors Rela and Stat3 in the regulation of the inflammatory response in the intestine.

Strengths of the manuscript include the focus on the function of these transcription factors in hepatocytes and the discovery of their role in the systemic response to experimental colitis. While the systemic response to induce colitis is appreciated, the cellular and molecular mechanisms that drive such systemic response, especially those involving other organs beyond the intestine are an active area of research. As such, this study contributes to this conceptual advance. Additional strengths are the complementary biochemical and metabolomics approaches to describe the activation of these transcription factors in the liver and their requirement - specifically in hepatocytes - for the production of bile acids in response to colitis.

Some weaknesses are noted in the presentation of the data, including a comprehensive representation of findings in all conditions and genotypes tested.

Reviewer #1 (Public Review):

Summary:

In this study, the authors showed that activation of RelA and Stat3 in hepatocytes of DSS-treated mice induced CYPs and thereby produced primary bile acids, particularly CDCA, which exacerbated intestinal inflammation.

Strengths:

This study reveals the RelA/Stat3-dependent gene program in the liver influences intestinal homeostasis.

Weaknesses:

Additional evidence will strengthen the conclusion.

1. In Fig. 1C, photos show that phosphorylation of RelA and Stat3 was induced in only a few hepatocytes. The authors conclude that activation of both RelA and Stat3 induces inflammatory pathways. Therefore, the authors should show that phosphorylation of RelA and Stat3 is induced in the same hepatocytes during DSS treatment.

2. In Fig. 5, the authors treated mice with CDCA intraperitoneally. In this experiment, the concentration of CDCA in the colon of CDCA-treated mice should be shown.

Reviewer #3 (Public Review):

Summary:

The authors try to elucidate the molecular mechanisms underlying the intra-organ crosstalks that perpetuate intestinal permeability and inflammation.

Strengths:

This study identifies a hepatocyte-specific rela/stat3 network as a potential therapeutic target for intestinal diseases via the gut-liver axis using both murine models and human samples.

Weaknesses:

1. The mechanism by which DSS administration induces the activation of the Rela and Stat3 pathways and subsequent modification of the bile acid pathway remains clear. As the authors state, intestinal bacteria are one candidate, and this needs to be clarified. I recommend the authors investigate whether gut sterilization by administration of antibiotics or germ-free condition affects 1. the activation of the Rela and Stat3 pathway in the liver by DSS-treated WT mice and 2. the reduction of colitis in DSS-treated relaΔhepstat3Δhep mice.

2. It has not been shown whether DSS administration causes an increase in primary bile acids, represented by CDCA, in the colon of WT mice following activation of the Rela and Stat3 pathways, as demonstrated in Figure 6.

3. The implications of these results for IBD treatment, especially in what ways they may lead to therapeutic intervention, need to be discussed.

Reviewer #2 (Public Review):

Summary:

The authors of this manuscript address an important question regarding how macrophages respond to external stimuli to create different functional phenotypes, also known as macrophage polarization. Although this has been studied extensively, the authors argue that the transcription factors that mediate the change in state in response to a specific trigger remain unknown. They create a "master" human gene regulatory network and then analyze existing gene expression data consisting of PBMC-derived macrophage response to 28 stimuli, which they sort into thirteen different states defined by perturbed gene expression networks. They then identify the top transcription factors involved in each response that have the strongest predicted association with the perturbation patterns they identify. Finally, using S. aureus infection as one example of a stimulus that macrophages respond to, they infect THP-1 cells while perturbing regulatory factors that they have identified and show that these factors have a functional effect on the macrophage response.

Strengths:

- The computational work done to create a "master" hGRN, response networks for each of the 28 stimuli studied, and the clustering of stimuli into 13 macrophage states is useful. The data generated will be a helpful resource for researchers who want to determine the regulatory factors involved in response to a particular stimulus and could serve as a hypothesis generator for future studies.

- The streamlined system used here - macrophages in culture responding to a single stimulus - is useful for removing confounding factors and studying the elements involved in response to each stimulus.

- The use of a functional study with S. aureus infection is helpful to provide proof of principle that the authors' computational analysis generates data that is testable and valid for in vitro analysis.

Weaknesses:

- Although a streamlined system is helpful for interrogating responses to a stimulus without the confounding effects of other factors, the reality is that macrophages respond to these stimuli within a niche and while interacting with other cell types. The functional analysis shown is just the first step in testing a hypothesis generated from this data and should be followed with analysis in primary human cells or in an in vivo model system if possible.

- It would be helpful for the authors to determine whether the effects they see in the THP-1 immortalized cell line are reproduced in another macrophage cell line, or ideally in PBMC-derived macrophages.

- The paper would benefit from an expanded explanation of the network mining approach used, as well as the cluster stability analysis and the Epitracer analysis. Although these approaches may be published elsewhere, readers with a non-computational background would benefit from additional descriptions.

- Although the authors identify 13 different polarization states, they return to the M0/M1/M2 paradigm for their validation and functional assays. It would be useful to comment on the broader applications of a 13-state model.

- The relative contributions of each "switching factor" to the phenotype remain unclear, especially as knocking out each individual factor changes different aspects of the model (Fig. S5).

Reviewer #1 (Public Review):

Summary:

Ravichandran et al investigate the regulatory panels that determine the polarization state of macrophages. They identify regulatory factors involved in M1 and M2 polarization states by using their network analysis pipeline. They demonstrate that a set of three regulatory factors (RFs) i.e., CEBPB, NFE2L2, and BCL3 can change macrophage polarization from the M1 state to the M2 state. They also show that siRNA-mediated knockdown of those 3-RF in THP1-derived M0 cells, in the presence of M1 stimulant increases the expression of M2 markers and showed decreased bactericidal effect. This study provides an elegant computational framework to explore the macrophage heterogeneity upon different external stimuli and adds an interesting approach to understanding the dynamics of macrophage phenotypes after pathogen challenge.

Strengths:

This study identified new regulatory factors involved in M1 to M2 macrophage polarization. The authors used their own network analysis pipeline to analyze the available datasets. The authors showed 13 different clusters of macrophages that encounter different external stimuli, which is interesting and could be translationally relevant as in physiological conditions after pathogen challenge, the body shows dynamic changes in different cytokines/chemokines that could lead to different polarization states of macrophages. The authors validated their primary computational findings with in vitro assays by knocking down the three regulatory factors-NCB.

Weaknesses:

One weakness of the paper is the insufficient analysis performed on all the clusters. They used macrophages treated with 28 distinct stimuli, which included a very interesting combination of pro- and anti-inflammatory cytokines/factors that can be very important in the context of in vivo pathogen challenge, but they did not characterize the full spectrum of clusters. Although they mentioned that their identified regulatory panels could determine the precise polarization state, they restricted their analysis to only the two well-established macrophage polarization states, M1 and M2. Analyzing the other states beyond M1 and M2 could substantially advance the field. They mentioned the regulatory factors involved in individual clusters but did not study the potential pathway involving the target genes of these regulatory factors, which can show the importance of different macrophage polarization states. Importantly, these findings were not validated in primary cells or using in vivo models.

Reviewer #2 (Public Review):

Summary:<br /> In this study, Huang et al. employed optogenetic stimulation alongside paired whole-cell recordings in genetically defined neuron populations of the medial entorhinal cortex to examine the spatial distribution of synaptic inputs and the functional-anatomical structure of the MEC. They specifically studied the spatial distribution of synaptic inputs from parvalbumin-expressing interneurons to pairs of excitatory stellate cells. Additionally, they explored the spatial distribution of synaptic inputs to pairs of PV INs. Their results indicate that both pairs of SCs and PV INs generally receive common input when their relative somata are within 200-300 ums of each other. The research is intriguing, with controlled and systematic methodologies. There are interesting takeaways based on the implications of this work to grid cell network organization in MEC.

Major concerns<br /> 1) Results indicate that in brain slices, nearby cells typically share a higher degree of common input. However, some proximate cells lack this shared input. The authors interpret these findings as: "Many cells in close proximity don't seem to share common input, as illustrated in Figures 3, 5, and 7. This implies that these cells might belong to separate networks or exist in distinct regions of the connectivity space within the same network.".

Every slice orientation could have potentially shared inputs from an orthogonal direction that are unavoidably eliminated. For instance, in a horizontal section, shared inputs to two SCs might be situated either dorsally or ventrally from the horizontal cut, and thus removed during slicing. Given the synaptic connection distributions observed within each intact orientation, and considering these distributions appear symmetrically in both horizontal and sagittal sections, the authors should be equipped to estimate the potential number of inputs absent due to sectioning in the orthogonal direction. How might this estimate influence the findings, especially those indicating that many close neurons don't have shared inputs?

2) The study examines correlations during various light-intensity phases of the ramp stimuli. One wonders if the spatial distribution of shared (or correlated) versus independent inputs differs when juxtaposing the initial light stimulation phase, which begins to trigger spiking, against subsequent phases. This differentiation might be particularly pertinent to the PV to SC measurements. Here, the initial phase of stimulation, as depicted in Figure 7, reveals a relatively sparse temporal frequency of IPSCs. This might not represent the physiological conditions under which high-firing INs function.

While the authors seem to have addressed parts of this concern in their focal stim experiments by examining correlations during both high and low light intensities, they could potentially extract this metric from data acquired in their ramp conditions. This would be especially valuable for PV to SC measurements, given the absence of corresponding focal stimulation experiments.

3) Re results from Figure 2: Please fully describe the model in the methods section. Generally, I like using a modeling approach to explore the impact of convergent synaptic input to PVs from SCs that could effectively validate the experimental approach and enhance the interpretability of the experimental stim/recording outcomes. However, as currently detailed in the manuscript, the model description is inadequate for assessing the robustness of the simulation outcomes. If the IN model is simply integrate-and-fire with minimal biophysical attributes, then the findings in Fig 2F results shown in Fig 2F might be trivial. Conversely, if the model offers a more biophysically accurate representation (e.g., with conductance-based synaptic inputs, synapses appropriately dispersed across the model IN dendritic tree, and standard PV IN voltage-gated membrane conductances), then the model's results could serve as a meaningful method to both validate and interpret the experiments.

Reviewer #3 (Public Review):

Summary:<br /> This paper presents convincing data from technically demanding dual whole-cell patch recordings of stellate cells in medial entorhinal cortex slice preparations during optogenetic stimulation of PV+ interneurons. The authors show that the patterns of postsynaptic activation are consistent with dual recorded cells close to each other receiving shared inhibitory input and sending excitatory connections back to the same PV neurons, supporting a circuitry in which clusters of stellate cells and PV+IN interact with each other with much weaker interactions between clusters. These data are important to our understanding of the dynamics of functional cell responses in the entorhinal cortex. The experiments and analysis are quite complex and would benefit from some revisions to enhance clarity.

Strengths:<br /> These are technically demanding experiments, but the authors show quite convincing differences in the correlated response of cell pairs that are close to each other in contrast to an absence of correlation in other cell pairs at a range of relative distances. This supports their main point of demonstrating anatomical clusters of cells receiving shared inhibitory input.

Weaknesses:<br /> The overall technique is complex and the presentation could be more clear about the techniques and analysis. In addition, due to this being a slice preparation they cannot directly relate the inhibitory interactions to the functional properties of grid cells which was possible in the 2-photon in vivo imaging experiment by Heys and Dombeck, 2014.

Reviewer #1 (Public Review):

Summary:<br /> The circuit mechanism underlying the formation of grid cell activity and the organization of grid cells in the medial entorhinal cortex (MEC) is still unclear. To understand the mechanism, the current study investigated synaptic interactions between stellate cells (SC) and PV+ interneurons (IN) in layer 2 of the MEC by combing optogenetic activations and paired patch-clamp recordings. The results convincingly demonstrated highly structured interactions between these neurons: specific and direct excitatory-inhibitory interactions existed at the scale of grid cell phase clusters, and indirect interactions occurred at the scale of grid modules.

Strengths:<br /> Overall, the manuscript is very well written, the approaches used are clever, and the data were thoroughly analyzed. The study conveyed important information for understanding the circuit mechanism that shapes grid cell activity. It is important not only for the field of MEC and grid cells, but also for broader fields of continuous attractor networks and neural circuits.

Weaknesses:<br /> (1) The study largely relies on the fact that ramp-like wide-field optogenetic stimulation and focal optogenetic activation both drove asynchronous action potentials in SCs, and therefore, if a pair of PV+ INs exhibited correlated activity, they should receive common inputs. However, it is unclear what criteria/thresholds were used to determine the level of activity asynchronization, and under these criteria, what percentage of cells actually showed synchronized or less asynchronized activity. A notable percentage of synchronized or less asynchronized SCs could complicate the results, i.e., PV+ INs with correlated activity could receive inputs from different SCs (different inputs), which had synchronized activity. More detailed information/statistics about the asynchronization of SC activity is necessary for interpreting the results.

(2) The hypothesis about the "direct excitatory-inhibitory" synaptic interactions is made based on the GABAzine experiments in Figure 4. In the Figure 8 diagram, the direct interaction is illustrated between PV+ INs and SCs. However, the evidence supporting this "direct interaction" between these two cell types is missing. Is it possible that pyramidal cells are also involved in this interaction? Some pieces of evidence or discussions are necessary to further support the "direction interaction".

Reviewer #1 (Public Review):

Summary:<br /> In this paper, the authors provide a characterisation of auditory responses (tones, noise, and amplitude-modulated sounds) and bimodal (somatosensory-auditory) responses and interactions in the higher-order lateral cortex (LC) of the inferior colliculus (IC) and compare these characteristics with the higher order dorsal cortex (DC) of the IC - in awake and anaesthetised mice. Dan Llano's group has previously identified gaba'ergic patches (modules) in the LC distinctly receiving inputs from somatosensory structures, surrounded by matrix regions receiving inputs from the auditory cortex. They here use 2P calcium imaging combined with an implanted prism to - for the first time - get functional optical access to these subregions (modules and matrix) in the lateral cortex of IC in vivo, in order to also characterise the functional difference in these subparts of LC. They find that both DC and LC of both awake and anaesthetised mice appear to be more responsive to more complex sounds (amplitude-modulated noise) compared to pure tones and that under anesthesia the matrix of LC is more modulated by specific frequency and temporal content compared to the gabaergic modules in LC. However, while both LC and DC appear to have low-frequency preferences, this preference for low frequencies is more pronounced in DC. Furthermore, in both awake and anesthetized mice, somatosensory inputs are capable of driving responses on their own in the modules of LC, but very little (possibly not at all) in the matrix. However, bimodal interactions may be different under awake and anesthesia in LC, which warrants deeper investigation by the authors: They find, under anesthesia, more bimodal enhancement in modules of LC compared to the matrix of LC and bimodal suppression dominating the matrix of LC. In contrast, under awake conditions bimodal enhancement is almost exclusively found in the matrix of LC, and bimodal suppression dominates both matrix and modules of LC.

The paper provides new information about how subregions with different inputs and neurochemical profiles in the higher-order auditory midbrain process auditory and multisensory information, and is useful for the auditory and multisensory circuits neuroscience community.

Strengths:<br /> The major strength of this study is undoubtedly the fact that the authors for the first time provide optical access to a subcortical region (the lateral cortex of the inferior colliculus (i.e. higher order auditory midbrain)) which we know (from previous work by the same group) have optically identifiable subdivisions with unique inputs and neurotransmitter release, and plays a central role in auditory and multisensory processing. A description of basic auditory and multisensory properties of this structure is therefore very useful for understanding auditory processing and multisensory interactions in subcortical circuits.

Weaknesses:<br /> I have divided my comments about weaknesses and improvements into major and minor comments. All of which I believe are addressable by the reviewers to provide a more clear picture of their characterisation of the higher-order auditory midbrain.

Major comment:<br /> 1. The differences between multisensory interactions in LC in anaesthetised and awake preparations appear to be qualitatively different, though the authors claim they are similar (see also minor comment related to figure 10H for further explanation of what I mean). However, the findings in awake and anaesthetised conditions are summarised differently, and plotting of similar findings in the awake figures and anaesthetised figures are different - and different statistics are used for the same comparisons. This makes it very difficult to assess how multisensory integration in LC is different under awake and anaesthetised conditions. I suggest that the authors plot (and test with similar statistics) the summary plots in Figure 8 (i.e. Figure 8H-K) for awake data in Figure 10, and also make similar plots to Figures 10G-H for anaesthetised data. This will help the readers understand the differences between bimodal stimulation effects on awake and anaesthetised preparations - which in its current form, looks very distinct. In general, it is unclear to me why the awake data related to Figures 9 and 10 is presented in a different way for similar comparisons. Please streamline the presentation of results for anaesthetised and awake results to aid the comparison of results in different states, and explicitly state and discuss differences under awake and anaesthetised conditions.

2. The claim about the degree of tonotopy in LC and DC should be aided by summary statistics to understand the degree to which tonotopy is actually present. For example, the authors could demonstrate that it is not possible/or is possible to predict above chance a cell's BF based on the group of other cells in the area. This will help understand to what degree the tonotopy is topographic vs salt and pepper. Also, it would be good to know if the gaba'ergic modules have a higher propensity of particular BFs or tonotopic structure compared to matrix regions in LC, and also if general tuning properties (e.g. tuning width) are different from the matrix cells and the ones in DC.

3. Throughout the paper more information needs to be given about the number of cells, sessions, and animals used in each panel, and what level was used as n in the statistical tests. For example, in Figure 4 I can't tell if the 4 mice shown for LC imaging are the only 4 mice imaged, and used in the Figure 4E summary or if these are just examples. In general, throughout the paper, it is currently not possible to assess how many cells, sessions, and animals the data shown comes from.

4. Throughout the paper, to better understand the summary maps and plots, it would be helpful to see example responses of the different components investigated. For example, given that module cells appear to have more auditory offset responses, it would be helpful to see what the bimodal, sound-only, and somatosensory responses look like in example cells in LC modules. This also goes for just general examples of what the responses to auditory and somatosensory inputs look like in DC vs LC. In general example plots of what the responses actually look like are needed to better understand what is being summarised.

Reviewer #2 (Public Review):

Summary:<br /> The study describes differences in responses to sounds and whisker deflections as well as combinations of these stimuli in different neurochemically defined subsections of the lateral and dorsal cortex of the inferior colliculus in anesthetised and awake mice.

Strengths:<br /> The main achievement of the work lies in obtaining the data in the first place as this required establishing and refining a challenging surgical procedure to insert a prism that enabled the authors to visualise the lateral surface of the inferior colliculus. Using this approach, the authors were then able to provide the first functional comparison of neural responses inside and outside of the GABA-rich modules of the lateral cortex. The strongest and most interesting aspects of the results, in my opinion, concern the interactions of auditory and somatosensory stimulation. For instance, the authors find that a) somatosensory-responses are strongest inside the modules and b) somatosensory-auditory suppression is stronger in the matrix than in the modules. This suggests that, while somatosensory inputs preferentially target the GABA-rich modules, they do not exclusively target GABAergic neurons within the modules (given that the authors record exclusively from excitatory neurons we wouldn't expect to see somatosensory responses if they targeted exclusively GABAergic neurons), and that the GABAergic neurons of the modules (consistent with previous work) preferentially impact neurons outside the modules, i.e. via long-range connections.

Weaknesses:<br /> While the findings are of interest to the subfield they have only rather limited implications beyond it. The writing is not as precise as it could be. Consequently, the manuscript is unclear in some places. For instance, the text is somewhat confusing as to whether there is a difference in the pattern (modules vs matrix) of somatosensory-auditory suppression between anesthetized and awake animals. Furthermore, there are aspects of the results which are potentially very interesting but have not been explored. For example, there is a remarkable degree of clustering of response properties evident in many of the maps included in the paper. Taking Figure 7 for instance, rather than a salt and pepper organization we can see auditory responsive neurons clumped together and non-responsive neurons clumped together and in the panels below we can see off-responsive neurons forming clusters (although it is not easy to make out the magenta dots against the black background). This degree of clustering seems much stronger than expected and deserves further attention.

Reviewer #3 (Public Review):

The lateral cortex of the inferior colliculus (LC) is a region of the auditory midbrain noted for receiving both auditory and somatosensory input. Anatomical studies have established that somatosensory input primarily impinges on "modular" regions of the LC, which are characterized by high densities of GABAergic neurons, while auditory input is more prominent in the "matrix" regions that surround the modules. However, how auditory and somatosensory stimuli shape activity, both individually and when combined, in the modular and matrix regions of the LC has remained unknown.

The major obstacle to progress has been the location of the LC on the lateral edge of the inferior colliculus where it cannot be accessed in vivo using conventional imaging approaches. The authors overcame this obstacle by developing methods to implant a microprism adjacent to the LC. By redirecting light from the lateral surface of the LC to the dorsal surface of the microprism, the microprism enabled two-photon imaging of the LC via a dorsal approach in anesthetized and awake mice. Then, by crossing GAD-67-GFP mice with Thy1-jRGECO1a mice, the authors showed that they could identify LC modules in vivo using GFP fluorescence while assessing neural responses to auditory, somatosensory, and multimodal stimuli using Ca2+ imaging. Critically, the authors also validated the accuracy of the microprism technique by directly comparing results obtained with a microprism to data collected using conventional imaging of the dorsal-most LC modules, which are directly visible on the dorsal IC surface, finding good correlations between the approaches.

Through this innovative combination of techniques, the authors found that matrix neurons were more sensitive to auditory stimuli than modular neurons, modular neurons were more sensitive to somatosensory stimuli than matrix neurons, and bimodal, auditory-somatosensory stimuli were more likely to suppress activity in matrix neurons and enhance activity in modular neurons. Interestingly, despite their higher sensitivity to somatosensory stimuli than matrix neurons, modular neurons in the anesthetized prep were far more responsive to auditory stimuli than somatosensory stimuli (albeit with a tendency to have offset responses to sounds). This suggests that modular neurons should not be thought of as primarily representing somatosensory input, but rather as being more prone to having their auditory responses modified by somatosensory input. However, this trend was reversed in the awake prep, where modular neurons became more responsive to somatosensory stimuli than auditory stimuli. Thus, to this reviewer, the most intriguing result of the present study is the dramatic extent to which neural responses in the LC changed in the awake preparation. While this is not entirely unexpected, the magnitude and stimulus specificity of the changes caused by anesthesia highlight the extent to which higher-level sensory processing is affected by anesthesia and strongly suggest that future studies of LC function should be conducted in awake animals.

Together, the results of this study expand our understanding of the functional roles of matrix and module neurons by showing that responses in LC subregions are more complicated than might have been expected based on anatomy alone. The development of the microprism technique for imaging the LC will be a boon to the field, finally enabling much-needed studies of LC function in vivo. The experiments were well-designed and well-controlled, and the limitations of two-photon imaging for tracking neural activity are acknowledged. Appropriate statistical tests were used. There are three main issues the authors should address, but otherwise, this study represents an important advance in the field.

1) Please address whether the Thy1 mouse evenly expresses jRGECO1a in all LC neurons. It is known that these mice express jRGECO1a in subsets of neurons in the cerebral cortex, and similar biases in the LC could have biased the results here.

2) I suggest adding a paragraph or two to the discussion to address the large differences observed between the anesthetized and awake preparations. For example, somatosensory responses in the modules increased dramatically from 14.4% in the anesthetized prep to 63.6% in the awake prep. At the same time, auditory responses decreased from 52.1% to 22%. (Numbers for anesthetized prep include auditory responses and somatosensory + auditory responses.). In addition, the tonotopy of the DC shifted in the awake condition. These are intriguing changes that are not entirely expected from the switch to an awake prep and therefore warrant discussion.

3) For somatosensory stimuli, the authors used whisker deflection, but based on the anatomy, this is presumably not the only somatosensory stimulus that affects LC. The authors could help readers place the present results in a broader context by discussing how other somatosensory stimuli might come into play. For example, might a larger percentage of modular neurons be activated by somatosensory stimuli if more diverse stimuli were used?

Reviewer #3 (Public Review):

Lee, Kyungtae and colleagues have discovered and mapped out alpha-arrestin interactomes in both human and Drosophila through the affinity purification/mass spectrometry and the SAINTexpress method. Their work revealed highly confident interactomes, consisting of 390 protein-protein interactions (PPIs) between six human alpha-arrestins and 307 preproteins, as well as 740 PPIs between twelve Drosophila alpha-arrestins and 467 prey proteins.

To define and characterize these identified alpha-arrestin interactomes, the team employed a variety of widely recognized bioinformatics tools. These analyses included protein domain enrichment analysis, PANTHER for protein class enrichment, DAVID for subcellular localization analysis, COMPLEAT for the identification of functional complexes, and DIOPT to identify evolutionary conserved interactomes. Through these assessments, they not only confirmed the roles and associated functions of known alpha-arrestin interactors, such as ubiquitin ligase and protease, but also unearthed unexpected biological functions in the newly discovered interactomes. These included involvement in RNA splicing and helicase, GTPase-activating proteins, and ATP synthase.

The authors carried out further study into the role of human TXNIP in transcription and epigenetic regulation, as well as the role of ARRDC5 in osteoclast differentiation. It is particularly commendable that the authors conducted comprehensive testing of TXNIP's role in HDAC2 in gene expression and provided a compelling model while revising the manuscript. Additionally, the quantification of the immunocytochemistry data presented in Figure 6 convincingly supports the authors' hypothesis.

Overall, this study holds important value, as the newly identified alpha-arrestin interactomes are likely aiding functional studies of this protein group and advance alpha-arrestin research.

Reviewer #1 (Public Review):

The study provides a complete comparative interactome analysis of α-arrestin in both humans and drosophila. The authors have presented interactomes of six humans and twelve Drosophila α-arrestins using affinity purification/mass spectrometry (AP/MS). The constructed interactomes helped to find α-arrestins binding partners through common protein motifs. The authors have used bioinformatic tools and experimental data in human cells to identify the roles of TXNIP and ARRDC5: TXNIP-HADC2 interaction and ARRDC5-V-type ATPase interaction. The study reveals the PPI network for α-arrestins and examines the functions of α-arrestins in both humans and Drosophila. The authors have carried out the necessary changes that were suggested.

I would like to congratulate the authors and the corresponding authors of this manuscript for bringing together such an elaborate study on α-arrestin and conducting a comparative study in drosophila and humans.

Reviewer #2 (Public Review):

In this manuscript, the authors present a novel interactome focused on human and fly alpha-arrestin family proteins and demonstrate its application in understanding the functions of these proteins. Initially, the authors employed AP/MS analysis, a popular method for mapping protein-protein interactions (PPIs) by isolating protein complexes. Through rigorous statistical and manual quality control procedures, they established two robust interactomes, consisting of 6 baits and 307 prey proteins for humans, and 12 baits and 467 prey proteins for flies. To gain insights into the gene function, the authors investigated the interactors of alpha-arrestin proteins through various functional analyses, such as gene set enrichment. Furthermore, by comparing the interactors between humans and flies, the authors described both conserved and species-specific functions of the alpha-arrestin proteins. To validate their findings, the authors performed several experimental validations for TXNIP and ARRDC5 using ATAC-seq, siRNA knockdown, and tissue staining assays. The experimental results strongly support the predicted functions of the alpha-arrestin proteins and underscore their importance.

Joint Public Review:

This study sought to characterize the influence of acute stress on prosocial behavior, combining an effort-based task with neuroimaging, neuroendocrinological measures, and computational cognitive modeling. Two major results are reported: 1) Compared to controls, participants who experienced acute stress were less willing to exert effort for others, with more prominent effects for those who were more selfish; 2) More stressed participants exhibited an increase in activation in the dorsal anterior cingulate cortex and anterior insula, which are implicated in self-benefiting behavior. The approach is sophisticated and the findings are informative. Concerns regarding potential confounds and data reporting were addressed in a revised submission.

Reviewer #1 (Public Review):

This paper studies the effects of tACS on detection of silence gaps in an FM modulated noise stimulus. Both FM modulation of the sound and the tACS are at 2Hz, and the phase of the two is varied to determine possible interactions between the auditory and electric stimulation. Additionally, two different electrode montages are used to determine if variation in electric field distribution across the brain may be related to the effects of tACS on behavioral performance in individual subjects.

Major strengths and weaknesses of the methods and results.

The study appears to be well powered to detect modulation of behavioral performance with N=42 subjects. There is a clear and reproducible modulation of behavioral effects with the phase of the FM sound modulation. The study was also well designed and executed in terms of fMRI, current flow modeling, montage optimization targeting, and behavioral analysis. A particular merit of this study is to have repeated the sessions for most subjects in order to test repeat-reliability, which is so often missing in human experiments. The results and methods are generally well described and well conceived. The portion of the analysis related to behavior alone is excellent. The analysis of the tACS results are also generally well described, candidly highlighting how variable results are across subjects and sessions. The figures are all of high quality and clear. One weakness of the experimental design is that no effort was made to control for sensation effects. tACS at 2Hz causes prominent skin sensations which could have interacted with auditory perception and thus, detection performance.

The central claim is that tACS modulates behavioral detection performance across the 0.5s  cycle of stimulation. Statistical analysis with randomize relative phase (between audio and tACS) show that detection performance is modulated by tACS. Neither the relative phase or the strength of this effect reproduces across subjects or sessions, which makes the interpretation of these results difficult. These result could be of interest to investigators in the field of tACS.

The claim that the variation in the strength of the effect can be explained by variation of electric fields is not compelling.

The following are more detailed comments to specific sections of the paper, including details on the concerns with the statistical analysis of the tACS effects.<br /> The introduction is well balanced, discussing the promise and limitations of previous results with tACS. The objectives are well defined.

The analysis surrounding behavioral performance and its dependence on phase of the FM modulation (Figure 3) is masterfully executed and explained. It appears that it reproduces previous studies and points to a very robust behavioral task that may be of use in other studies.

The definition of tACS(+) vs tACS(-) phase is adjusted to each subject/session, which seems unconventional.  For argument sake, let's assume the curves in Fig. 3E are random fluctuations. Then aligning them to best-fitting cosine will trivially generate a FM-amplitude fluctuation with cosine shape as shown in Fig. 4a. Selecting the positive and negative phase of that will trivially be larger and smaller than sham, respectively, as shown in Fig 4b.

"Data from the optimal tACS lag and its opposite lag (corresponding trough) were excluded to avoid any artificial bias in estimating tACS effects induced by the alignment procedure (33)." The delay was found by fitting a cosine, so removing just the peaks of that cosine does little to avoid this problem.

To demonstrate that this is not a trivial result of the definition, the analysis compares this to the same analysis but with a randomize alignment to the two stimuli (audio and tACS) in Figure 4d. Assuming this shuffle was done correctly, this shows that the modulation observed in 4b is not just a result of the analysis procedure.

The authors are to be commended for analyzing the robustness of their observation across subjects and across sessions in Fig. 5. The lack of consistency in the optimal time delay between the two stimuli is hard to reconcile with the common theory that tACS entrains brain function.

"To better understand what factors might be influencing inter-session variability in tACS effects, we estimated multiple linear models ..." "Inter-individual variability in the simulated E-field predicts tACS effects" Authors here are attempting to predict a property of the subjects that was just shown to not be a reliable property of the subject. Authors are picking 9 possible features for this, testing 33 possible models with N=34 data points. With these circumstances it is not hard to find something that correlates by chance. And some of the models tested had interaction terms, possibly further increasing the number of comparisons. In the absence of multiple comparison correction, what is happening here is that multiple models are fit to the data, and a statistical test is performed for the best model on the same (training) data. The corresponding claim that variations are explained by variations in electric field is not persuasive.

"Can we reduce inter-individual variability in tACS effects ..." This section seems even more speculative and with mixed results.

Given the concerns with the statistical analysis above, there are concerns about the following statements in the summary of the Discussion:

"4) individual variability in tACS effect size was partially explained by two interactions: between the normal component of the E-field and the field focality, and between the normal component of the E-field and the distance between the peak of the electric field and the functional target ROIs."

The complexity of this statement alone may be a good indication that this could be the result of false discovery due to multiple comparisons.

For the same reason as stated above, the following statements in the Abstract do not appear to have adequate support in the data:

"Inter-individual variability of tACS effects was best explained by the strength of the inward electric field, depending on the field focality and proximity to the target brain region. Although additional evidence is necessary, our results<br /> 42 also provided suggestive insights that spatially optimizing the electrode montage could be a promising tool to reduce inter-individual variability of tACS effects."

Reviewer #2 (Public Review):

I thank the authors for considering my comments and think the manuscript has been significantly improved with revision. However while I considered that the analysis employed for predicting tACS effects with linear models was convincing, I am still concerned by a multiple comparison issue for this analysis. An alternative option would be to report the results of a Partial Least Squares (PLS) analysis, with the stimulation properties as predictor variables and tACS effects as response variables. The authors could use PLS instead of multiple linear regression models to take into account the multicollinearity in the predictor variables, and also this can be done with only one PLS model. They could then extract the fitted responses values and estimate if the model can significantly fit the tACS effects.

Then, to determine which variables contribute more to the prediction, they can calculate the variable importance in projection (VIP) scores for the PLS regression model.<br /> An alternative option for the authors would be to temper their conclusions regarding how well field modeling/montage explains the variance observed across subjects.

Joint Public Review:

This manuscript tackles an important question, namely how K+ affects substrate transport in the SLC6 family. K+ effects have previously been reported for DAT and SERT, but the prototypical SLC6-fold transporter LeuT was not known to be sensitive to the K+ concentration. In this manuscript, the authors demonstrate convincingly that K+ inhibits Na+ binding, and Na+-dependent amino acid binding at high concentrations, and that K+ inside of vesicles containing LeuT increases the transport rate. However, outside K+ apparently had very little effect. Uptake data are supplemented with binding data, using the scintillation proximity assay, and transition metal FRET, allowing the observation of the distribution of distinct conformational states of the transporter.

Overall, the data are of high quality. I was initially concerned about the use of solutions of very high ionic strength (the Km for K+ is in the 200 mM range), however, the authors performed good controls with lower ionic strength solutions, suggesting that the K+ effect are specific and not caused by artifacts from the high salt concentrations.

Reviewer #1 (Public Review):

Summary:<br /> In this study, Nandy and colleagues examine neural and behavioral correlates of perceptual variability in monkeys performing a visual change detection task. They used a laminar probe to record from area V4 while two macaque monkeys detected a small change in stimulus orientation that occurred at a random time in one of two locations, focusing their analysis on stimulus conditions where the animal was equally likely to detect (hit) or not-detect (miss) a briefly presented orientation change (target). They discovered two behavioral measures that are significantly different between hit and miss trials - pupil size tends to be slightly larger on hits vs. misses, and monkeys are more likely to miss the target on trials in which they made a microsaccade shortly before target onset. They also examined multiple measures of neural activity across the cortical layers and found some measures that are significantly different between hits and misses.

Strengths:<br /> Overall the study is well executed and the analyses are appropriate (though multiple issues do need to be addressed).

Weaknesses:<br /> My main concern with this study is that with the exception of the pre-target microsaccades, the physiological and behavioral correlates of perceptual variability (differences between hits and misses) appear to be very weak and disconnected. Some of these measures rely on complex analyses that are not hypothesis-driven and where statistical significance is difficult to assess. The more intuitive analysis of the predictive power of trial outcomes based on the behavioral and neural measures is only discussed at the end of the paper. This analysis shows that some of the significant measures have no predictive power, while others cannot be examined using the predictive power analysis because these measures cannot be estimated in single trials. Given these weak and disconnected effects, my overall sense is that the current results do not significantly advance our understanding of the neural basis of perceptual variability.

Reviewer #2 (Public Review):

In this manuscript, the authors conducted a study in which they measured eye movements, pupil diameter, and neural activity in V4 in monkeys engaged in a visual attention task. The task required the monkeys to report changes in the orientation of Gabors' visual stimuli. The authors manipulated the difficulty of the trials by varying the degree of orientation change and focused their analysis on trials of intermediate difficulty where the monkeys' hit rate was approximately 50%. Their key findings include the following: 1) Hit trials were preceded by larger pupil diameter, reflecting higher arousal, and by more stable eye positions; 2) V4 neurons exhibit larger visual responses in hit trials; 3) Superficial and deep layers exhibited greater coherence in hit trials during both the pre-target stimulus period and the non-target stimulus presentation period. These findings have useful implications for the field, and the experiments and analyses presented in this manuscript validly support the authors' claims.

Strengths:<br /> The experiments were well-designed and executed with meticulous control. The analyses of both behavioural and electrophysiological data align with the standards in the field.

Weaknesses:<br /> Many of the findings appear to be incremental compared to previous literature, including the authors' own work. While incremental findings are not necessarily a problem, the manuscript lacks clear statements about the extent to which the dataset, analysis, and findings overlap with the authors' prior research. For example, one of the main findings, which suggests that V4 neurons exhibit larger visual responses in hit trials (as shown in Fig. 3), appears to have been previously reported in their 2017 paper. Additionally, it seems that the entire Fig1-S1 may have been reused from the 2017 paper. These overlaps should have been explicitly acknowledged and correctly referenced.

Previous studies have demonstrated that attention leads to decorrelation in V4 population activity. The authors should have discussed how and why the high coherence across layers observed in the current study can coexist with this decorrelation.

Furthermore, the manuscript does not explore potentially interesting aspects of the dataset. For instance, the authors could have investigated instances where monkeys made 'false' reports, such as executing saccades towards visual stimuli when no orientation change occurred. It would be valuable to provide the fraction of the monkeys' responses in a session, including false reports and correct rejections in catch trials, to allow for a broader analysis that considers the perceptual component of neural activity over pure sensory responses.

Reviewer #1 (Public Review):

Zhu, et al present a genome-wide histone modification analysis comparing patients with schizophrenia (on or off antipsychotics) to non-psychiatric controls. The authors performed analyses across the dorsolateral prefrontal cortex and tested for enrichment of nearby genes and pathways. The authors performed an analysis measuring the effect of age on the epigenomic landscape as well. While this paper provides a unique resource around SCZ and its epigenetic correlates, and some potentially intriguing findings in the antipsychotic response dataset there were some potential missed opportunities - related to the integration of outside datasets and genotypes that could have strengthened the results and novelty of the paper.

Major Comments

1. Is there genotype data available for this cohort of donors or can it be generated? This would open several novel avenues of investigation for the authors. First the authors can test for enrichment of heritability for SCZ or even highly comorbid disorders such as bipolar. Second, it would allow the authors to directly measure the genetic regulation of histone markers by calculating QTLs (in this case histone hQTLs). The authors assert that although interesting, ATAC-seq approach does not provide the same chromatin state information as histone mods mapped by ChiP. Why do the authors not test this? There are several ATAC-seq datasets available for SCZ [https://pubmed.ncbi.nlm.nih.gov/30087329/]and an additional genomic overlap could help tease apart genetic regulation of the changes observed.

2. Can the authors theorize why their analysis found significant effects for H3K27Ac for antipsychotic use when a recent epigenomic study of SCZ using a larger cohort of samples and including the same histone modifications did not [https://pubmed.ncbi.nlm.nih.gov/30038276/]? Given the lower n and lower number of cells in this group, it would be helpful if the authors could speculate on why they see this. Do the authors know if there is any overlap with the Girdhar study donors or if there are other phenotypic differences that could account for this?

3. The reviewer is concerned about the low concordance between bulk nuclei RNA-seq and single-cell RNA-seq for SCZ (236 of 802 DEGs in NeuN+ and 63 of 1043 NEuN-). While it is not surprising for different cohorts to have different sets of DEGs these seem to be vastly different. Was there a particular cell type(s) that enriched for the authors' DEGs in the single-cell dataset? Do the authors know if any donors overlapped between these cohorts?

4. Functional enrichment analyses: details are not provided by the authors and should be added. The authors need to consider a) providing a gene universe, ie only considering the sets of genes with nearby H3K4me3/ H3K27ac levels, to such pathway tools, and b) should take into account the fact that some genes have many more peaks with data. There are known biases in seemingly just using the best p-value per gene in other epigenetic analysis (ie. DNA methylation data) and software is available to run correct analyses: https://pubmed.ncbi.nlm.nih.gov/23732277.

Reviewer #2 (Public Review):

The manuscript by Zhu has generated ChIP-seq and RNA-seq data from sizeable cohorts of SCZ patient samples and controls. The samples include 15 AF-SCZ samples and 15 controls, as well as 14 AT-SCZ samples and 14 controls. The genomics data was generated using techniques optimized for low-input samples: MOWChIP-seq and SMART-seq2 for histone profiles and transcriptome, respectively. The study has generated a significant data resource for the investigation of epigenomic alterations in SCZ. I am not convinced that the hierarchical pairwise design - first comparing AF-SCZ and AT-SCZ with their corresponding controls and secondarily contrasting the two comparisons is fully justified. The authors should repeat the statistical analysis by modeling all three groups simultaneously with an interaction effect for treatment or directly compare AF-SCZ to AT-SCZ groups and evaluate if the main conclusions remain supported.

Major comments

1. The manuscript did not discuss (mention) the quality control of RNA-seq data shown in Fig. 1B. The color scheme choice for the heatmap visualization did not provide a quantitative presentation of the specificity of the RNA-seq data. I would recommend using bar plots to present the results more quantitatively.

2. How does the specificity of this RNA-seq dataset compare to previous studies using a similar NeuN sorting strategy?

3. I appreciate the effort to assess the ChIP-seq data quality using phantompeakqualtools. However, prior knowledge/experience with this tool is required to fully understand the QC results. The authors should additionally provide browser shots at different scales for key neuronal/glial genes, so readers can have a more direct assessment of data quality, such as the enrichment of H3K4me3 at promoters (but not elsewhere), and H3K27ac at promoters and enhancers. Existing browser views, such as Fig. 2B are too zoomed out for assessing the data quality.

4. The pairwise regression model should be explicitly reported in methods.

5. The statistical strategy to compare AF-SCZ and AT-SCZ to their corresponding control groups was unjustified. Why not model all three groups simultaneously with an interaction effect for treatment or directly compare AF-SCZ to AT-SCZ groups? If the manuscript argues that the antipsychotic effect is the main novelty, why not directly compare AF-SCZ and AT-SCZ?

6. The method of pairwise comparison to corresponding control groups, then further comparing the pairwise results opens the study to a number of statistical vulnerabilities. For example, on page 12, the studies identified 166 DEGs between AF and control, and 1273 DEGs between AT and control. Instead of implicating a greater amount of difference between AT and control, such a result can often be driven by differences in between-group variance, rather than between-group means, that is, are the SCZ-AF and SCZ-treated effect size magnitudes and directionalities similar (but the treated group has lower variance) or are the two groups truly different in terms of means? The result in Fig. 5A suggests effect sizes for the two comparisons (AF-Ctrl and AT-Ctrl) are similar but have lower variability in the treated group.

7. The pairwise comparison further raised the possibility the results were driven by the difference in the two control cohorts rather than the two SCZ cohorts.

Reviewer #1 (Public Review):

The authors used mathematical models to explore the mechanism(s) underlying the process of polar tube extrusion and the transport of the sporoplasm and nucleus through this structure. They combined this with experimental observations of the structure of the tube during extrusion using serial block face EM providing 3 dimensional data on this process. They also examined the effect of hyperosmolar media on this process to evaluate which model fit the predicted observed behavior of the polar tube in these various media solutions. Overall, this work resulted in the authors arriving at a model of this process that fit the data (model 5, E-OE-PTPV-ExP). This model is consistent with other data in the literature and provides support for the concept that the polar tube functions by eversion (unfolding like a finger of a glove) and that the expanding polar vacuole is part of this process. Finally, the authors provide important new insights into the bucking of the spore wall (and possible cavitation) as providing force for the nucleus to be transported via the polar tube. This is an important observation that has not been in previous models of this process.

Reviewer #2 (Public Review):

The paper follows a recent study by the same team (Jaroenlak et al Plos Pathogens 2020), which documented the dramatic ejection dynamics of the polar tube (PT) in microsporidia using live-imaging and scanning electron microscopy. Although several key observations were reported in this paper (the 3D architecture of the PT within the spore, the speed and extent of the ejection process, the translocation dynamics of the nucleus during germination), the precise geometry of the PT during ejection remain inaccessible to imaging, making it difficult to physically understand the phenomenon.

This paper aims to fill this gap with an indirect "data-driven" approach. By modeling the hydrodynamic dissipation for different unfolding mechanisms identified in the literature and by comparing the predictions with experiments of ejection in media of various viscosities, authors shows that data are compatible with an eversion (caterpillar-like) mechanism but not compatible with a "jack-in-the-box" scenario. In addition, the authors observe that most germinated spores exhibit an inward bulge, which they attribute to buckling due to negative pressure difference. They suggest that this buckling may be a mean of pushing the nucleus out of the PT during the final stage of ejection.

Major strengths:

The most compelling aspect of the study is the experimental analysis of the ejection dynamics (velocity, ejection length) in medium of various viscosities over 3 orders of magnitudes, which, combined with a modeling of the viscous drag of the PT tube, provides very convincing evidence that the unfolding geometry is not a global displacement of the tube but rather an apical extension, where the motion is localized at the end of the tube.

The systematic classification of the different unfolding scenarios, consistent with the previous literature, and their confrontation with data in terms of energy, pressure and velocity also constitute an original approach in microbiology, where in-situ and real time geometry is often difficult to access.

Major weaknesses:

The revised version has clarified some details of the model, adding a paragraph and a figure in the Sup Mat. However, in my opinion, it remains difficult to understand the precise topology and ejection mechanism from the various sketches presented in the article.

The article does not address the mechanical driver (force) of ejection, and the role of pressure is unclear. The revised version replaced the term "negative pressure" with "negative pressure difference", arguing that a positive or negative pressure difference could not be differentiated. However, it is not clear how a lower pressure in the spore than in the bath could eject the tube outside.

Reviewer #1 (Public Review):

In this study, the authors investigated the role of MAM and the Notch signalling pathway in the onset of the atrophic phenotype in both in vivo and in vitro models. The rationale used to obtain the data is one of the main strengths of the study. Already from the reading, the reasoning scheme used by the authors in setting up the study and evaluating the data obtained is clear. Using both cellular and mouse models in vivo consolidates the data obtained. The authors also methodologically described all the choices made in the supplementary section.

Reviewer #2 (Public Review):

In this study, the authors examined how maintenance of mitochondrial-associated endoplasmic reticulum membranes (MAM) are critical for the prevention of muscle atrophy under microgravity conditions. They observed, a reduction in MAM in myotubes placed in a microgravity condition; in addition, MFN2-deficient human iPS cells showed a decrease in the number of MAM, similar to in myotubes differentiated under microgravity conditions, in addition to the activation of the Notch signaling pathway. The authors, morover, obsreved that by treatment with the gamma-secretase inhibitor with DAPT preserved from the atrophic phenotype of differentiated myotubes in microgravity and improve the regenerative capacity of Mfn2-deficient muscle stem cells in dystrophic mice.

The entire study was well conducted, bringing an interesting analysis in vitro and in vivo of aging condition. In my opinion it is necessary to implement the analysis of both genes and proteins for better supporting the conclusions

The study can contribute to better understand one of the major problems of aging, such as muscle atrophy and inhibition of muscle regeneration, emphasizing the importance of NOTCH patway in these pathological situations. The work will be of interest to all scientist working on aging.

Joint Public Review:

The biogenesis of outer membrane proteins (OMPs) into the outer membranes of Gram-negative bacteria is not fully understood, particularly client recognition and insertion by the conserved beta-assembly machinery (BAM), which is itself integrated in the outer membranes. So far, the last strand of an OMP, referred to as the beta-signal, has been known as a primary recognition motif by BAM. Here, authors have identified additional sequence motifs that are located in the upstream of the last strand.

Here, authors carried out rigorous biochemical, biophysical, and genetic approaches to prove that the newly identified internal motifs are critical to the assembly of outer membrane proteins as well as to the interaction with the BAM complex. The identification of important regions on the substrates and Bam proteins during biogenesis is an important contribution that gives clues to the path substrates take en route to the membrane. Assessing the effect of the internal motifs in the assembly of model OMPs in the absence (in vitro) and presence (in vitro and in vivo) of BAM machinery aids a precise definition of the role of the motifs, solidifying the conclusions.

The initial reviews raised several concerns:

1. Strengthening the claim that the recognition of the internal signal by BAM is mediated by BamA and BamD via specific interactions.

2. Justification of the rationale of the peptide inhibition assays as a primary tool to identify significant recognition motifs.

3. More careful interpretation of the mutational effects on OMP assembly - that is, discerning the impairment of BAM-nascent polypeptide chain interaction from the impairment of intrinsic folding.

4. Providing further clarification of the discrepancy between in vitro assay and in vivo assay regarding the effect of the mutation Y286A on OMP assembly.

5. More elaboration on the rationale, interpretation, and representation of neutron refractory data.

6. An explanation is lacking why the strain with BamD R197A does not display VCN sensitivity in contrast to the strain with BamD Y62A.

Those concerns were well addressed in the revised manuscript in a rigorous manner.

Overall, this study comprehensively addresses an important question in the field. The notion that additional signals assist in biogenesis is a novel concept that has been tested and verified at least for a subset of model OMPs in this study. The generalization of the conclusion awaits a further proof of the concept.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript examined the impact of prenatal alcohol exposure on genome-wide DNA methylation in the brain and liver, comparing ethanol-exposed mice to unexposed controls. They also investigated whether a high-methyl diet (HMD) could prevent the DNA methylation alterations caused by alcohol. Using bisulfite sequencing (n=4 per group), they identified 78 alcohol-associated differentially methylated regions (DMRs) in the brain and 759 DMRs in the liver, of which 85% and 84% were mitigated by the HMD group, respectively. The authors further validated 7 DMRs in humans using previously published data from a Canadian cohort of children with FASD.

Overall, the findings from this study provide new insight into the impact of prenatal alcohol exposure, while also showing evidence for methyl-rich diets as an intervention to prevent the effects of alcohol on the epigenome. However, several methodological concerns limit the robustness of these results and should be addressed to further strengthen the conclusions of this study and its applicability to broader settings.

Strengths:<br /> - The use of whole genome bisulfite sequencing allowed for the interrogation of the entire DNA methylome and DMR analysis, rather than a subset of CpGs.<br /> - The combination of data from animal models and humans allowed the authors to make stronger inferences regarding their findings.<br /> - The authors investigated a potential mechanism (high methyl diet) to buffer against the effects of prenatal alcohol exposure, which increases the relevance and applicability of this research.

Weaknesses:<br /> - Mistakes and discontinuities in the reporting of results and methods made the manuscript difficult to follow. There was also some overuse of causal language and overinterpretation of differences.<br /> - The authors provide insufficient details to replicate their analyses, particularly for data quality control steps and statistical analyses.<br /> - The sample size was very small for the epigenetic analyses, which limits the robustness of the findings. This limitation is further emphasized by the cutoffs used to identify DMRs, which did not include multiple test corrections and used a delta cutoff that was not supported by the sequencing depth.<br /> - The authors do not account for potential confounders in their analyses, including birthweight, alcohol levels, and sex. This is a particular problem for the high-methyl diet analyses, in which the alcohol-exposed mice seemed to consume less alcohol than their non-diet counterparts.

Reviewer #2 (Public Review):

Summary:<br /> Bestry et al. investigated the effects of prenatal alcohol exposure (PAE) and high methyl donor diet (HMD) on offspring DNA methylation and behavioral outcomes using a mouse model that mimics common patterns of alcohol consumption in pregnancy in humans. The researchers employed whole-genome bisulfite sequencing (WGBS) for unbiased assessment of the epigenome in the newborn brain and liver, two organs affected by ethanol, to explore tissue-specific effects and to determine any "tissue-agnostic" effects that may have arisen prior to the germ-layer commitment during early gastrulation. The authors found that PAE induces measurable changes in offspring DNA methylation. DNA methylation changes induced by PAE coincide with non-coding regions, including enhancers and promoters, with the potential to regulate gene expression. Though the majority of the alcohol-sensitive differentially methylated regions (DMRs) were not conserved in humans, the ones that were conserved were associated with clinically relevant traits such as facial morphology, educational attainment, intelligence, autism, and schizophrenia. Finally, the study provides evidence that maternal dietary support with methyl donors alleviates the effects of PAE on DNA methylation, suggesting a potential prenatal care option.

Strengths:<br /> The strengths of the study include the use of a mouse model where confounding factors such as genetic background and diet can be well controlled. The study performed whole-genome bisulfite sequencing which allows a comprehensive analysis of the effects of PAE on DNA methylation. However, some weaknesses and limitations of the study are detected.

Weaknesses:<br /> 1. The low generalizability between mouse and human data alerts the validity of the mouse model designed in the study. On the same note, the authors failed to detect any significant effect on PAE-induced behavioral outcomes. I recognize that it is difficult to model all possible conditions of PAE in mice because the amount, frequency, and duration of alcohol consumption in humans vary significantly. Therefore, if the authors only focus on moderate PAE, it should be emphasized in the title and throughout the paper to avoid misinterpretation. In addition, is it possible to stratify the human data based on the level of PAE and compare it to the mouse data?<br /> 2. A major finding of the study is that PAE affects non-coding genomic regions in mice including enhancers and promoters. To improve the significance of the study, the authors need to back up this finding with transcriptome analysis and determine if these DMRs indeed affect gene expression.<br /> 3. The low generalizability between mouse and human data suggests that the regions affected by PAE may be species-specific. It is critical to analyze if PAE-induced DMRs in humans are also enriched in non-coding genomic regions. Considering the huge difference between mouse and human development, particularly in the brain, it is not surprising that different genomic loci are affected, but the affected loci may share similar features.<br /> 4. The specific brain regions and the lobes of the liver where the samples were taken should be clearly indicated.<br /> 5. I don't fully agree with the authors' interpretation that the two shared genomic regions affected in the brain and the liver "must have arisen before the germ layers separated". To claim so, the authors need to exclude the possibility that the two regions are just a coincidence due to the stochastic effect of PAE on DNA methylation.

Reviewer #1 (Public Review):

Summary:<br /> In their manuscript, Massa and colleagues provide a map of the epigenetic landscape in podocytes and analyze the role of the transcription factor MafB in podocyte gene expression. They initially map the histone profile in adult podocytes of the mouse by assaying three different histone methylation marks, namely H3K4me3, H3K4me1, and H3K27me3 for active, primed, and repressed states. They then perform Wt1- and MafB-ChIP-Seq analysis to identify respective direct targets of those transcription factors. Subsequently, they employ an inducible MafB knockout model and show that homozygous knockout mice show proteinuria and FSGS, suggesting an important role for MafB in podocyte homeostasis. RNA-Seq analysis in mice two days after tamoxifen application identified direct and indirect MafB target genes. Finally, the authors turn to a constitutive MafB knockout model, carry out anti-H3K4me3 and anti-Wt1 ChIP experiments, and examine selected promoters. One main conclusion from this work is that MafB opens chromatin and thus facilitates the binding of other transcription factors like Wt1 to podocyte-specific genes.

Strengths and weaknesses:<br /> The authors have performed an impressive number of experiments and generated very valuable data. They use state-of the-art technology and the data are presented well and are sound. This being said the manuscript contains significant novel data, but also experiments that are already available in some sort. The histone profile in adult mouse podocytes is novel and provides an interesting map of epigenetic marks in this particular cell type. It is maybe not too surprising that podocyte-differentiation genes have different chromatin accessibility than genes associated with general development. The Wt1-ChIP has been done before by several labs but is certainly an important control in this work. The MafB-ChIP is new. The inducible MafB knockout model including the identification of Tcf21 as a target gene has been published by others in 2020 (and is acknowledged by the authors). The experiments addressing the potential role of MafB in chromatin opening are new. I find that the data are certainly compatible with the model put forward by the authors, but they are not compelling.

Reviewer #2 (Public Review):

Summary:<br /> The authors investigate the role of MafB in regulating podocyte genes. Mafb is required for podocyte differentiation and maintenance. Mutations of this gene cause FSGS in mice and humans. They profiled MafB binding genome-wide in isolated glomeruli and defined overlap with Wt1. They provide evidence that Mafb is required for Wt1 binding and H3K4me3 methylation at the promoters of two essential podocyte genes, Nphs1 and Nphs2. Understanding how the action of different transcription factors is coordinated to control gene expression - the main goal of this paper - is an important line of investigation.

While the main conclusion of the paper is supported by their data, the scope is limited. Additional ChIP-seq experiments and data analysis are needed to solidify and extend their conclusions.

Strengths:<br /> 1) Performing ChIP-seq for histone modifications on isolated podocytes provides valuable cell-type-specific information. Similarly, profiling Mafb and Wt1 in isolated glomeruli provides podocyte-specific binding patterns because these transcription factors (TFs) are not expressed in other cell types in glomeruli. The significant overlap of their Wt1 binding genome-wide with that of prior published work is reassuring. RNA-seq on isolated podocytes provides the appropriate cell-type specific gene expression data to integrate with ChIP-seq data. Together, the RNA-seq and ChIP-seq data are valuable resources for other investigators examining gene regulation in mouse podocytes.

2) The phenotype analysis of their FSGS model is convincing and well done.

3) Testing how Wt1 binding is affected by loss of Mafb provides insight into how these key podocyte TFs may cooperate to regulate genes.

Weaknesses:<br /> 1) The conclusion that Mafb is required for Wt1 binding and H3K4me3 methylation is based solely on ChIP-PCR at two gene promoters (Nphs1, Nphs2). This result should be validated and extended by ChIP-seq. Mafb and Wt1 binding overlap at more than 200 sites. If their model is correct, it is likely that Wt1 binding would be affected at other genomic sites. This result would add strong support to their model of how Wt1 and Mafb cooperate to regulate genes in podocytes. Moreover, ChIP-seq would define whether the dependence of Wt1 on Mafb is also evident at distal regulatory regions (defined H3K4me1, which is typically found at predicted enhancers).

2) The FSGS model generated by the authors involved conditional deletion of Mafb in podocytes at 8 weeks of age. They found that this resulted in reduced expression of Nphs1 and Nphs2 within 48 hours post-deletion. However, they investigated Wt1 binding and H3K4me3 genomic binding in Mafb homozygous null embryos. While this result provides information about podocyte differentiation, it does not address the maintenance of expression of these essential podocyte genes in the adult kidney. Because post-natal deletion of Mafb led to FSGS and reduced expression of Nphs1/2, ChIP-seq should be performed on the adult conditional mutants in order to provide mechanistic information about the disease.

3) H3K4me1 binds enhancer regions. The authors performed ChIP-seq to profile H3K4me1 in isolated podocytes. However, there was no analysis reported of these results. It would be valuable to determine if Wt1 and Mafb co-localize at predicted enhancers in podocytes and if Wt1 binding is lost at these regions in Mafb mutant glomeruli.

Reviewer #1 (Public Review):

Summary:<br /> The manuscript titled "Coevolution due to physical interactions is not a major driving force behind evolutionary rate covariation" by Little et al., explores the potential contribution of physical interaction between correlated evolutionary rates among gene pairs. The authors find that physical interaction is not the main driving of evolutionary rate covariation (ECR). This finding is similar to a previous report by Clark et al. (2012), Genome Research, wherein the authors stated that "direct physical interaction is not required to produce ERC." The previous study used 18 Saccharomycotina yeast species, whereas the present study used 332 Saccharomycotina yeast species and 11 outgroup taxa. As a result, the present study is better positioned to evaluate the interplay between physical interaction and ECR more robustly.

Strengths & Weaknesses:<br /> Various analyses nicely support the authors' claims. Accordingly, I have only one significant comment and several minor comments that focus on wordsmithing - e.g., clarifying the interpretation of statistical results and requesting additional citations to support claims in the introduction.

Reviewer #2 (Public Review):

Summary:<br /> The authors address an important outstanding question: what forces are the primary drivers of evolutionary rate covariation? Exploration of this topic is important because it is currently difficult to interpret the functional/mechanistic implications of evolutionary covariation. These analyses also speak to the predictive power (and limits) of evolutionary rate covariation. This study reinforces the existing paradigm that covariation is driven by a varied/mixed set of interaction types that all fall under the umbrella explanation of 'co-functional interactions'.

Strengths:<br /> Very smart experimental design that leverages individual protein domains for increased resolution.

Weaknesses:<br /> Nuanced and sometimes inconclusive results that are difficult to capture in a short title/abstract statement.

Reviewer #3 (Public Review):

Summary:<br /> The paper makes a convincing argument that physical interactions of proteins do not cause substantial evolutionary co-variation.

Strengths:<br /> The presented analyses are reasonable and look correct and the conclusions make sense.

Weaknesses:<br /> The overall problem of the analysis is that nobody who has followed the literature on evolutionary rate variation over the last 20 years would think that physical interactions are a major cause of evolutionary rate variation. First, there have been probably hundreds of studies showing that gene expression level is the primary driver of evolutionary rate variation (see, for example, [1]). The present study doesn't mention this once. People can argue the causes or the strength of the effect, but entirely ignoring this body of literature is a serious lack of scholarship. Second, interacting proteins will likely be co-expressed, so the obvious null hypothesis would be to ask whether their observed rates are higher or lower than expected given their respective gene expression levels. Third, protein-protein interfaces exert a relatively weak selection pressure so I wouldn't expect them to play much role in the overall evolutionary rate of a protein.

On point 3, the authors seem confused though, as they claim a co-evolving interface would evolve *faster* than the rest of the protein (Figure 1, caption). Instead, the observation is they evolve slower (see, for example, [2]). This makes sense: A binding interface adds additional constraint that reduces the rate at which mutations accumulate. However, the effect is rather weak.

All in all, I'm fine with the analysis the authors perform, and I think the conclusions make sense, but the authors have to put some serious effort into reading the relevant literature and then reassess whether they are actually asking a meaningful question and, if so, whether they're doing the best analysis they could do or whether alternative hypotheses or analyses would make more sense.

[1] https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4523088/<br /> [2] https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4854464/

Reviewer #1 (Public Review):

Zhou et al. have slightly expanded and improved their web tool from the previous submission, fixing some small issues and adding in additional sets of data from HMDP mice. Essentially, the authors have created a tool that facilitates the integrated analysis of omics datasets (particularly transcriptomics, but could be easily adapted to include proteomics) across tissues.

The strength is that this is new; as far as I know, any other multi-tissue analysis software is relatively ad hoc and it is not easily supported by e.g. SRA/GEO, but rather you'd need to download the multiple datasets and DIY. The authors have now shown some statistically significant (albeit expected from literature) results created using their pipeline. Whether the method will be generally useful for the community depends on its further development and support, but of course whether a project is supported also depends on whether its first publication is accepted - somewhat of a Catch-22 for a reviewer. Right now, the results shown are a convincing proof-of-concept that would likely be of utility mostly to the hosting laboratory and their direct collaborators, but which, with continued development at a similar level of effort, could be more generally useful for the growing number of groups interested in cross-tissue analysis.

Reviewer #2 (Public Review):

Summary:<br /> Zhou et al. have revised their previous manuscript, which has greatly improved the quality of the work. Zhou et al. use publicly available GTEx data of 18 metabolic tissues from 310 individuals to explore gene expression correlation patterns within-tissue and across-tissues. Furthermore, they have added an analysis of data from a diverse panel of inbred mouse strains, which allows them to also incorporate data on physiological phenotypes relevant to metabolic signaling between tissues. They now focus on validating their approach to exploring signal in gene co-expression rather than emphasizing unvalidated discoveries. They provide a webtool (GD-CAT) to allow users to explore these data. Focusing more on known biology does result in the study making stronger conclusions from its data. The webtool is also improved, expanded with the mouse data, and of value to the scientific community. Their revision has also corrected key misconceptions from the initial submission and provides greater clarification of the methodologies used.

Strengths:<br /> GTEx as well as the hybrid diversity mouse panel are powerful resource for many areas of biomedicine, and this study represents a valid use of gene co-expression network methodology. They have greatly improved its description and contextualization within the gene co-expression studies. The authors previously did a good job of providing examples confirming known signaling biology and have further improved these. They have largely removed the sections on discovery of novel biology, which is potentially for the better given a lack of follow-up validation, which could be beyond the scope of this manuscript anyway. The webtool, GD-CAT, is easy to use and allows researchers with genes and tissues of interest to perform the same analyses in the GTEx and HMDP data.

Weaknesses:<br /> With the previous version, the primary weaknesses for me were key misconceptions and lack of detail in the methods, which have all been greatly improved. The manuscript could be considered more of a "Resource" than "Research", though there is value in showing how the known biology is reflected in the correlation data and could presumably be paired with validation to discover new biology. Finally, there are sentences here and there that could be rephrased to improve clarity, but overall it is greatly improved.

Reviewer #1 (Public Review):

Summary:<br /> The CPC plays multiple essential roles in mitosis such as kinetochore-microtubule attachment regulation, kinetochore assembly, spindle assembly checkpoint activation, anaphase spindle stabilization, cytokinesis, and nuclear envelope formation, as it dynamically changes its mitotic localization: it is enriched at inner centromeres from prophase to metaphase but it is relocalized at the spindle midzone in anaphase. The business end of the CPC is Aurora B and its allosteric activation module IN-box, which is located at the C-terminal part of INCENP. In most well-studied eukaryotic species, Aurora B activity is locally controlled by the localization module of the CPC, Survivin, Borealin, and the N-terminal portion of INCENP. Survivin and Borealin, which bind the N terminus of INCENP, recognize histone residues that are specifically phosphorylated in mitosis, while anaphase spindle midzone localization is supported by the direct microtubule-binding capacity of the SAH (single alpha helix) domain of INCENP and other microtubule-binding proteins that specifically interact with INCENP during anaphase, which are under the regulation of CDK activity. One of these examples includes the kinesin-like protein MKLP2 in vertebrates.

Trypanosoma is an evolutionarily interesting species to study mitosis since its kinetochore and centromere proteins do not show any similarity to other major branches of eukaryotes, while orthologs of Aurora B and INCENP have been identified. Combining molecular genetics, imaging, biochemistry, cross-linking IP-MS (IP-CLMS), and structural modeling, this manuscript reveals that two orphan kinesin-like proteins KIN-A and KIN-B act as localization modules of the CPC in Trypanosoma brucei. The IP-CLMS, AlphaFold2 structural predictions, and domain deletion analysis support the idea that (1) KIN-A and KIN-B form a heterodimer via their coiled-coil domain, (2) Two alpha helices of INCENP interact with the coiled-coil of the KIN-A-KIN-B heterodimer, (3) the conserved KIN-A C-terminal CD1 interacts with the heterodimeric KKT9-KKT11 complex, which is a submodule of the KKT7-KKT8 kinetochore complex unique to Trypanosoma, (4) KIN-A and KIN-B coiled-coil domains and the KKT7-KKT8 complex are required for CPC localization at the centromere, (5) CD1 and CD2 domains of KIN-A support its centromere localization. The authors further show that the ATPase activity of KIN-A is critical for spindle midzone enrichment of the CPC. The imaging data of the KIN-A rigor mutant suggest that dynamic KIN-A-microtubule interaction is required for metaphase alignment of the kinetochores and proliferation. Overall, the study reveals novel pathways of CPC localization regulation via KIN-A and KIN-B by multiple complementary approaches.

Strengths:<br /> The major conclusion is collectively supported by multiple approaches, combining site-specific genome engineering, epistasis analysis of cellular localization, AlphaFold2 structure prediction of protein complexes, IP-CLMS, and biochemical reconstitution (the complex of KKT8, KKT9, KKT11, and KKT12).

Weaknesses:<br /> - The predictions of direct interactions (e.g. INCENP with KIN-A/KIN-B, or KIN-A with KKT9-KKT11) have not yet been confirmed experimentally, e.g. by domain mutagenesis and interaction studies.

- The criteria used to judge a failure of localization are not clearly explained (e.g., Figure 5F, G).

- It remains to be shown that KIN-A has motor activity.

- The authors imply that KIN-A, but not KIN-B, interacts with microtubules based on microtubule pelleting assay (Fig. S6), but the substantial insoluble fractions of 6HIS-KINA and 6HIS-KIN-B make it difficult to conclusively interpret the data. It is possible that these two proteins are not stable unless they form a heterodimer.

- For broader context, some prior findings should be introduced, e.g. on the importance of the microtubule-binding capacity of the INCENP SAH domain and its regulation by mitotic phosphorylation (PMID 8408220, 26175154, 26166576, 28314740, 28314741, 21727193), since KIN-A and KIN-B may substitute for the function of the SAH domain.

Reviewer #2 (Public Review):

How the chromosomal passenger complex (CPC) and its subunit Aurora B kinase regulate kinetochore-microtubule attachment, and how the CPC relocates from kinetochores to the spindle midzone as a cell transitions from metaphase to anaphase are questions of great interest. In this study, Ballmer and Akiyoshi take a deep dive into the CPC in T. brucei, a kinetoplastid parasite with a kinetochore composition that varies greatly from other organisms.

Using a combination of approaches, most importantly in silico protein predictions using alphafold multimer and light microscopy in dividing T. brucei, the authors convincingly present and analyse the composition of the T. brucei CPC. This includes the identification of KIN-A and KIN-B, proteins of the kinesin family, as targeting subunits of the CPC. This is a clear advancement over earlier work, for example by Li and colleagues in 2008. The involvement of KIN-A and KIN-B is of particular interest, as it provides a clue for the (re)localization of the CPC during the cell cycle. The evolutionary perspective makes the paper potentially interesting for a wide audience of cell biologists, a point that the authors bring across properly in the title, the abstract, and their discussion.

The evolutionary twist of the paper would be strengthened 'experimentally' by predictions of the structure of the CPC beyond T. brucei. Depending on how far the authors can extend their in-silico analysis, it would be of interest to discuss a) available/predicted CPC structures in well-studied organisms and b) structural predictions in other euglenozoa. What are the general structural properties of the CPC (e.g. flexible linkers, overall dimensions, structural differences when subunits are missing etc.)? How common is the involvement of kinesin-like proteins? In line with this, it would be good to display the figure currently shown as S1D (or similar) as a main panel.

Reviewer #3 (Public Review):

Summary:<br /> The protein kinase, Aurora B, is a critical regulator of mitosis and cytokinesis in eukaryotes, exhibiting a dynamic localisation. As part of the Chromosomal Passenger Complex (CPC), along with the Aurora B activator, INCENP, and the CPC localisation module comprised of Borealin and Survivin, Aurora B travels from the kinetochores at metaphase to the spindle midzone at anaphase, which ensures its substrates are phosphorylated in a time- and space-dependent manner. In the kinetoplastid parasite, T. brucei, the Aurora B orthologue (AUK1), along with an INCENP orthologue known as CPC1, and a kinetoplastid-specific protein CPC2, also displays a dynamic localisation, moving from the kinetochores at metaphase to the spindle midzone at anaphase, to the anterior end of the newly synthesised flagellum attachment zone (FAZ) at cytokinesis. However, the trypanosome CPC lacks orthologues of Borealin and Survivin, and T. brucei kinetochores also have a unique composition, being comprised of dozens of kinetoplastid-specific proteins (KKTs). Of particular importance for this study are KKT7 and the KKT8 complex (comprising KKT8, KKT9, KKT11, and KKT12). Here, Ballmer and Akiyoshi seek to understand how the CPC assembles and is targeted to its different locations during the cell cycle in T. brucei.

Strengths & Weaknesses:<br /> Using immunoprecipitation and mass-spectrometry approaches, Ballmer and Akiyoshi show that AUK1, CPC1, and CPC2 associate with two orphan kinesins, KIN-A and KIN-B, and with the use of endogenously expressed fluorescent fusion proteins, demonstrate for the first time that KIN-A and KIN-B display a dynamic localisation pattern similar to other components of the CPC. Most of these data provide convincing evidence for KIN-A and KIN-B being bona fide CPC proteins, although the evidence that KIN-A and KIN-B translocate to the anterior end of the new FAZ at cytokinesis is weak - the KIN-A/B signals are very faint and difficult to see, and cell outlines/brightfield images are not presented to allow the reader to determine the cellular location of these faint signals (Fig S1B).

They then demonstrate, by using RNAi to deplete individual components, that the CPC proteins have hierarchical interdependencies for their localisation to the kinetochores at metaphase. These experiments appear to have been well performed, although only images of cell nuclei were shown (Fig 2A), meaning that the reader cannot properly assess whether CPC components have localised elsewhere in the cell, or if their abundance changes in response to depletion of another CPC protein.

Ballmer and Akiyoshi then go on to determine the kinetochore localisation domains of KIN-A and KIN-B. Using ectopically expressed GFP-tagged truncations, they show that coiled-coil domains within KIN-A and KIN-B, as well as a disordered C-terminal tail present only in KIN-A, but not the N-terminal motor domains of KIN-A or KIN-B, are required for kinetochore localisation. These data are strengthened by immunoprecipitating CPC complexes and crosslinking them prior to mass spectrometry analysis (IP-CLMS), a state-of-the-art approach, to determine the contacts between the CPC components. Structural predictions of the CPC structure are also made using AlphaFold2, suggesting that coiled coils form between KIN-A and KIN-B, and that KIN-A/B interact with the N termini of CPC1 and CPC2. Experimental results show that CPC1 and CPC2 are unable to localise to kinetochores if they lack their N-terminal domains consistent with these predictions. Altogether these data provide convincing evidence of the protein domains required for CPC kinetochore localisation and CPC protein interactions. However, the authors also conclude that KIN-B plays a minor role in localising the CPC to kinetochores compared to KIN-A. This conclusion is not particularly compelling as it stems from the observation that ectopically expressed GFP-NLS-KIN-A (full length or coiled-coil domain + tail) is also present at kinetochores during anaphase unlike endogenously expressed YFP-KIN-A. Not only is this localisation probably an artifact of the ectopic expression, but the KIN-B coiled-coil domain localises to kinetochores from S to metaphase and Fig S2G appears to show a portion of the expressed KIN-B coiled-coil domain colocalising with KKT2 at anaphase. It is unclear why KIN-B has been discounted here.

Next, using a mixture of RNAi depletion and LacI-LacO recruitment experiments, the authors show that kinetochore proteins KKT7 and KKT9 are required for AUK1 to localise to kinetochores (other KKT8 complex components were not tested here) and that all components of the KKT8 complex are required for KIN-A kinetochore localisation. Further, both KKT7 and KKT8 were able to recruit AUK1 to an ectopic locus in the S phase, and KKT7 recruited KKT8 complex proteins, which the authors suggest indicates it is upstream of KKT8. However, while these experiments have been performed well, the reciprocal experiment to show that KKT8 complex proteins cannot recruit KKT7, which could have confirmed this hierarchy, does not appear to have been performed. Further, since the LacI fusion proteins used in these experiments were ectopically expressed, they were retained (artificially) at kinetochores into anaphase; KKT8 and KIN-A were both able to recruit AUK1 to LacO foci in anaphase, while KKT7 was not. The authors conclude that this suggests the KKT8 complex is the main kinetochore receptor of the CPC - while very plausible, this conclusion is based on a likely artifact of ectopic expression, and for that reason, should be interpreted with a degree of caution.

Further IP-CLMS experiments, in combination with recombinant protein pull-down assays and structural predictions, suggested that within the KKT8 complex, there are two subcomplexes of KKT8:KKT12 and KKT9:KKT11, and that KKT7 interacts with KKT9:KKT11 to recruit the remainder of the KKT8 complex. The authors also assess the interdependencies between KKT8 complex components for localisation and expression, showing that all four subunits are required for the assembly of a stable KKT8 complex and present AlphaFold2 structural modelling data to support the two subcomplex models. In general, these data are of high quality and convincing with a few exceptions. The recombinant pulldown assay (Fig. 4H) is not particularly convincing as the 3rd eluate gel appears to show a band at the size of KKT11 (despite the labelling indicating no KKT11 was present in the input) but no pulldown of KKT9, which was present in the input according to the figure legend (although this may be mislabeled since not consistent with the text). The text also states that 6HIS-KKT8 was insoluble in the absence of KKT12, but this is not possible to assess from the data presented. It is also surprising that data showing the effects of KKT8, KKT9, and KKT12 depletion on KKT11 localisation and abundance are not presented alongside the reciprocal experiments in Fig S4G-J.

The authors also convincingly show that AlphaFold2 predictions of interactions between KKT9:KKT11 and a conserved domain (CD1) in the C-terminal tail of KIN-A are likely correct, with CD1 and a second conserved domain, CD2, identified through sequence analysis, acting synergistically to promote KIN-A kinetochore localisation at metaphase, but not being required for KIN-A to move to the central spindle at anaphase. They then hypothesise that the kinesin motor domain of KIN-A (but not KIN-B which is predicted to be inactive based on non-conservation of residues key for activity) determines its central spindle localisation at anaphase through binding to microtubules. In support of this hypothesis, the authors show that KIN-A, but not KIN-B can bind microtubules in vitro and in vivo. However, ectopically expressed GFP-NLS fusions of full-length KIN-A or KIN-A motor domain did not localise to the central spindle at anaphase. The authors suggest this is due to the GPF fusion disrupting the ATPase activity of the motor domain, but they provide no evidence that this is the case. Instead, they replace endogenous KIN-A with a predicted ATPase-defective mutant (G209A), showing that while this still localises to kinetochores, the kinetochores were frequently misaligned at metaphase, and that it no longer concentrates at the central spindle (with concomitant mis-localisation of AUK1), causing cells to accumulate at anaphase. From these data, the authors conclude that KIN-A ATPase activity is required for chromosome congression to the metaphase plate and its central spindle localisation at anaphase. While potentially very interesting, these data are incomplete in the absence of any experimental data to show that KIN-A possesses ATPase activity or that this activity is abrogated by the G209A mutation, and the conclusions of this section are rather speculative.

Impact:<br /> Overall, this work uses a wide range of cutting-edge molecular and structural predictive tools to provide a significant amount of new and detailed molecular data that shed light on the composition of the unusual trypanosome CPC and how it is assembled and targeted to different cellular locations during cell division. Given the fundamental nature of this research, it will be of interest to many parasitology researchers as well as cell biologists more generally, especially those working on aspects of mitosis and cell division, and those interested in the evolution of the CPC.

Reviewer #1 (Public Review):

Summary:<br /> In this study, Faniyan and colleagues build on their recent finding that renal Glut2 knockout mice display normal fasting blood glucose levels despite massive glucosuria. Renal Glut2 knockout mice were found to exhibit increased endogenous glucose production along with decreased hepatic metabolites associated with glucose metabolism. Crh mRNA levels were higher in the hypothalamus while circulating ACTH and corticosterone were elevated in this model. While these mice were able to maintain normal fasting glucose levels, ablating afferent renal signals to the brain resulted in substantially lower blood glucose levels compared to wildtype mice. In addition, the higher CRH and higher corticosterone levels of the knockout mice were lost following this denervation. Finally, acute phase proteins were altered, plasma Gpx3 was lower, and major urinary protein MUP18 and its gene expression were higher in renal Glut2 knockout mice. Overall, the main conclusion that afferent signaling from the kidney is required for renal glut2 dependent increases in endogenous glucose production is well supported by these findings.

Strengths:<br /> An important strength of the paper is the novelty of the identification of kidney-to-brain communication as being important for glucose homeostasis. Previous studies had focused on other functions of the kidney modulated by or modulating brain activity. This work is likely to promote interest in CNS pathways that respond to afferent renal signals and the response of the HPA axis to glucosuria. Additional strengths of this paper stem from the use of incisive techniques. Specifically, the authors use isotope-enabled measurement of endogenous glucose production by GC-MS/MS, capsaicin ablation of afferent renal nerves, and multifiber recording from the renal nerve. The authors also paid excellent attention to rigor in the design and performance of these studies. For example, they used appropriate surgical controls, confirmed denervation through renal pelvic CGRP measurement, and avoided the confounding effects of nerve regrowth over time. These factors strengthen confidence in their results. Finally, humans with glucose transporter mutations and those being treated with SGLT2 inhibitors show a compensatory increase in endogenous glucose production. Therefore, this study strengthens the case for using renal Glut2 knockout mice as a model for understanding the physiology of these patients.

Weaknesses:<br /> A few weaknesses exist. Clarification of some aspects of the experimental design would improve the manuscript. However, most concerns relate to the interpretation of this study's findings. The authors state that loss of glucose in urine is sensed as a biological threat based on the HPA axis activation seen in this mouse model. This interpretation is understandable but speculative. Importantly, whether stress hormones mediate the increase in endogenous glucose production in this model and in humans with altered glucose transporter function remains to be demonstrated conclusively. For example, the paper found several other circulating and local factors that could be causal. In addition, the approach used in these studies cannot definitively determine whether renal glucose production or only hepatic glucose production was altered. This model is also unable to shed light on how elevated stress hormones might interact with insulin resistance, which is known to increase endogenous glucose production. That issue is of substantial clinical relevance for patients with T2D and metabolic disease. Finally, while findings from the Glut2 knockout mice are of scientific interest, it should be noted that the Glut2 receptor is critical to the function of pancreatic islets and as such is not a good candidate for pharmacological targeting.

Reviewer #2 (Public Review):

Summary:<br /> The authors previously generated renal Glut2 knockout mice, which have high levels of glycosuria but normal fasting glucose. They use this as an opportunity to investigate how compensatory mechanisms are engaged in response to glycosuria. They show that renal and hepatic glucose production, but not metabolism, is elevated in renal Glut2 male mice. They show that renal Glut2 male mice have elevated Crh mRNA in the hypothalamus and elevated plasma levels of ACTH and corticosterone. They also show that temporary denervation of renal nerves leads to a decrease in fasting and fed blood glucose levels in female renal Glut2 mice, but not control mice. Finally, they perform plasma proteomics in male mice to identify plasma proteins with a greater than 25% (up or down) between the knockouts and controls.

Strengths:<br /> The question that is trying to be addressed is clinically important: enhancing glycosuria is a current treatment for diabetes, but is limited in efficacy because of compensatory increases in glucose production.<br /> Also, the mouse line used is an inducible knockout, thus minimizing the impact of compensatory mechanisms engaged in early development.

Weaknesses:<br /> 1) Though the Methods specify that both male and female mice were used, it appears each experiment was performed only on one sex, rather than each experiment being performed on both sexes. For example, renal denervation was performed only on females, whereas all other experiments were performed exclusively on males. This makes it impossible to examine whether there are sex differences in any measures.

2) This study appears to use an inducible Glut2 knockout with tamoxifen, yet nothing describes when the tamoxifen was delivered relative to the experimental manipulations. Was the knockout performed in young animals? In adult animals? This is important both for the ability of readers to repeat the experiment, but also to interpret the results in light of potential compensatory changes (if the knockout was performed at an early age, for example).

3) In Methods, please clarify whether littermate controls were WT, het, or both. If het mice were used as controls, this is potentially problematic.

4) Conclusions like "the HPA axis may contribute to the compensatory increase in glucose production in renal Glut2 knockout mice" (line 215) are premature. All that is shown is that renal Glut2 male mice have elevated HPA activity. There are no experiments establishing causation. For example, the authors could administer a CRF antagonist or a glucocorticoid receptor antagonist in this mouse line, and examine whether this impacts blood glucose. This was not done.

5) If elevated glycosuria drives HPA activity, one would expect to see elevated HPA activity in humans who take SGLT2 inhibitors. Yet, this does not seem to be the case (Higashikawa et al, 2021; see also Perry et al, 2021 for rodent example). This raises the question of whether the glycosuria observed in the mouse line here is relevant to any human conditions. The relevance of the mechanisms proposed here would be much more convincing if a second model of glycosuria was used here (for example, inducing diabetes in mice and treating with SGLT2 inhibitors). Without these types of experiments, any relevance to human conditions is highly speculative and should be reserved for the Discussion. What the authors are studying here is one mechanism for maintaining blood glucose when glycosuria is induced by a genetic knockout.

6) The experiment examining the impact of renal denervation is nice but incomplete. For example, what is the relevance to the hepatic glucose production that was reported? It is interesting that the renal denervation normalized the elevated HPA activity in Glut2 female mice, but it is not clear how this signaling would alter HPA activity.

7) The Methods need to describe the plasma collection procedure for both ELISA and plasma proteomic experiments. What time of day were samples collected? Were samples collected when animals were euthanized from other experiments after experimental manipulations, or in animals without other experimentation?

8) In general, the links between the disparate mechanisms (signals in the plasma, changes in renal activity, changes in HPA activity) are weak. There are more experiments needed to establish a direct kidney-hypothalamus axis. If renal activity elevates blood glucose in the face of glycosuria, why are there no differences in renal activity between control and Glut2 knockout mice? If the blood glucose levels are regulated by renal activity, it must be the sensitivity to the renal activity that differs between control and knockout mice - perhaps this should be investigated. If one stimulates afferent renal nerves, can one drive HPA activation and elevate blood glucose? How are these measures related to the plasma proteins identified? Without these links, this study is descriptive and correlational.

Reviewer #1 (Public Review):

Summary:<br /> In their study, Petersen et al. investigated the relationship between parameters of metabolic syndrome (MetS) and cortical thickness using partial least-squares correlation analysis (PLS) and performed subsequently a group comparison (sensitivity analysis). To do this, they utilized data from two large-scale population-based cohorts: the UK BioBank (UKB) and the Hamburg City Health Study (HCHS). They identified a latent variable that explained 77% of the shared variance, driven by several measures related to MetS, with obesity-related measures having the strongest contribution. Their results highlighted that higher cortical thickness in the orbitofrontal, lateral prefrontal, insular, anterior cingulate, and temporal areas is associated with lower MetS metric severity. Conversely, the opposite pattern was observed in the superior frontal, parietal, and occipital regions. A similar pattern was then observed in the sensitivity analysis when comparing two groups (MetS vs. matched controls) separately. They then mapped local cellular and network topological attributes to the observed cortical changes associated with MetS. This was achieved using cell-type-specific gene expressions from the Allen Human Brain Atlas and the group consensus functional and structural connectomes of the Human Connectome Project (HCP), respectively. This contextualization analysis allowed them to identify potential cellular contributions in these structures driven by endothelial cells, microglial cells, and excitatory neurons. It also indicated functional and structural interconnectedness of areas experiencing similar MetS effects.

Strengths:<br /> The effects of metabolic syndrome on the brain are still incompletely understood, and such multi-scale analyses are important for the field. Despite the study's sole 'correlation-based' nature, it yields valuable results, including several scales of brain parameters (cortical thickness, cellular, and network-based). The results are robust and benefit from two 'large-scale' datasets, resulting in highly powered statistics.

Weaknesses:<br /> However, some concerns arise regarding certain interpretations and claims made by the authors. In particular, it is not entirely convincing that the authors' results are relevant for studying insulin resistance as a clinical measure of MetS. This is due to the use of non-fasting glycemia as a metric, which the authors claim represents insulin resistance. While non-fasting blood glucose is a potential, albeit poor, indicator of insulin resistance, claiming a direct correlation between insulin resistance and cortical thickness does not seem entirely convincing. By doing so, the authors suggest that insulin resistance might have a weak contribution to cortical thickness abnormalities, with a rather low 'loading' of glycemia compared to the other MetS metrics, although this cannot be conclusively determined from these results.

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Petersen et al. aimed for a comprehensive assessment of the relationship between cardiometabolic risk factors and cortical thickness. They found that a latent variable reflecting higher obesity, hypertension, LDL cholesterol, triglyerides, glucose, and lower HDL cholesterol was associated with lower cortical thickness in orbitofrontal, lateral prefrontal, insular, anterior cingulate, and temporal areas. In sensitivity analyses, they showed that this pattern replicated across cohorts and was also consistent with a clinical definition of the metabolic syndrome.

Further, when including cognition in the multivariate analysis, the pattern remained unchanged and indicated that cardiometabolic risk factors were associated with worse cognitive performance across different tests. The authors investigated the cell types implicated in the regions associated with cardiometabolic risk using the Allen brain atlas and found that the density of excitatory neurons type 8, endothelial cells, and microglia reliably co-located with the pattern of cortical thickness. Furthermore, they showed that cortical regions more strongly associated with MetS were more closely structurally & functionally connected than others.

Strengths:<br /> This study performed a comprehensive assessment of the combined association of cardiometabolic risk factors and brain structure and investigated micro- and macroscopic underpinnings. A major strength of the study is the methodological approach of Partial Least Squares which allows the authors to not single out risk factors but to take them into account simultaneously. The large sample size from two cohorts allowed for different sensitivity analyses and convincing evidence for the stability of the first latent variable. The authors demonstrated that the component was also reliably related to cognitive performance, replicating multiple previous studies that evidenced associations of different components of the MetS with worse cognitive performance.

The novel contribution of the study lies in the virtual histology and brain topology investigation of the cortical pattern related to MetS. The virtual histology provided clear evidence of the co-localization of endothelial, glial, and excitatory neuronal cells with the regions of MetS-associated cortical thinning while the brain topology analysis highlighted the disproportionate structural and functional connectivity between associated regions. This analysis provides insights into the role of inflammatory processes and the intricate link between gray matter morphology and microvasculature, both locally and in relation to long-range connectivity. This information is valuable to inform future mechanistic studies.

Weaknesses:<br /> The study is exclusively cross-sectional which does not allow to the authors to disentangle causes from consequences. While studies indicate that most of the differences seen in middle age are probably consequences of the MetS on the vasculature, blood-brain barrier, or inflammatory processes, differences in cortical morphology might also represent a risk factor for weight gain.

Another limitation is the omission of subcortical structures and the cerebellum which might have provided additional information on the pattern of GM differences associated with MetS.

The study is exploratory in nature and for the contextualization analyses it is difficult to judge whether those were selected from a larger pool of analyses. The analysis approach taken to relate the cardiometabolic risk, brain structure, and cognition does not allow the reader to determine whether brain regions most strongly related to the MetS are the ones also most strongly associated with cognitive performance. The cortical pattern arising from the models including cognition is not thoroughly compared to the MetS-only pattern and therefore, it is difficult to estimate to which extent the MetS-related cortical patterns explain variance in cognitive performance.

Reviewer #3 (Public Review):

Summary:<br /> This study investigates the continuous effect of MetS components - namely, obesity, arterial hypertension, dyslipidemia, and insulin resistance - on cortical thickness. It also examines the spatial correlations between MetS effects on cortical thickness with brain cellular and network topological attributes. Additionally, the authors attempt to explore the complex interplay among MetS, cognitive function, and cortical thickness.

The results reveal a latent relationship between MetS and cortical thickness based on a clinical-anatomical dimension. Furthermore, the effect of MetS on cortical thickness is linked to local cell types and network topological attributes. These findings suggest that the authors achieved most, though not all, of their research objectives.

The conclusions are mostly well supported by data and results. However, the use of "was governed by" in the conclusion section suggests a causal relationship. This phrasing is inappropriate given that the study primarily employs correlational analyses.

Strengths<br /> The study presents several strengths:

This study undertakes a comprehensive assessment encompassing the full range of MetS components, such as obesity or arterial hypertension, rather than adopting a case-control study approach (categorizing participants into MetS or non-MetS groups) as seen in some previous research. Utilizing Partial Least Squares (PLS) for correlational analysis effectively addresses issues of multicollinearity (or high covariance among MetS components) and explores the relationship between MetS and brain morphology.

The study leverages two datasets, examining a large sample size of 40,087 individuals. This substantial sample potentially aids in identifying nuanced and underexplored brain anomalies. By incorporating high-quality MRI images, standardized data, and statistical analysis procedures, as well as sensitivity analyses, the results gain robustness, which addresses the limitations of small samples and low reproducibility.

In the context of MetS, this research uniquely employs the concept of imaging transcriptomics, i.e. virtual histology analysis. This approach allows the study to explore intricate relationships between cellular types and cortical thickness anomalies.

Weaknesses<br /> While this work has foundational strengths, the analyses and data seem inadequate to fully support the key claim and analysis. In particular:

After a thorough review of the methods and results sections, I found no direct or strong evidence supporting the authors' claim that the identified latent variables were related to more severe MetS to worse cognitive performance. While a sub-group comparison was conducted, it did not adequately account for confounding factors such as educational level. Additionally, the strength of evidence from such a sub-group comparison is substantially weaker than that from randomized controlled trials or longitudinal cohort studies. Therefore, it is inaccurate for the authors to assert a direct relationship between MetS and cognitive function based on the presented data. A more appropriate research design or data analysis approach, such as mediation analysis, can be employed to address this issue.

The use of the imaging transcriptomics pipeline (virtual histology analysis) to explore the microscale associations with MetS effects on the brain is commendable and has shown promising results. Nevertheless, variations in gene sets may introduce a degree of heterogeneity in the results (Seidlitz, et al., 2020; Martins et al., 2021). Consequently, further validation or exploratory analyses utilizing different gene sets can yield more compelling results and conclusions.

Reviewer #1 (Public Review):

Smirnova et al. present a cryo-EM structure of a nucleosome-SIRT6 complex to understand how the histone deacetylase SIRT6 deacetylates the N-terminal tail of histone H3. The authors obtained the structure at sub-4 Å resolution and can visualize how interactions between the nucleosome and SIRT6 position SIRT6 to allow for H3 tail deacetylation. Through additional conformational analysis of their cryo-EM data, they reveal that SIRT6 positioning is flexible on the nucleosome surface, and this could accommodate the targeting of certain H3 tail residues. This work is significant as it represents the visualization of a histone deacetylase on its native nucleosomal target and reveals how substrate specificity is achieved. Importantly, it should be noted that recently two additional structures of the nucleosome-SIRT6 complex were already published. Therefore, Smirnova et al. confirm and complement these previous findings. Additionally, Smirnova et al. expand our understanding of the structural flexibility of SIRT6 on the nucleosome and clarify that SIRT6 also shows histone deacetylase activity on H3K27Ac.

Reviewer #2 (Public Review):

Smirnova et al. present a cryo-EM structure of human SIRT6 bound to a nucleosome as well as the results from molecular dynamics simulations. The results show that the combined conformational flexibilities of SIRT6 and the N-terminal tail of histone H3 limit the residues with access to the active site, partially explaining the substrate specificity of this sirtuin-class histone deacetylase. Two other groups have recently published cryo-EM structures of SIRT6:nucleosome complexes; this manuscript confirms and complements these previous findings, with the addition of some novel insights into the role of structural flexibility in substrate selection.

Reviewer #3 (Public Review):

Summary: The present study sought to investigate the role ERα expressed in Gabaergic neurons of the rostral periventricular aspect of the third ventricle (RP3V) and medial preoptic nucleus (MPN) in the positive feedback using genetically driven Crispr-Cas9 mediated knockdown of ESR1 in VGAT expressing neurons. ESR1 Knockdown in preoptic gabaergic neurons led to an absence of LH surge and acyclicity when associated with severely reduced kisspeptin (Kp) expression suggesting that a subpopulation of neurons co-expressing Kp and VGAT are key for LH surge since total absence of Kp is associated with an absence of GnRH neuron activation and reduced LH surge. Although the implication of kisspeptin neurons was highly suspected already, the novelty of these results lies in the fact that estrogen signaling is necessary in only a selected fraction of them to maintain both regular cycles and LH surge capacity.

Strengths:<br /> Remarkable aspects of this study are, its dataset which allowed them to segregate animals based on distinct neuronal phenotype matching specific physiological outcomes, the transparency in reporting the results (e.g. all statistical values being reported, all grouping variables being clearly defined, clarity about animals that were excluded and why) and the clarity of the writing. Another remarkable feature of this work lies in the analysis of the dataset. As opposed to the cre-lox approach which theoretically allows for the complete ablation of specific neuronal populations, but may lack specificity regarding timing of action and location, genetically driven in vivo Crispr-Cas9 editing offers both temporal and neuroanatomic selectivity but cannot achieve a complete knock down. This approach based on stereotaxic delivery of the AAV encoded guide RNAs comes with inevitable variability in the location where gene knockdown is achieved. By adjusting their original grouping of the animals based on the evaluation of the extent of kisspeptin expression in the target region, the authors obtained a much clearer and interpretable picture. Although only few animals (n=4) displayed absent kisspeptin expression, the convergence of observations suggesting a central impairment of the reproductive axis is convincing. Finally, the observation that the pulsatile secretion of LH is maintained in the absence of Kp expression in the RP3V lends support to the notion that LH surge and pulsatility are regulated independently by distinct neuronal populations, a model put forward by corresponding author a few years ago.

Reviewer #1 (Public Review):

Summary: The current study examines the necessity of estrogen receptor alpha (ESR1) in GABA neurons located in the anteroventral and preoptic periventricular nuclei and the medial preoptic nucleus of hypothalamus. This brain area is implicated in regulating the pre-ovulatory LH surge in females, but the identity of the estrogen-sensitive neurons that are required remains unknown. The data indicate that approximately 70% knockdown of ESR1 in GABA neurons resulted in variable reproductive phenotypes. However, when the ESR1 knockdown also results in a decrease in kisspeptin expression by these cells, the females had disrupted LH surges, but no alterations in pulsatile LH release. These data support the hypothesis that kisspeptin cells in this region are critical for the pre-ovulatory LH surge in females.

Strengths: The current study examined the efficacy of two guide RNAs to knockdown ESR1 in GABA neurons, resulting in an approximate 70% reduction in ESR1 in GABA neurons. The efficacy of this knockdown was confirmed in the brain via immunohistochemistry and the reproductive outcomes were analyzed several ways to account for differences in guide RNAs or the precise brain region with the ESR1 knockdown. The analysis was taken one step further by grouping mice based on kisspeptin expression following ESR1 knockdown and examining the reproductive phenotypes. Overall, the aims of the study were achieved, the methods were appropriate, and the data were analyzed extensively. This data supports the hypothesis that kisspeptin neurons in the anterior hypothalamus are critical for the preovulatory LH surge.

Weaknesses: One minor weakness in this study is the conclusion that the two different guide RNAs didn't seem to have unique effects on GnRH cFos expression or the reproductive phenotypes. Though the data indicate a 60-70% knockdown for both gRNA2 and gRNA3, 3 of the 4 gRNA2 mice had no cFos expression in GnRH neurons during the time of the LH surge, whereas all mice receiving gRNA3 had at least some cFos/GnRH co-expression. In addition, when mice were re-categorized based on reduction (>75%) in kisspeptin expression, most of the mice in the unilateral or bilateral groups received gRNA2, whereas many of the mice that received gRNA3 were in the "normal" group with no disruption in kisspeptin expression. Whether these results occurred by chance or due to differences in the gRNAs remains unknown. Thus, additional experiments with increased sample sizes would be needed, even if the efficacy of the ESR1 knockdown was comparable, before concluding these 2 gRNAs don't have unique actions.

Reviewer #2 (Public Review):

Clarkson et al investigated the impact of in vivo ESR1 gene disruption selectively in preoptic area GABA neurons on the estrogen regulation of LH secretion. The hypothalamic pathways by which estradiol controls the secretion of gonadotrophins are incompletely understood and relevant to a better understanding of the mechanisms driving fertility and reproduction. Using CRISPR-Cas9 methodology, the authors were able to effectively reduce the expression of estrogen receptor (ER)-alpha in GABA neurons located in the preoptic area of adult female mice. The results obtained were rather variable except in the animals with concomitant suppression of kisspeptin in the rostral periventricular region of the third ventricle (RP3V), which displayed interruption of ovarian cyclicity and an altered estradiol-induced LH surge. The experimental approach used allowed for a cell-selective, temporally-controlled suppression of ER-alpha expression, providing further evidence of the critical role of RP3V kisspeptin neurons in the estrogen positive-feedback effect. The preovulatory LH surge is a variable phenomenon and is better evaluated using serial blood sampling. Although the assessment of the estradiol-induced LH surge was performed in one terminal blood collection, c-Fos expression in GnRH neurons was used as a reliable proxy of the LH surge occurrence. The present findings also suggest that GABA neurotransmission in the preoptic area itself is not involved in the positive-feedback effect of estradiol on LH secretion.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript explores the impact of serotonin on olfactory coding in the antennal lobe of locusts and odor-evoked behavior. The authors use serotonin injections paired with an odor-evoked palp-opening response assay and bath application of serotonin with intracellular recordings of odor-evoked responses from projection neurons (PNs).

Strengths:<br /> The authors make several interesting observations, including that serotonin enhances behavioral responses to appetitive odors in starved and fed animals, induces spontaneous bursting in PNs, and uniformly enhances PN responses to odors. Overall, I had no technical concerns.

Weaknesses:<br /> While there are several interesting observations, the conclusions that serotonin enhanced sensitivity specifically and that serotonin had feeding-state-specific effects, were not supported by the evidence provided. Furthermore, there were other instances in which much more clarification was needed for me to follow the assumptions being made and inadequate statistical testing was reported.

Major concerns.<br /> -To enhance olfactory sensitivity, the expected results would be that serotonin causes locusts to perceive each odor as being at a relatively higher concentration. The authors recapitulate a classic olfactory behavioral phenomenon where higher odor concentrations evoke weaker responses which is indicative of the odors becoming aversive. If serotonin enhanced the sensitivity to odors, then the dose-response curve should have shifted to the left, resulting in a more pronounced aversion to high odor concentrations. However, the authors show an increase in response magnitude across all odor concentrations. I don't think the authors can claim that serotonin enhances the behavioral sensitivity to odors because the locusts no longer show concentration-dependent aversion. Instead, I think the authors can claim that serotonin induces increased olfactory arousal.

-The authors report that 5-HT causes PNs to change from tonic to bursting and conclude that this stems from a change in excitability. However, excitability tests (such as I/V plots) were not included, so it's difficult to disambiguate excitability changes from changes in synaptic input from other network components.

-There is another explanation for the theoretical discrepancy between physiology and behavior, which is that odor coding is further processing in higher brain regions (ie. Other than the antennal lobe) not studied in the physiological component of this study. This should at least be discussed.

-The authors cannot claim that serotonin underlies a hunger state-dependent modulation, only that serotonin impacts responses to appetitive odors. Serotonin enhanced PORs for starved and fed locusts, so the conclusion would be that serotonin enhances responses regardless of the hunger state. If the authors had antagonized 5-HT receptors and shown that feeding no longer impacts POR, then they could make the claim that serotonin underlies this effect. As it stands, these appear to be two independent phenomena.

Reviewer #2 (Public Review):

Summary:<br /> The authors investigate the influence of serotonin on feeding behavior and electrophysiological responses in the antennal lobe of locusts. They find that serotonin injection changes behavior in an odor-specific way. In physiology experiments, they can show that antennal lobe neurons generally increase their baseline firing and odor responses upon serotonin injection. Using a modeling approach the authors propose a framework on how a general increase in antennal lobe output can lead to odor-specific changes in behavior. The authors finally suggest that serotonin injection can mimic a change in a hunger state.

Strengths:<br /> This study shows that serotonin affects feeding behavior and odor processing in the antennal lobe of locusts, as serotonin injection increases activity levels of antennal lobe neurons. This study provides another piece of evidence that serotonin is a general neuromodulator within the early olfactory processing system across insects and even phyla.

Weaknesses:<br /> I have several concerns regarding missing control experiments, unclear data analysis, and interpretation of results.

A detailed description of the behavioral experiments is lacking. Did the authors also provide a mineral oil control and did they analyze the baseline POR response? Is there an increase in baseline response after serotonin exposure already at the behavioral output level? It is generally unclear how naturalistic the chosen odor concentrations are. This is especially important as behavioral responses to different concentrations of odors are differently modulated after serotonin injection (Figure 2: Linalool and Ammonium).

Regarding recordings of potential PNs - the authors do not provide evidence that they did record from projection neurons and not other types of antennal lobe neurons. Thus, these claims should be phrased more carefully.

The presented model suggests labeled lines in the antennal lobe output of locusts. Could the presented model also explain a shift in behavior from aversion to attraction - such as seen in locusts when they switch from a solitarious to a gregarious state? The authors might want to discuss other possible scenarios, such as that odor evaluation and decision-making take place in higher brain regions, or that other neuromodulators might affect behavioral output. Serotonin injections could affect behavior via modulation of other cell types than antennal lobe neurons. This should also be discussed - the same is true for potential PNs - serotonin might not directly affect this cell type, but might rather shut down local inhibitory neurons.

Finally, the authors claim that serotonin injection can mimic the starved state behavioral response. However, this is only shown for one of the four odors that are tested for behavior (HEX), thus the data does not support this claim.

Reviewer #1 (Public Review):

Summary:<br /> Animals in natural environments need to identify predator-associated cues and respond with the appropriate behavioral response to survive. In rodents, some chemical cues produced by predators (e.g., cat saliva) are detected by chemosensory neurons in the vomeronasal organ (VNO). The VNO transmits predator-associated information to the accessory olfactory bulb, which in turn projects to the medial amygdala and the bed nucleus of the stria terminalis, two regions implicated in the initiation of antipredator defensive behaviors. A downstream area to these two regions is the ventromedial hypothalamus (VMH), which has been shown to control both active (i.e., flight) and passive (i.e, freezing) antipredator defensive responses via distinct efferent projections to the anterior hypothalamic nucleus or the periaqueductal gray, respectively. However, whether differences in predator-associated sensory information initially processed in the VNO and further conveyed to the VMH can trigger different types of behavioral responses remained unexplored. To address this question, here the authors investigated the behavioral responses of mice exposed to either fresh or old cat saliva, and further compared the underlying neural circuits that are activated by cat saliva with different freshness.

The scientific question of the study is valid, the experiments were well-performed, and the statistical analyses are appropriate. However, there are some concerns that may directly affect the main interpretation of the results.

Major Concerns:<br /> 1. An important point that the authors should clarify in this study is whether mice are detecting qualitative or quantitative differences between fresh and old cat saliva. Do the environmental conditions in which the old saliva was maintained cause degradation of Fel d 4, the main protein known for inducing a defensive response in rodents? (see Papes et al, 2010 again). If that is the case, one would expect that a lower concentration of Fel d 4 in the old saliva after protein degradation would result in reduced antipredator responses. Alternatively, if the authors believe that different proteins that are absent in the old saliva are contributing to the increased defensive responses observed with the fresh saliva, further protein quantification experiments should be performed. An important experiment to differentiate qualitative versus quantitative differences between the two types of saliva would be diluting the fresh saliva to verify if the amount of protein, rather than the type of protein, is the main factor regulating the behavioral differences.

2. The authors claim that fresh saliva is recognized as an immediate danger by rodents, whereas old saliva is recognized as a trace of danger. However, the study lacks empirical tests to support this interpretation. With the current experimental tests, the behavioral differences between animals exposed to fresh vs. old saliva could be uniquely due to the reduced amount of the exact same protein (e.g., Fel d 4) in the two samples of saliva.

3. In Figure 4H, the authors state that there were no significant differences in the number of cFos-positive cells between the two saliva-exposed groups. However, this result disagrees with the next result section showing that fresh and old saliva differentially activate the VMH. It is unclear why cFos quantification and behavioral correlations were not performed in other upstream areas that connect the VNO to the VMH (e.g., BNST, MeA, and PMCo). That would provide a better understanding of how brain activity correlates with the different types of behaviors reported with the fresh vs. old saliva.

4. The interpretation that fresh and old saliva activates different subpopulations of neurons in the VMH based on the observation that cFos positively correlates with freezing responses only with the fresh saliva lacks empirical evidence. To address this question, the authors should use two neuronal activity markers to track the response of the same population of VHM cells within the same animals during exposure to fresh vs. old saliva. Alternatively, they could use single-cell electrophysiology or imaging tools to demonstrate that cat saliva of distinct freshness activates different subpopulations of cells in the VMH. Any interpretation without a direct within-subject comparison or the use of cell-type markers would become merely speculative. Furthermore, the authors assume that differential activations of mitral cells between fresh and old saliva result in the differential activation of VMH subpopulations (page 13, line 3). However, there are intermediate structures between the mitral cells and the VMH, which are completely ignored in this study (e.g., BNST, medial amygdala).

5. The authors incorrectly cited the Papes et al., 2010 article on several occasions across the manuscript. In the introduction, the authors cited the Papes et al 2010 study to make reference to the response of rodents to chemical cues, but the Papes et al. study did not use any of the chemical cues listed by the authors (e.g., fox feces, snake skin, cat fur, and cat collars). Instead, the Papes et al. 2010 article used the same chemical cue as the present study: cat saliva. The Papes et al. 2010 article was miscited again in the results section where the authors cited the study to make reference to other sources of cat odor that differ from the cat saliva such as cat fur and cat collars. Because the Papes et al. 2010 article has previously shown the involvement of Trpc2 receptors in the VNO for the detection of cat saliva and the subsequent expression of defensive behaviors by using Trpc2-KO mice, the authors should properly cite this study in the introduction and across the manuscript when making reference to their findings.

6. In the introduction, the authors hypothesized that the VNO detects predator cues and sends sensory signals to the VMH to trigger defensive behavioral decisions and stated that direct evidence to support this hypothesis is still missing. However, the evidence that cat saliva activates the VMH and that activity in the VMH is necessary for the expression of antipredator defensive response in rodents has been previously demonstrated in a study by Engelke et al., 2021 (PMID: 33947849), which was entirely omitted by the authors.

7. In the discussion, the authors stated that their findings suggest that the induction of robust freezing behavior is mediated by a distinct subpopulation of VMH neurons. The authors should cite the study by Kennedy et al., 2020 (PMID: 32939094) that shows the involvement of VMH in the regulation of persistent internal states of fear, which may provide an alternative explanation for why distinct concentrations of saliva could result in different behavioral outcomes.

8. The anatomical connectivity between the olfactory system and the ventromedial hypothalamus (VMH) in the abstract is unclear. The authors should clarify that the VMH does not receive direct inputs from the vomeronasal organ (VNO) nor the accessory olfactory bulb (AOB) as it seems in the current text.

Reviewer #2 (Public Review):

In this study, Nguyen et al. showed that cat saliva can robustly induce freezing behavior in mice. This effect is mediated through the accessory olfactory system as it requires physical contact and is abolished in Trp2 KO mice. The authors further showed that V2R-A4 cluster is responsive to cat saliva. Lastly, they demonstrated c-Fos induction in AOB and VMHdm/c by the cat saliva. The c-Fos level in the VMHdm/c is correlated with the freezing response.

Strength:<br /> The study opens an interesting direction. It reveals the potential neural circuit for detecting cat saliva and driving defense behavior in mice. The behavior results and the critical role of the accessory olfactory system in detecting cat saliva are clear and convincing.

Weakness:<br /> The findings are relatively preliminary. The identities of the receptor and the ligand in the cat saliva that induces the behavior remain unclear. The identity of VMH cells that are activated by the cat saliva remains unclear. There is a lack of targeted functional manipulation to demonstrate the role of V2R-A4 or VMH cells in the behavioral response to cat saliva.

Reviewer #3 (Public Review):

Summary:<br /> Nguyen et al show data indicating that the vomeronasal organ (VNO) and ventromedial hypothalamus (VMH) are part of a circuit that elicits defensive responses induced by predator odors. They also show that using fresh or old predator saliva may be a method to change the perceived imminence of predation. The authors also identify a family of VNO receptors that are activated by cat saliva. Next, the authors show how different components of this defensive circuit are activated by saliva, as measured by fos expression. Though interesting, the findings are not all integrated into a single narrative, and some of the results are only replications of earlier findings using modern methods. Overall, these findings provide incremental advance.

Strengths:<br /> 1 Predator saliva is a stimulus of high ethological relevance<br /> 2 The authors performed a careful quantification of fos induction across the anterior-posterior axis in Figure 6.

Weaknesses:<br /> 1 It is unclear if fresh and old saliva indeed alter the perceived imminence predation, as claimed by the authors. Prior work indicates that lower imminence induces anxiety-related actions, such as re-organization of meal patterns and avoidance of open spaces, while slightly higher imminence produces freezing. Here, the authors show that fresh and old predator saliva only provoke different amounts of freezing, rather than changing the topography of defensive behaviors, as explained above. Another prediction of predatory imminence theory would be that lower imminence induced by old saliva should produce stronger cortical activation, while fresh saliva would activate the amygdala, if these stimuli indeed correspond to significantly different levels of predation imminence.

2 It is known that predator odors activate and require AOB, VNO, and VMH, thus replications of these findings are not novel, decreasing the impact of this work.

3 There is a lack of standard circuit dissection methods, such as characterizing the behavioral effects of increasing and decreasing the neural activity of relevant cell bodies and axonal projections, significantly decreasing the mechanistic insights generated by this work.

4 The correlation shown in Figure 5c may be spurious. It appears that the correlation is primarily driven by a single point (the green square point near the bottom left corner). All correlations should be calculated using Spearman correlation, which is non-parametric and less likely to show a large correlation due to a small number of outliers. Regardless of the correlation method used, there are too few points in Figure 5c to establish a reliable correlation. Please add more points to 5c.

5 Some of the findings are disconnected from the story. For example, the authors show that V2R-A4-expressing cells are activated by predator odors. Are these cells more likely to be connected to the rest of the predatory defense circuit than other VNO cells?

6 Were there other behavioral differences induced by fresh compared to old saliva? Do they provoke differences in stretch-attend risk evaluation postures, number of approaches, the average distance to odor stimulus, the velocity of movements towards and away from the odor stimulus, etc?

Reviewer #3 (Public Review):

The main problem with the work is that the results are only descriptive and do not allow any inferences or conclusions about the importance of the function of G4 structures. The discussion and conclusions are poor. The results are preliminary and in order to try to make the analysis more interesting, it should be further extended and the data must be explored in a much greater depth.

Reviewer #1 (Public Review):

Summary:

This study explores the relationship between guanine-quadruplex (G4) structures and pathogenicity islands (PAIs) in 89 pathogenic strains. G4 structures were found to be non-randomly distributed within PAIs and conserved within the same strains. Positive correlations were observed between G4s and GC content across various genomic features, suggesting a link between G4 structures and GC-rich regions. Differences in GC content between PAIs and the core genome underscored the unique nature of PAIs. High-confidence G4 structures in Escherichia coli's regulatory regions were identified, influencing DNA integration within PAIs. These findings shed light on the molecular mechanisms of G4-PAI interactions, enhancing our understanding of bacterial pathogenicity and G4 structures in infectious diseases.

Strengths:

The findings of this study hold significant implications for our understanding of bacterial pathogenicity and the role of guanine-quadruplex (G4) structures.

Molecular Mechanisms of Pathogenicity: The study highlights that G4 structures are not randomly distributed within pathogenicity islands (PAIs), suggesting a potential role in regulating pathogenicity. This insight into the uneven distribution of G4s within PAIs provides a basis for further research into the molecular mechanisms underlying bacterial pathogenicity.

Conservation of G4 Structures: The consistent conservation of G4 structures within the same pathogenic strains suggests that these structures might play a vital and possibly conserved role in the pathogenicity of these bacteria. This finding opens doors for exploring how G4s influence virulence across different pathogens.

Unique Nature of PAIs: The differences in GC content between PAIs and the core genome underscore the unique nature of PAIs. This distinction suggests that factors such as DNA topology and G4 structures might contribute to the specialized functions and characteristics of PAIs, which are often associated with virulence genes.

Regulatory Role of G4s: The identification of high-confidence G4 structures within regulatory regions of Escherichia coli implies that these structures could influence the efficiency or specificity of DNA integration events within PAIs. This finding provides a potential mechanism by which G4s can impact the pathogenicity of bacteria.

Weaknesses:

No weaknesses were identified by this reviewer.

Overall, the study provides fundamental insights into the pathogenicity island and conservation of G4 motifs.

Reviewer #2 (Public Review):

Summary:

In the manuscript entitled "The Intricate Relationship of G-Quadruplexes and Pathogenicity Islands: A Window into Bacterial Pathogenicity" Bo Lyu explored the interactions between guanine-quadruplex (G4) structures and pathogenicity islands (PAIs) in 89 bacterial genomes through a rigorous computational approach. This paper handles an intriguing and complex topic in the field of pathogenomics. It has the potential to contribute significantly to the understanding of G4-PAI interactions and bacterial pathogenicity.

Strengths:

- The chosen research area.<br /> - The summarizing of the results through neat illustrations.

Weaknesses:

This reviewer did not find any significant weaknesses.

Reviewer #2 (Public Review):

Summary:

This study by Sun et al. identifies a novel role for IBTK in promoting cancer protein translation, through regulation of the translational helicase eIF4A1. Using a multifaceted approach, the authors demonstrate that IBTK interacts with and ubiquitinates eIF4A1 in a non-degradative manner, enhancing its activation downstream of mTORC1/S6K1 signaling. This represents a significant advance in elucidating the complex layers of dysregulated translational control in cancer.

Strengths:

A major strength of this work is the convincing biochemical evidence for a direct regulatory relationship between IBTK and eIF4A1. The authors utilize affinity purification and proximity labeling methods to comprehensively map the IBTK interactome, identifying eIF4A1 as a top hit. Importantly, they validate this interaction and the specificity for eIF4A1 over other eIF4 isoforms by co-immunoprecipitation in multiple cell lines. Building on this, they demonstrate that IBTK catalyzes non-degradative ubiquitination of eIF4A1 both in cells and in vitro through the E3 ligase activity of the CRL3-IBTK complex. Mapping IBTK phosphorylation sites and showing mTORC1/S6K1-dependent regulation provides mechanistic insight. The reduction in global translation and eIF4A1-dependent oncoproteins upon IBTK loss, along with clinical data linking IBTK to poor prognosis, support the functional importance.

Weaknesses:

While these data compellingly establish IBTK as a binding partner and modifier of eIF4A1, a remaining weakness is the lack of direct measurements showing IBTK regulates eIF4A1 helicase activity and translation of target mRNAs. While the effects of IBTK knockout/overexpression on bulk protein synthesis are shown, the expression of multiple eIF4A1 target oncogenes remains unchanged.

Summary:

Overall, this study significantly advances our understanding of how aberrant mTORC1/S6K1 signaling promotes cancer pathogenic translation via IBTK and eIF4A1. The proteomic, biochemical, and phosphorylation mapping approaches established here provide a blueprint for interrogating IBTK function. These data should galvanize future efforts to target the mTORC1/S6K1-IBTK-eIF4A1 axis as an avenue for cancer therapy, particularly in combination with eIF4A inhibitors.

Reviewer #1 (Public Review):

In this study, the authors examined the role of IBTK, a substrate-binding adaptor of the CRL3 ubiquitin ligase complex, in modulating the activity of the eiF4F translation initiation complex. They find that IBTK mediates the non-degradative ubiquitination of eiF4A1, promotes cap-dependent translational initiation, nascent protein synthesis, oncogene expression, and tumor cell growth. Correspondingly, phosphorylation of  IBTK by mTORC1/ S6K1 increases eIF4A1 ubiquitination and sustains oncogenic translation.

Strengths:

This study utilizes multiple biochemical, proteomic, functional, and cell biology assays to substantiate their results.  Importantly, the work nominates IBTK as a unique substrate of mTORC1, and further validates eiF4A1 ( a crucial subunit of the ei44F complex) as a promising therapeutic target in cancer. Since IBTK interacts broadly with multiple members of the translational initial complex - it will be interesting to examine its role in eiF2alpha-mediated ER stress as well as eiF3-mediated translation. Additionally, since IBTK exerts pro-survival effects in multiple cell types, it will be of relevance to characterize the role of IBTK in mediating increased mTORC1 mediated translation in other tumor types, thus potentially impacting their treatment with eiF4F inhibitors.

Limitations/Weaknesses:

The findings are mostly well supported by data, but some areas need clarification and could potentially be enhanced with further experiments:

1) Since eiF4A1 appears to function downstream of IBTK1, can the effects of IBTK1 KO/KD in reducing puromycin incorporation (in Fig 3A),  cap-dependent luciferase reporter activity (Fig 3G), reduced oncogene expression ( Fig 4A) or 2D growth/ invasion assays (Fig 4) be overcome or bypassed by overexpressing eiF4A1? These could potentially be tested in future studies. 

2) The decrease in nascent protein synthesis in puromycin incorporation assays in Figure 3A suggest that the effects of IBTK KO are comparable to and additive with silvesterol. It would be of interest to examine whether silvesterol decreases nascent protein synthesis or increases stress granules in the IBTK KO cells stably expressing IBTK as well. 

3) The data presented in Figure 5 regarding the role of mTORC1 in IBTK-mediated eiF4A1 ubiquitination needs further clarification on several points:

- It is not clear if the experiments in Figure 5F with Phos-tag gels are using the FLAG-IBTK deletion mutant or the peptide containing the mTOR sites as it is mentioned on line 517, page 19 "To do so, we generated an IBTK deletion mutant (900-1150 aa) spanning the potential mTORC1-regulated phosphorylation sites" This needs further clarification.

-It may be of benefit to repeat the Phos tag experiments with full-length FLAG-IBTK and/or endogenous IBTK with molecular weight markers indicating the size of migrated bands.

-Additionally, torin or Lambda phosphatase treatment may be used to confirm the specificity of the band in separate experiments.

-Phos-tag gels with the IBTK CRISPR KO line would also help confirm that the non-phosphorylated band is indeed IBTK. 

-It is unclear why the lower, phosphorylated bands seem to be increasing (rather than decreasing) with AA starvation/ Rapa in Fig 5H.

Reviewer #1 (Public Review):

Summary:<br /> In this study, the authors investigated the mechanisms to repair DSBs induced in euchromatic (Eu) or heterochromatic (Het) contexts in Drosophila. They used a previously described reporter construct that can be used to differentiate between HR, SSA, and mutagenic end joining in response to an I-SceI-induced DSB. Different sub-pathways of end joining (NHEJ, MMEJ, and SD-MMEJ) could be further distinguished by DNA sequence analysis. The main findings of the study are: (1) HR repair is more frequent in Het than in the Eu context; (2) mutagenic EJ repair is more frequent than HR in both contexts; (3) sub-pathways of mutagenic EJ are variable even within the same chromatin domain; and (4) SD-MMEJ repair is associated with larger deletions in the Eu than within the Het compartment.

Strengths:<br /> Overall, the study is well designed and the use of the Bam promoter to drive I-SceI removes some of the variability observed in previous studies. Importantly, the observation of different repair outcomes using the same reporter integrated at different genomic sites suggests that repair is influenced by chromatin state in addition to local DNA sequence context.

Weaknesses:<br /> The main concern I have is the use of only one Eu site versus four for the Het insertions. Given the variability observed between the Het insertions, analysis of a second Eu insertion would give more confidence that the differences observed are significant. One puzzling finding is that HR is increased when the reporter is inserted within the Het domain relative to the Eu domain, suggesting more end resection, yet deletions are smaller for the Het insertions. Bright Ddc2/ATRIP focus formation at DSBs induced in the Het domain is consistent with extensive end resection in this compartment. The authors speculate that this finding could indicate differences in the density of RPA loading or recruitment of Pol theta near ends. I recognize that measuring RPA density on single-stranded DNA would be extremely challenging, but is it known if Pol theta is recruited to DSBs within the Het domain before they move to the periphery?

Reviewer #2 (Public Review):

Summary:<br /> The authors seek to vary the integration site of a double-strand break repair reporter and assess how the chromatin state of different reporter integration sites impacts the contribution of various DSB repair pathways.

Strengths:<br /> It addresses repair in vivo. The reporter improves assay reliability (relative to previous fly DSB repair substrates) by inducing I-SceI within a more narrow and well-defined expression window. The authors' characterization of the spectrum of a-EJ products by sequencing is largely rigorous and thorough, and this often difficult to communicate data is presented in a clear and easily digested manner.

Weaknesses:<br /> The use of the single euchromatic site undercuts their ability to generalize the impact of chromatin state. This concern is minor when considering repair by HR, as repair efficiency appears to vary little when comparing repair across the 4 different heterochromatic sites. Still, it is possible the single euchromatic site they used is an outlier in its sparing use of HR. The assessment of repair by alt-EJ is more problematic, though, since the character of repair appears to vary as much across the different heterochromatic sites as it does comparing a given heterochromatic site vs. the euchromatic site. For example, focusing on their central argument (decreased deletion during SD-MMEJ at heterochromatic sites), the difference between Het2 and all other sites appears to be more dramatic than the difference between Het1 and the single euchromatic site (Figure 5A, Supp Fig 2).

Reviewer #3 (Public Review):

Summary:<br /> In this manuscript, Chiolo and colleagues adapt a Drosophila induced-DSB repair outcome assay to the spermatogonia. In order to compare the outcomes in H3K9me-rich centromeric heterochromatin with a euchromatic site they use a cross to a silencing mutant to reveal the sequence changes in the reporter, which otherwise are not expressed. The authors corroborate that homologous recombination (HR) is up-regulated in this chromatin context, consistent with prior studies. Applying sequencing to mutagenic products the authors reveal context-dependent preferences in mutagenic end joining pathways and mechanisms, although these seem less categorical in terms of hetero- and euchromatin and instead sensitive to more subtle aspects of the local chromatin landscape. One theme, however, is that the microhomologies used for synthesis-dependent end joining are nearer to the induced DSB in heterochromatin than seen for the euchromatic DSB.

Strengths:<br /> 1. The use of the mitotically active spermatogonia and transient expression of the I-SceI to induce the DSB mitigates some caveats of prior experimental approaches including the fact that the cells are universally mitotically active. This approach also enables the outcomes to be assayed in the next generation, which is necessary for reporters expressed within heterochromatin. Thus, this is a technological tool that will be useful to other groups.

2. The observations suggest that MMEJ within heterochromatin (inferred to be Pol theta-dependent) prefers to use microhomologies close to the DSB. This suggests that either DSB end resection or RPA loading/removal is modulated by chromatin context, which is a new finding.

Weaknesses:<br /> 1. The observation that HR is preferred in heterochromatin has been documented in many prior systems.

2. Although the conclusions of the authors are well-supported by the data, the study is somewhat limited in mechanistic detail and would be strengthened by additional use of the genetic tools in the model system, particularly with regard to whether the preference for using microhomologies near the DSB in heterochromatin arises due to modulation of resection or RPA loading stability (the latter is the preferred interpretation of the authors, but goes untested). Nucleosome stability, presence of HP1, etc. seem attractive.

3. Given the variability observed for EJ pathway usage at the four heterochromatic genomic sites probed in the manuscript there is some concern that a single euchromatic site may not be sufficient for rigorous comparisons. This is particularly true because there seems to be little transcription at the "euchromatic" region (Fig. S5). Given that we do not know what matters to dictate the outcomes (epigenetic modifications and/or transcriptional status), this is concerning.

4. (Minor) Some caution should be stated in comparing the HR frequency between this system (low single digits) and prior induction/tissue systems (~20%) because the time domain of cut and repair cycles is vastly different.

5. (Minor) While there are certainly strengths to using the spermatogonia system, one also wonders if it might not have some unique biology given the importance of maintaining genome integrity in this tissue (e.g. the piRNA pathways to repress transposon mobilization). A comment on this point would be welcomed.

6. (Minor) The authors argue that alt-EJ is less mutagenic as a consequence of the observed use of microhomologues closer to the DSB, but what they really mean perhaps is that less sequence is lost? A mutagenic outcome can be equally deleterious in other cases if 1, 5, or 20+ bps are lost, depending on the context.

Reviewer #1 (Public Review):

The authors sought to resolve the coordinated functions of the two muscles that primarily power flight in birds (supracoracoideus and pectoralis), with particular focus on the pectoralis. Technology has limited the ability to resolve some details of pectoralis function, so the authors developed a model that can make accurate predictions about this muscle's function during flight. The authors first measured aerodynamic forces, wing shape changes, and pectoralis muscle activity in flying doves. They used cutting-edge techniques for the aerodynamic and wing shape measurements and they used well-established methods to measure activity and length of the pectoralis muscle. The authors then developed two mathematical models to estimate the instantaneous force vector produced by the pectoralis throughout the wing stroke. Finally, the authors applied their mathematical models to other-sized birds in order to compare muscle physiology across species.

The strength of the methods is that they smoothly incorporate techniques from many complementary fields to generate a comprehensive model of pectoralis muscle function during flight. The high-speed structured-light technique for quantifying surface area during flight is novel and cutting-edge, as is the aerodynamic force platform used. These methods push the boundaries of what has historically been used to quantify their respective aspects of bird flight and their use here is exciting. The methods used for measuring muscle activation and length are standard in the field. Together, these provide both a strong conceptual foundation for the model and highlight its novelty. This model allows for estimations of muscle function that are not feasible to measure in live birds during flight at present. The weakness of this approach is that it relies heavily on a series of assumptions. While the research presented in this paper makes use of powerful methods from multiple fields, those methods each have assumptions inherent to them that simplify the biological system of study. This reduction in the complexity of phenomena allows specific measurements to be made. In joining the techniques of multiple fields to study greater complexity of the phenomenon of interest, the assumptions are all incorporated also. Furthermore, assumptions are inherent to mathematical modelling of biological phenomena. That being said, the authors acknowledge and justify their assumptions at each step and their model seems to be quite good at predicting muscle function.

Indeed, the authors achieve their aims. They effectively integrate methods from multiple disciplines to explore the coordination and function of the pectoralis and supracoracoideus muscles during flight. The conclusions that the authors derive from their model address the intended research aim.

The authors demonstrate the value of such interdisciplinary research, especially in studying complex behaviors that are difficult or infeasible to measure in living animals. Additionally, this work provides predictions for muscle function that can be tested empirically. These methods are certainly valuable for understanding flight, but also have implications for biologists studying movement and muscle function more generally.

Reviewer #2 (Public Review):

In this work, the authors investigated the pectoralis work loop and the function of the supracoracoideus muscle in the down stroke during slow flight in doves. The aim of this study was to determine how aerodynamic force is generated, using simultaneous high-speed measurements of the wings' kinematics, aerodynamics, and activation and strain of pectoralis muscles during slow flight. The measurements show a reduction in the angle of attack during mid-downstroke, which induces a peak power factor and facilitates the tensioning of the supracoracoideus tendon with pectoralis power, which then can be released in the up-stroke. By combining the data with a muscle mechanics model, the timely tuning of elastic storage in the supracoracoideus tendon was examined and showed an improvement of the pectoralis work loop shape factor. Finally, other bird species were integrated into the model for a comparative investigation.

The major strength of the methods is the simultaneous application of four high-speed techniques - to quantify kinematics, aerodynamics and muscle activation and strain - as well as the implementation of the time-resolved data into a muscle mechanics model. With a thorough analysis which supports the conclusions convincingly, the authors achieved their goal of reaching an improved understanding of the interplay of the pectoralis and supracoracoideus muscles during slow flight and the resulting energetic benefits.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript builds upon the authors' previous work on the cross-talk between transcription initiation and post-transcriptional events in yeast gene expression. These prior studies identified an mRNA 'imprinting' phenomenon linked to genes activated by the Rap1 transcription factor (TF), a surprising role for the Sfp1 TF in promoting RNA polymerase II (RNAPII) backtracking, and a role for the non-essential RNAPII subunits Rpb4/7 in the regulation of mRNA decay and translation. Here the authors aimed to extend these observations to provide a more coherent picture of the role of Sfp1 in transcription initiation and subsequent steps in gene expression. They provide evidence for (1) a physical interaction between Sfp1 and Rpb4, (2) Sfp1 binding and stabilization of mRNAs derived from genes whose promoters are bound by both Rap1 and Sfp1 and (3) an effect of Sfp1 on Rpb4 binding or conformation during transcription elongation.

Strengths:<br /> This study provides evidence that a TF (yeast Sfp1), in addition to stimulating transcription initiation, can at some target genes interact with their mRNA transcripts and promote their stability. Sfp1 thus has a positive effect on two distinct regulatory steps. Furthermore, evidence is presented indicating that strong Sfp1 mRNA association requires both Rap1 and Sfp1 promoter binding and is increased at a sequence motif near the polyA track of many target mRNAs. Finally, they provide compelling evidence that Sfp1-bound mRNAs have higher levels of RNAPII backtracking and altered Rpb4 association or conformation compared to those not bound by Sfp1.

Weaknesses:<br /> The Sfp1-Rpb4 association is supported only by a two-hybrid assay that is poorly described and lacks an important control. Furthermore, there is no evidence that this interaction is direct, nor are the interaction domains on either protein identified (or mutated to address function).

The contention that Sfp1 nuclear export to the cytoplasm is transcription-dependent is not well supported by the experiments shown, which are not properly described in the text and are not accompanied by any primary data.<br /> The presence of Sfp1 in P-bodies is of unclear relevance and the authors do not ask whether Sfp1-bound mRNAs are also present in these condensates.

Further analysis of Sfp1-bound mRNAs would be of interest, particularly to address the question of whether those from ribosomal protein genes and other growth-related genes that are known to display Sfp1 binding in their promoters are regulated (either stabilized or destabilized) by Sfp1.

The authors need to discuss, and ideally address, the apparent paradox that their previous findings showed that Rap1 acts to destabilize its downstream transcripts, i.e. that it has the opposite effect of Sfp1 shown here.

Finally, recent studies indicate that the drugs used here to measure mRNA stability induce a strong stress response accompanied by rapid and complex effects on transcription. Their relevance to mRNA stability in unstressed cells is questionable.

Reviewer #1 (Public Review):

Li et al. report here on the expression of a G-protein subunit Gng13 in ectopic tuft cells that develop after severe pulmonary injury in mice. By deleting this gene in ectopic tuft cells as they arise, the authors observed worsened lung injury and greater inflammation after influenza infection, as well as a decrease in the overall number of ectopic tuft cells. This was in stark contrast to the deletion of Trpm5, a cation channel generally thought to be required for all functional gustatory signaling in tuft cells, where no phenotype is observed. Strengths here include a thorough assessment of lung injury via a number of different techniques. Weaknesses are notable: confusingly, these findings are at odds with reports from other groups demonstrating no obvious phenotype upon influenza infection in mice lacking the transcription factor Pou2f3, which is essential for all tuft cell specification and development. The authors speculate that heterogeneity within nascent tuft cell populations, specifically the presence of pro- and anti-inflammatory tuft cells, may explain this difference, but they do not provide any data to support this idea.

Reviewer #2 (Public Review):

Summary:<br /> The study by Li et al. aimed to demonstrate the role of the G𝛾13-mediated signal transduction pathway in tuft cell-driven inflammation resolution and repairing injured lung tissue. The authors showed a reduced number of tuft cells in the parenchyma of G𝛾13 null lungs following viral infection. Mice with a G𝛾13 null mutation showed increased lung damage and heightened macrophage infiltration when exposed to the H1N1 virus. Their further findings suggested that lung inflammation resolution, epithelial barrier, and fibrosis were worsened in G𝛾13 null mutants.

Strengths:<br /> The beautiful immunostaining findings do suggest that the number of tuft cells is decreased in Gr13 null mutants.

Weaknesses:<br /> The description of phenotypes, and the approaches used to measure the phenotypes are problematic. Rigorous investigation of the mouse lung phenotypes is needed to draw meaningful conclusions.

Reviewer #1 (Public Review):

Summary:<br /> In this paper, Song, Shi, and Lin use an existing deep learning-based sequence model to derive a score for each haplotype within a genomic region, and then perform association tests between these scores and phenotypes of interest. The authors then perform some downstream analyses (fine-mapping, various enrichment analyses, and building polygenic scores) to ensure that these associations are meaningful. The authors find that their approach allows them to find additional associations, the associations have biologically interpretable enrichments in terms of tissues and pathways, and can slightly improve polygenic scores when combined with standard SNP-based PRS.

Strengths:<br /> - I found the central idea of the paper to be conceptually straightforward and an appealing way to use the power of sequence models in an association testing framework.<br /> - The findings are largely biologically interpretable, and it seems like this could be a promising approach to boost power for some downstream applications.

Weaknesses:<br /> - The methods used to generate polygenic scores were difficult to follow. In particular, a fully connected neural network with linear activations predicting a single output should be equivalent to linear regression (all intermediate layers of the network can be collapsed using matrix-multiplication, so the output is just the inner product of the input with some vector). Using the last hidden layer of such a network for downstream tasks should also be equivalent to projecting the input down to a lower dimensional space with some essentially randomly chosen projection. As such, I am surprised that the neural network approach performs so well, and it would be nice if the authors could compare it to other linear approaches (e.g., LASSO or ridge regression for prediction; PCA or an auto-encoder for converting the input to a lower dimensional representation).

- A very interesting point of the paper was the low R^2 between the HFS scores in adjacent windows, but the explanation of this was unclear to me. Since the HFS scores are just deterministic functions of the SNPs, it feels like if the SNPs are in LD then the HFS scores should be and vice versa. It would be nice to compare the LD between adjacent windows to the average LD of pairs of SNPs from the two windows to see if this is driven by the fact that SNPs are being separated into windows, or if sei is somehow upweighting the importance of SNPs that are less linked to other SNPs (e.g., rare variants).

- There were also a number of robustness checks that would have been good to include in the paper. For instance, do the findings change if the windows are shifted? Do the findings change if the sequence is reverse-complemented?

- It was also difficult to contextualize the present work in terms of recent results showing that sequence models tend to not do very well at predicting cross-individual expression changes (and such results presumably hold for predicting cross-individual chromatin changes). In particular, it would be good for the authors to contrast their findings with the work of Alex Sasse and colleagues (https://www.biorxiv.org/content/10.1101/2023.03.16.532969.abstract) and Connie Huang and colleagues (https://www.biorxiv.org/content/10.1101/2023.06.30.547100.abstract).

Reviewer #2 (Public Review):

Summary:<br /> In this work, Song et al. propose a locus-based framework for performing GWAS and related downstream analyses including finemapping and polygenic risk score (PRS) estimation. GWAS are not sufficiently powered to detect phenotype associations with low-frequency variants. To overcome this limitation, the manuscript proposes a method to aggregate variant impacts on chromatin and transcription across a 4096 base pair (bp) loci in the form of a haplotype function score (HFS). At each locus, an association is computed between the HFS and trait. Computing associations at the level of imputed functional genomic scores should enable the integration of information across variants spanning the allele frequency spectrum and bolster the power of GWAS.

The HFS for each locus is derived from a sequence-based predictive model. Sei. Sei predicts 21,907 chromatin and TF binding tracks, which can be projected onto 40 pre-defined sequence classes ( representing promoters, enhancers, etc.). For each 4096 bp haplotype in their UKB cohort, the proposed method uses the Sei sequence class scores to derive the haplotype function score (HFS). The authors apply their method to 14 polygenic traits, identifying ~16,500 HFS-trait associations. They finemap these trait-associated loci with SuSie, as well as perform target gene/pathway discovery and PRS estimation.

Strengths:<br /> Sequence-based deep learning predictors of chromatin status and TF binding have become increasingly accurate over the past few years. Imputing aggregated variant impact using Sei, and then performing an HFS-trait association is, therefore, an interesting approach to bolster power in GWAS discovery. The manuscript demonstrates that associations can be identified at the level of an aggregated functional score. The finemapping and pathway identification analyses suggest that HFS-based associations identify relevant causal pathways and genes from an association study. Identifying associations at the level of functional genomics increases the portability of PRSs across populations. Imputing functional genomic predictions using a sequence-based deep learning model does not suffer from the limitation of TWAS where gene expression is imputed from a limited-size reference panel such as GTEx.

However, there are several major limitations that need to be addressed.

Major concerns/weaknesses:<br /> 1. There is limited characterization of the locus-level associations to SNP-level associations. How does the set of HFS-based associations differ from SNP-level associations?

2. A clear advantage of performing HFS-trait associations is that the HFS score is imputed by considering variants across the allele frequency spectrum. However, no evidence is provided demonstrating that rare variants contribute to associations derived by the model. Similarly, do the authors find evidence that allelic heterogeneity is leveraged by the HFS-based association model? It would be useful to do simulations here to characterize the model behavior in the presence of trait-associated rare variants.

3. Sei predicts chromatin status / ChIP-seq peaks in the center of a 4kb region. It would therefore be more relevant to predict HFS using overlapping sequence windows that tile the genome as opposed to using non-overlapping windows for computing HFS scores. Specifically, in line 482, the authors state that "the HFS score represents overall activity of the entire sequence, not only the few bp at the center", but this would not hold given that Sei is predicting activity at the center for any sequence.

4. Is the HFS-based association going to miss coding variation and several regulatory variants such as splicing variants? There are also going to be cases where there's an association driven by a variant that is correlated with a Sei prediction in a neighboring window. These would represent false positives for the method, it would be useful to identify or characterize these cases.

Additional minor concerns:<br /> 1. It's not clear whether SuSie-based finemapping is appropriate at the locus level, when there is limited LD between neighboring HFS bins. How does the choice of the number of causal loci and the size of the segment being finemapped affect the results and is SuSie a good fit in this scenario?

2. It is not clear how a single score is chosen from the 117 values predicted by Sei for each locus. SuSie is run assuming a single causal signal per locus, an assumption which may not hold at ~4kb resolution (several classes could be associated with the trait of interest). It's not clear whether SuSie, run in this parameter setting, is a good choice for variable selection here.

3.. A single HFS score is being chosen from amongst multiple tracks at each locus independently. Does this require additional multiple-hypothesis correction?

4. The results show that a larger number of loci are identified with HFS-based finemapping & that causal loci are enriched for causal SNPs. However, it is not clear how the number of causal loci should relate to the number of SNPs. It would be really nice to see examples of cases where a previously unresolved association is resolved when using HFS-based GWAS + finemapping.

5. Sequence-based deep learning model predictions can be miscalibrated for insertions and deletions (INDELs) as compared to SNPs. Scaling INDEL predictions would likely improve the downstream modeling.

Reviewer #1 (Public Review):

Summary:<br /> Shakhawat et al., investigated how enhancement of plasticity and impairment could result in the same behavioral phenotype. The authors tested the hypothesis that learning impairments result from saturation of plasticity mechanisms and had previously tested this hypothesis using mice lacking two class I major histocompatibility molecules. The current study extends this work by testing the saturation hypothesis in a Purkinje-cell (L7) specific Fmr1 knockout mouse mice, which have enhanced parallel fiber-Purkinje cell LTD. The authors found that L7-Fmr1 knockout mice are impaired on an oculomotor learning task and both pre-training, to reverse LTD, and diazepam, to suppress neural activity, eliminated the deficit when compared to controls.

Strengths:

This study tests the "saturation hypothesis" to understand plasticity in learning using a well-known behavior task, VOR, and an additional genetic mouse line with a cerebellar cell-specific target, L7-Fmr1 KO. This hypothesis is of interest to the community as it evokes a novel inquisition into LTD that has not been examined previously.

Utilizing a cell-specific mouse line that has been previously used as a genetic model to study Fragile X syndrome is a unique way to study the role of Purkinje cells and the Fmr1 gene. This increases the understanding in the field in regards to Fragile X syndrome and LTD.

The VOR task is a classic behavior task that is well understood, therefore using this metric is very reliable for testing new animal models and treatment strategies. The effects of pretraining are clearly robust and this analysis technique could be applied across different behavior data sets.

The rescue shown using diazepam is very interesting as this is a therapeutic that could be used in clinical populations as it is already approved.

There was a proper use of controls and all animal information was described. The statistical analysis and figures are clear and well describe the results.

Weaknesses:<br /> While the proposed hypothesis is tested using genetic animal models and the VOR task, LTD itself is not measured. This study would have benefited from a direct analysis of LTD in the cerebellar cortex in the proposed circuits.

Diazepam was shown to rescue learning in L7-Fmr1 KO mice, but this drug is a benzodiazepine and can cause a physical dependence. While the concentrations used in this study were quite low and animals were dosed acutely, potential side-effects of the drug were not examined, including any possible withdrawal. This drug is not specific to Purkinje cells or cerebellar circuits, so the action of the drug on cerebellar circuitry is not well understood for the study presented.

It was not mentioned if L7-Fmr1 KO mice have behavior impairments that worsen with age or if Purkinje cells and the cerebellar microcircuit are intact throughout the lifespan. Connections between Purkinje cells and interneurons could also influence the behavior results found.

While males and females were both used for the current study, only 7 of each sex were analyzed, which could be underpowered. While it might be justified to combine sexes for this particular study, it would be worth understanding this model in more detail.

Training was only shown up to 30 minutes and learning did not seem to plateau in most cases. What would happen if training continued beyond the 30 minutes? Would L7-Fmr1 KO mice catch-up to WT littermates?

The pathway discussed as the main focus for VOR in this learning paradigm was connections between parallel fibers (PF) and Purkinje cells, but the possibility of other local or downstream circuitry being involved was not discussed. PF-Purkinje cell circuits were not directly analyzed, which makes this claim difficult to assess.

The authors mostly achieved their aim and the results support their conclusion and proposed hypothesis. This work will be impactful on the field as it uses a new Purkinje-cell specific mouse model to study a classic cerebellar task. The use of diazepam could be further analyzed in other genetic models of neurodevelopmental disorders to understand if effects on LTD can rescue other pathways and behavior outcomes.

Reviewer #2 (Public Review):

This manuscript explores the seemingly paradoxical observation that enhanced synaptic plasticity impairs (rather than enhances) certain forms of learning and memory. The central hypothesis is that such impairments arise due to saturation of synaptic plasticity, such that the synaptic plasticity required for learning can no longer be induced. A prior study provided evidence for this hypothesis using transgenic mice that lack major histocompatibility class 1 molecules and show enhanced long-term depression (LTD) at synapses between granule cells and Purkinje cells of the cerebellum. The study found that a form of LTD-dependent motor learning-increasing the gain of the vestibulo-ocular reflex (VOR)-is impaired in these mice and can be rescued by manipulations designed to "unsaturate" LTD. The present study extends this line of investigation to another transgenic mouse line with enhanced LTD, namely, mice with the Fragile X gene knocked out. The main findings are that VOR gain increased learning is selectively impaired in these mice but can be rescued by specific manipulations of visuomotor experience known to reverse cerebellar LTD. Additionally, the authors show that a transient global enhancement of neuronal inhibition also selectively rescues gain increases learning. This latter finding has potential clinical relevance since the drug used to boost inhibition, diazepam, is FDA-approved and commonly used in the clinic. The evidence provided for the saturation is somewhat indirect because directly measuring synaptic strength in vivo is technically difficult. Nevertheless, the experimental results are solid. In particular, the specificity of the effects to forms of plasticity previously shown to require LTD is remarkable. The authors should consider including a brief discussion of some of the important untested assumptions of the saturation hypothesis, including the requirement that cerebellar LTD depends not only on pre- and postsynaptic activity (as is typically assumed) but also on the prior history of synaptic activation.

Reviewer #1 (Public Review):

Summary:

Direction selectivity (DS) in the visual system is first observed in the radiating dendrites of starburst amacrine cells (SACs). Studies over the last two decades have aimed to understand the mechanisms that underlie these unique properties. Most recently, a 'space-time' model has garnered special attention. This model is based on two fundamental features of the circuit. First, distinct anatomical types of bipolar cells (BCs) are connected to proximal/distal regions of each of the SAC dendritic sectors (Kim et al., 2014). Second, that input across the length of the starburst is kinetically diverse, a hypothesis that has only recently gained some experimental support using iGluSnFR imaging (Srivastava et al., 2022). However, in these prior studies, the sustained/transient distinctions in BC input that are proposed to underlie direction selectivity were shown to be present mainly in responses to stationary stimuli. When BC receptive field properties are probed using white noise stimuli, the kinetic differences between proximal/distal BC input are relatively subtle or nonexistent (Gaynes et al., 2022; Strauss et al., 2022, Srivastava et al., 2022). Thus, if and how BCs contribute to direction selectivity driven by moving spots that are commonly used to probe the circuit remains to be clarified. To address this issue, Gaynes et al., combine evolutionary computational modeling (Ankri et al., 2020) with two-photon iGluSnFR imaging to address to what degree BCs contribute to the generation of direction selectivity in the starburst dendrites.

Strengths:

Combining theoretical models and iGluSnFR imaging is a powerful approach as it first provides a basic intuition on what is required for the generation of robust DS, and then tests the extent to which the experimentally measured BC output meets these requirements.

The conclusion of this study builds on the previous literature and comprehensively considers the diverse BC receptive field properties that may contribute to DS (e.g. size, lag, rise time, decay time).

By 'evolving' bipolar inputs to produce robust DS in a model network, these authors provide a sound framework for understanding which kinetic properties could potentially be important for driving downstream DS. They suggest that response delay/decay kinetics, rather than the center/surround dynamics are likely to be most relevant (albeit the latter could generate asymmetric responses to radiating/looming stimuli).

Weaknesses:

Finally, these authors report that the experimentally measured BC responses are far from optimal for generating DS. Thus, the BC-based DS mechanism does not appear to explain the robust DS observed experimentally (even with mutual inhibition blocked). Nevertheless, I feel the comprehensive description of BC kinetics and the solid assessment of the extent to which they may shape DS in SAC dendrites, is a significant advancement in the field.

Reviewer #2 (Public Review):

Summary:

In this study, the authors sought to understand how the receptive fields of bipolar cells contribute to direction selectivity in starburst amacrine cell (SAC) dendrites, their post synaptic partners. In previous literature, this contribution is primarily conceptualized as the 'space-time wiring model', whereby bipolar cells with slow-release kinetics synapse onto proximal dendrites while bipolar cells with faster kinetics synapse more distally, leading to maximal summation of the slow proximal and fast distal depolarizations in response to motion away from the soma. The space-time wiring contribution to SAC direction selectivity has been extensively tested in previous literature using connectomic, functional, and modeling approaches. However, the authors argue that previous functional studies of bipolar cell kinetics have focused on static stimuli, which may not accurately represent the spatiotemporal properties of the bipolar cell receptive field in response to movement. Moreover, this group and others have recently shown that bipolar cell signal processing can change directionally when visual stimuli starts within the receptive field rather than passing through it, complicating the interpretation of moving stimuli that start within a bipolar cell of interest's receptive field (e.g. stimulating only one branch of a SAC or expanding/contracting rings). Thus, the authors choose to focus on modeling and functionally mapping bipolar cell kinetics in response to moving stimuli across the entire SAC dendritic field.

General Comments:

There have been several studies that have addressed the contribution of space-time wiring to SAC process direction selectivity. This study offers a more complete assessment of potential impact space-time wiring can have on this dendrite computation. The experimental results based on glutamate imaging assess the kinetics of glutamate release under conditions of visual stimulation across a large region of retina largely confirm previous observations. By combining their model with this experiment data, they conclude that even the optimal space-time wiring is not sufficient to explain the SAC process DS. Though there is no conclusion which of the many other proposed cellular and circuit mechanisms could potentially contribute to this computation, the limited role for spacetime wiring is firmly established.

Reviewer #3 (Public Review):

Summary:

Gaynes et al. investigated the presynaptic and postsynaptic mechanisms of starburst amacrine cell (SAC) direction selectivity in the mouse retina by computational modeling and glutamate sensitivity (iGluSnFR) imaging methods. Using the SAC computational simulation, the authors initially tested bipolar cell contributions (space-time wiring model, presynaptic effect) and SAC axial resistance contributions (postsynaptic effect) to the SAC DS. Then, the authors conducted two-photon iGluSnFR imaging from SACs to examine the presynaptic glutamate release and found seven clusters of ON-responding and six clusters of OFF-responding bipolar cells. They were categorized based on their response kinetics: delay, onset phase, decay time, and others. Finally, the authors used cluster data to reconstruct bipolar cell inputs to SACs that generate direction selectivity. They concluded that presynaptic effects through the space-time wiring model only account for a fraction of SAC DS.

The article has many interesting findings, and the data presentation is superb. Strengths and weaknesses are summarized below.

Major Strengths:

The authors utilized solid technology to conduct computational modeling with Neuron software and a machine-learning approach based on evolutionary algorithms. Results are effectively and thoroughly presented.

The space-time wiring model was evaluated by changing bipolar cell response properties in the proximal and distal SAC dendrites. Many response parameters in bipolar cells are compared, and DSI is compared in Figure 3. These parameter comparisons are valuable to the field.

Two-photon microscopy was used to measure the bipolar cell glutamate outputs onto SACs by conducting iGluSnFR imaging. All the data sets, including images and transients, are elegantly presented. The authors analyzed the response based on various parameters, which generated more than several response clusters. The clustering is convincing.

Major Weaknesses:

The computational modeling demonstrates intriguing results: SAC dendritic morphology produces dendritic isolation, and a massive input overcomes the dendritic isolation (Figure 1). This modeling seems to be generated by basic dendritic cable properties. However, it has been reported that SAC dendrites express Kv3 and voltage-gated Ca channels. Are they incorporated into this model? If not, how about comparing these channel contributions?

In Figure 9 the authors generated the bipolar cell cluster alignment based on the space-time wiring model. The space-time wiring model has been proposed based on the EM study that distinct types of bipolar cells synapse on distinct parts of SAC dendrites (Green et al 2016, Kim et al 2014). While this is one of the representative Reicardt models, it is not fully agreed upon in the field (see Stincic et al 2016). Therefore, the authors' approach might be only hypothetical without concrete evidence for geographical cluster distributions. Is there any data suggesting each cluster's location on the SAC dendrites? I assume that the iGluSnFR imaging was conducted on the SAC dendritic network, which does not provide geographical information. How about injecting the iGluSnFR-AAV at a lower titer, which labels only some SACs in a tissue? This method may reveal each cluster's location on SAC dendrites.

The authors found that there are seven ON clusters and six OFF clusters, which are supposed to be bipolar cell terminals. However, bipolar cells reported to provide synaptic inputs are T-7, T-6, and multiple T-5s for ON SACs and T-1, T-2, and T-3s for OFF SACs. The number of types is less than the number of clusters. Is there a possibility of clusters belonging to glutamatergic amacrine cells? Please provide a discussion regarding the relations between clusters and cell types.

In Figure 5B, representative traces are shown responding to moving bars in horizontal directions. These did not show different responses to two directional stimuli. Is there any directional preference from other ROIs? Yonehara's group recently exhibited the bipolar cells' direction selectivity (Matsumoto et al 2021). Did you see any correlations with their results? Please discuss.

Reviewer #1 (Public Review):

Summary: The authors set out to clarify the molecular mechanism of endocytosis (re-uptake) of synaptic vesicle (SV) membrane in the presynaptic terminal following release. They have examined the role of presynaptic actin, and of the actin regulatory proteins diaphanous-related formins ( mDia1/3), and Rho and Rac GTPases in controlling the endocytosis. They successfully show that presynaptic membrane-associated actin is required for normal SV endocytosis in the presynaptic terminal and that the rate of endocytosis is increased by activation of mDia1/3. They show that RhoA activity and Rac1 activity act in a partially redundant and synergistic fashion together with mDia1/3 to regulate the rate of SV endocytosis. The work adds substantially to our understanding of the molecular mechanisms of SV endocytosis in the presynaptic terminal.

Strengths: The authors use state-of-the-art optical recording of presynaptic endocytosis in primary hippocampal neurons, combined with well-executed genetic and pharmacological perturbations to document effects of alteration of actin polymerization on the rate of SV endocytosis. They show that removal of the short amino-terminal portion of mDia1 that associates with the membrane interrupts the association of mDia1 with membrane actin in the presynaptic terminal. They then use a wide variety of controlled perturbations, including genetic modification of the amount of mDia1/3 by knock-down and knockout, combined with inhibition of activity of RhoA and Rac1 by pharmacological agents, to document the quantitative importance of each agent and their synergistic relationship in regulation of endocytosis.<br /> The analysis is augmented by ultrastructural analyses that demonstrate the quantitative changes in numbers of synaptic vesicles and in uncoated membrane invaginations that are predicted by the optical recordings.<br /> The manuscript is well-written and the data are clearly explained. Statistical analysis of the data is strengthened by the very large number of data points analyzed for each experiment.

Weaknesses: There are no major weaknesses. The optical images as first presented are small and it is recommended that the authors provide larger, higher-resolution images.

Reviewer #2 (Public Review):

Summary:<br /> This manuscript expands on previous work from the Haucke group which demonstrated the role of formins in synaptic vesicle endocytosis. The techniques used to address the research question are state-of-the-art. As stated above there is a significant advance in knowledge, with particular respect to Rho/Rac signalling.

Strengths:<br /> The major strength of the work was to reveal new information regarding the control of both presynaptic actin dynamics and synaptic vesicle endocytosis via Rho/Rac cascades. In addition, there was further mechanistic insight regarding the specific function of mDia1/3. The methods used were state-of-the-art.

Weaknesses:<br /> There are a number of instances where the conclusions drawn are not supported by the submitted data, or further work is required to confirm these conclusions.

Reviewer #1 (Public Review):

Summary:<br /> O'Leary and colleagues present data identifying several procedures that alter discrimination between novel and familiar objects, including time, environmental enrichment, Rac-1, context reexposure, and brief reminders of the familiar object. This is complimented with an engram approach to quantify cells that are active during learning to examine how their activation is impacted following each of the above procedures at test. With this behavioral data, authors apply a modeling approach to understand the factors that contribute to good and poor object memory recall.

Strengths:<br /> • Authors systematically test several factors that contribute to poor discrimination between novel and familiar objects. These results are extremely interesting and outline essential boundaries of incidental, nonaversive memory.<br /> • These results are further supported by engram-focused approaches to examine engram cells that are reactivated in states with poor and good object recognition recall.

Weaknesses:<br /> • For the environmental enrichment, authors seem to suggest objects in the homecage are similar to (or reminiscent of) the familiar object. Thus, the effect of improved memory may not be related to enrichment per se as much as it may be related to the preservation of an object's memory through multiple retrievals, not the enriching experiences of the environment itself. This would be consistent with the brief retrieval figure. Authors should include a more thorough discussion of this.

• Authors should justify the marginally increased number of engram cells in the non-enrichment group that did not show object discrimination at test, especially relative to other figures. More specific cell counting criteria may be helpful for this. For example, was the DG region counted for engram and cfos cells or only a subsection?

• It is unclear why the authors chose a reactivation time point of 1hr prior to testing. While this may be outside of the effective time window for pharmacological interference with reconsolidation for most compounds, it is not necessarily outside of the structural and functional neuronal changes accompanied by reconsolidation-related manipulations.

• Figure 5: Levels of exploration at test are inconsistent between manipulations. This is problematic, as context-only reexposures seem to increase exploration for objects overall in a manner that I'm unsure resembles 'forgetting'. Instead, cross-group comparisons would likely reveal increased exploration time for familiar and novel objects. While I understand 'forgetting' may be accompanied by greater exploration towards objects, this is inconsistent across and within the same figure. Further, this effect is within the period of time that rodents should show intact recognition. Instead, context-only exposures may form a competing (empty context) memory for the familiar object in that particular context.

• I am concerned at the interpretation that a memory is 'forgotten' across figures, especially considering the brief reminder experiments. Typically, if a reminder session can trigger the original memory or there is rapid reacquisition, then this implies there is some savings for the original content of the memory. For instance, multiple context retrievals in the absence of an object reminder may be more consistent with procedures that create a distinct memory and subsequently recruit a distinct engram.

• Authors state that spine density decreases over time. While that may be generally true, there is no evidence that mature mushroom spines are altered or that this is consistent across figures. Additionally, it's unclear if spine volume is consistently reduced in reactivated and non-reactivated engram cells across groups. This would provide evidence that there is a functionally distinct aspect of engram cells that is altered consistently in procedures resulting in poor recognition memory (e.g. increased spine density relative to spine density of non-reactivated engram cells and non-engram cells)

• Authors should discuss how the enrichment-neurogenesis results here are compatible with other neurogenesis work that supports forgetting.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript examines an important question about how an inaccessible, natural forgotten memory can be retrieved through engram ensemble reactivation. It uses a variety of strategies including optogenetics, behavioral and pharmacological interventions to modulate engram accessibility. The data characterize the time course of natural forgetting using an object recognition task, in which animals can retrieve 1 day and 1 week after learning, but not 2 weeks later. Forgetting is correlated with lower levels of cell reactivation (c-fos expression during learning compared to retrieval) and reduction in spine density and volume in the engram cells. Artificial activation of the original engram was sufficient to induce recall of the forgotten object memory while artificial inhibition of the engram cells precluded memory retrieval. Mice housed in an enriched environment had a slower rate of forgetting, and a brief reminder before the retrieval session promoted retrieval of a forgotten memory. Repeated reintroduction to the training context in the absence of objects accelerated forgetting. Additionally, activation of Rac1-mediated plasticity mechanisms enhanced forgetting, while its inhibition prolonged memory retrieval. The authors also reproduce the behavioral findings using a computational model inspired by Rescorla-Wagner model. In essence, the model proposes that forgetting is a form of adaptive learning that can be updated based on prediction error rules in which engram relevancy is altered in response to environmental feedback.

Strengths:<br /> 1) The data presented in the current paper are consistent with the authors claim that seemingly forgotten engrams sometimes remain accessible. This suggests that retrieval deficits can lead to memory impairments rather than a loss of the original engram (at least in some cases).

2) The experimental procedures and statistics are appropriate, and the behavioral effects appear to be very robust. Several key effects are replicated multiple times in the manuscript.

Weaknesses:<br /> 1) My major issue with the paper is the forgetting model proposed in Figure 7. Prior work has shown that neutral stimuli become associated in a manner similar to conditioned and unconditioned stimuli. As a result, the Rescorla-Wagner model can be used to describe this learning (Todd & Homes, 2022). In the current experiments, the neutral context will become associated with the unpredicted objects during training (due to a positive prediction error). Consequently, the context will activate a memory for the objects during the test, which should facilitate performance. Conversely, any manipulation that degrades the association between the context and object should disrupt performance. An example of this can be found in Figure 5A. Exposing the mice to the context in the absence of the objects should violate their expectations and create a negative prediction error. According to the Rescorla-Wagner model, this error will create an inhibitory association between the context and the objects, which should make it harder for the former to activate a memory of the latter (Rescorla & Wagner, 1972). As a result, performance should be impaired, and this is what the authors find. However, if the cells encoding the context and objects were inhibited during the context-alone sessions (Figure 5D) then no prediction error should occur, and inhibitory associations would not be formed. As a result, performance should be intact, which is what the authors observe.

What about forgetting of the objects that occurs over time? Bouton and others have demonstrated that retrieval failure is often due to contextual changes that occur with the passage of time (Bouton, 1993; Rosas & Bouton, 1997, Bouton, Nelson & Rosas, 1999). That is, both internal (e.g. state of the animal) and external (e.g. testing room, chambers, experimenter) contextual cues change over time. This shift makes it difficult for the context to activate memories with which it was once associated (in the current paper, objects). To overcome this deficit, one can simply re-expose animals to the original context, which facilitates memory retrieval (Bouton, 1993). In Figure 2D, the authors do something similar. They activate the engram cells encoding the original context and objects, which enhances retrieval.

Therefore, the forgetting effects presented in the current paper can be explained by changes in the context and the associations it has formed with the objects (excitatory or inhibitory). The results are perfectly predicted by the Rescorla-Wagner model and the context-change findings of Bouton and others. As a result, the authors do not need to propose the existence of a new "forgetting" variable that is driven by negative prediction errors. This does not add anything novel to the paper as it is not necessary to explain the data (Figures 7 and 8).

2) I also have an issue with the conclusions drawn from the enriched environment experiment (Figure 3). The authors hypothesize that this manipulation alleviates forgetting because "Experiencing extra toys and objects during environmental enrichment that are reminiscent of the previously learned familiar object might help maintain or nudge mice to infer a higher engram relevancy that is more robust against forgetting.". This statement is completely speculative. A much simpler explanation (based on the existing literature) is that enrichment enhances synaptic plasticity, spine growth, etc., which in turn reduces forgetting. If the authors want to make their claim, then they need to test it experimentally. For example, the enriched environment could be filled with objects that are similar or dissimilar to those used in the memory experiments. If their hypothesis is correct, only the similar condition should prevent forgetting.

3) It is well-known that updating can both weaken or strengthen memory. The authors suggest that memory is updated when animals are exposed to the context in the absence of the objects. If the engram is artificially inhibited (opto) during context-only re-exposures, memory cannot be updated. To further support this updating idea, it would be good to run experiments that investigate whether multiple short re-exposures to the training context (in the presence of the objects or during optogenetic activation of the engram) could prevent forgetting. It would also be good to know the levels of neuronal reactivation during multiple re-exposures to the context in the absence versus context in the presence of the objects.

4) There are a number of studies that show boundary conditions for memory destabilization/reconsolidation. Is there any evidence that similar boundary conditions exist to make an inaccessible engram accessible?

5) More details about how the quantification of immunohistochemistry (c-fos, BrdU, DAPI) was performed should be provided (which software and parameters were used to consider a fos positive neurons, for example).

6) Duration of the enrichment environment was not detailed.

Reviewer #3 (Public Review):

Summary: The manuscript by Ryan and colleagues uses a well-established object recognition task to examine memory retrieval and forgetting. They show that memory retrieval requires activation of the acquisition engram in the dentate gyrus and failure to do so leads to forgetting. Using a variety of clever behavioural methods, the authors show that memories can be maintained and retrieval slowed when animals are reared in environmental enrichment and that normally retrieved memories can be forgotten if exposed to the environment in which the expected objects are no longer presented. Using a series of neural methods, the authors also show that activation or inhibition of the acquisition engram is key to memory expression and that forgetting is due to Rac1.

Strengths:<br /> This is an exemplary examination of different conditions that affect successful retrieval vs forgetting of object memory. Furthermore, the computational modelling that captures in a formal way how certain parameters may influence memory provides an important and testable approach to understanding forgetting.<br /> The use of the Rescorla-Wagner model in the context of object recognition and the idea of relevance being captured in negative prediction error are novel (but see below).<br /> The use of gain and loss of function approaches are a considerable strength and the dissociable effects on behaviour eliminate the possibility of extraneous variables such as light artifacts as potential explanations for the effects.

Weaknesses:<br /> Knowing what process (object retrieval vs familiarity) governed the behavioural effect in the present investigation would have been of even greater significance.

The impact of the paper is somewhat limited by the use of only one sex.

While relevance is an interesting concept that has been operationalized in the paper, it is unclear how distinct it is from extinction. Specifically, in the case where the animals are exposed to the context in the absence of the object, the paper currently expresses this as a process of relevance - the objects are no longer relevant in that context. Another way to think about this is in terms of extinction - the association between the context and the objects is reduced results in a disrupted ability of the context to activate the object engram.

Reviewer #1 (Public Review):

This manuscript provides an important case study for in-depth research on the adaptability of vertebrates in deep-sea environments. Through analysis of the genomic data of the hadal snailfish, the authors found that this species may have entered and fully adapted to extreme environments only in the last few million years. Additionally, the study revealed the adaptive features of hadal snailfish in terms of perceptions, circadian rhythms and metabolisms, and the role of ferritin in high-hydrostatic pressure adaptation. Besides, the reads mapping method used to identify events such as gene loss and duplication avoids false positives caused by genome assembly and annotation. This ensures the reliability of the results presented in this manuscript. Overall, these findings provide important clues for a better understanding of deep-sea ecosystems and vertebrate evolution.

Reviewer #2 (Public Review):

This paper presents improved, chromosome level assemblies of the hadal snailfish and Tanaka's snailfish. This is an extension and update of previous work from the group on the hadal snailfish genome. The chromosomal assemblies allow comparisons of genome architecture between a shallow water snailfish and the hadal snailfish to aid inference on timing of colonization of trenches and genomic changes that may have been adaptive for that move.

The comparisons in genomic architecture are compelling: genes present in Tanaka's snailfish that are lost in hadal snailfish that involve whole regions of the genome that no longer map even though adjacent regions do map between the species and across a large evolutionary distance to stickleback. Or genes that are duplicated in hadal snailfish but only appear as single copy in other fishes. The paper focuses on genes in the eye, in hearing, in circadian rythms, and in ROS scavaging. These are all functions that could play a role in adapting to the hadal environment.

The genomic comparisons all seem sound. Stylistically I would prefer if the authors could introduce the gene product and protein function every time they introduce a gene locus. They introduce a gene and general function, but don't usually note what the protein encoded by the gene is and what it's specific function is.

I found the paper generally well written, and the data compelling and creatively displayed.

Upon revision, the authors have commendably addressed all reviewer comments and added a slew of additional analyses. I find the paper stronger, better argued and have no further questions or comments.

Reviewer #1 (Public Review):

Summary:<br /> This valuable study analyzes the contribution of fungal and bacterial microbiota species to the growth and development of Drosophila. The authors use bacterial and fungal species associated with Drosophila in the wild to analyze their respective contributions in promoting larval growth in a decaying banana, mimicking the natural niche of fruit fly. They found that some fungal species and some fungus/bacteria combinations effectively promote growth by supplementing key branched amino acids in the food substratum. Production of these amino acids by Drosophila itself is not sufficient, and only fungal species that secrete these amino acids into the medium can sustain Drosophila growth. Thus, the authors clarify how facultative symbionts contribute to host growth in a natural setting by changing the food substratum in a dynamic manner.

Strengths:<br /> The natural setting developed by the authors to analyze the impact of the microbiota is clearly valuable, as is the focus on the role of fungal microbiota species. This complements studies of Drosophila microbiota that have previously focused on bacterial species and used a lab setting.

While there has been an extensive focus on obligate endosymbionts or gut symbionts, this study analyzes how facultative symbionts shape the food substratum and influence host growth.<br /> A last strength of this study is that it analyzes the contribution of Drosophila microbiota over a dynamic timeframe, analyzing how microbial species change in decaying fruit over time.

Weaknesses:<br /> 1) The author should better review what we know of fungal Drosophila microbiota species as well as the ecology of rotting fruit. Are the microbiota species described in this article specific to their location/setting? It would have been interesting to know if similar species can be retrieved in other locations using other decaying fruits. The term 'core' in the title suggests that these species are generally found associated with Drosophila but this is not demonstrated. The paper is written in a way that implies the microbiota members they have found are universal. What is the evidence for this? Have the fungal species described in this paper been found in other studies? Even if this is not the case, the paper is interesting, but there should be a discussion of how generalizable the findings are.

2) Can the author clearly demonstrate that the microbiota species that develop in the banana trap are derived from flies? Are these species found in flies in the wild? Did the authors check that the flies belong to the D. melanogaster species and not to the sister group D. simulans?

3) Did the microarrays highlight a change in immune genes (ex. antibacterial peptide genes)? Whatever the answer, this would be worth mentioning. The authors described their microarray data in terms of fed/starved in relation to the Finke article. This is fine they should clarify if they observed significant differences between species (differences between species within bacteria or fungi, and more generally differences between bacteria versus fungi).

4) The whole paper - and this is one of its merits - points to a role of the Drosophila larval microbiota in processing the fly food. Are these bacterial and fungal species found in the gut of larvae/adults? Are these species capable of establishing a niche in the cardia of adults as shown recently in by the Ludington lab (Dodge et al.,)? Previous studies have suggested that microbiota members stimulate the Imd pathway leading to an increase in digestive proteases (Erkosar/Leulier). Are the microbiota species studied here affecting gut signaling pathways beyond providing branched amino acids?

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Mure et al investigated host-microbe interactions in wild-mimicked settings. They analyzed microbiome composition using bananas that had been fed on by wild larvae and found that the microbiota composition shifted from the early stage of feeding to the later stage of the fermentation process proceeded. They isolated several yeast and bacterial species from the food, and examined larval growth on banana-based food, mimicking natural setting where germ-free larvae cannot grow on it. The authors found that a yeast, Hanseniaspora uvarum, can support larval growth sufficiently, and insists that branched-chain amino acids (BCAAs) provided by the yeast may partly be accounted for the growth support. Interestingly, other isolated yeast species, some were non-supportive strains in terms of larval growth, can assist larval development when they were heat-killed. Besides, they showed that acetic acid bacteria, isolated from well-fermented banana (later-stage food), is sufficiently supportive but their presence depended on other microbes, lactic acid bacteria or yeast.

Strengths:<br /> So far, host-microbe studies using Drosophila melanogaster have relatively less focused on the roles of fungi and many studies used only "model" yeasts. In the experimental setting where natural conditions may be well mimicked, the authors successfully isolated wild yeast species and convincingly showed that wild yeast plays a critical role in promoting host growth. In addition, the authors provided intriguing observations that all of the heat-killed yeast promoted larval growth even though some of the yeast never support the development when they were alive, suggesting that wild yeasts produce the necessary nutrients for larval development, but the nutrients of non-supportive yeasts are not accessible to the host. This might be an interesting indication for further studies revealing host-fungi interactions.

Weaknesses:<br /> The experimental setting that, the authors think, reflects host-microbe interactions in nature is one of the key points. However, it is not explicitly mentioned whether isolated microbes are indeed colonized in wild larvae of Drosophila melanogaster who eat bananas. Another matter is that this work is rather descriptive. A molecular level explanation is missing in "interspecies interactions" between lactic acid bacteria (or yeast) and acetic acid bacteria that assure their inhabitation.

Reviewer #3 (Public Review):

Summary: In this manuscript, Mure et al. describe interactions between diet, microbiome, and host development using Drosophila as a model. By characterizing microbial communities in food sources and animals, the authors showed that microbial community dynamics in the food source is critical for host development.

Strengths: This is a very interesting study where authors managed to tackle a difficult question in an elegant manner. How the interactions between different microbial species within the microbiome shape host physiology is an area of great interest but equally challenging due to the complexity of intercellular interactions in complex, host-associated microbial communities. By using a simplified model and interrogating not only microbe-microbe and host-microbe interactions, but also the role played by diet, authors were able to identify significant interactions during fly development.

Weaknesses: All weaknesses observed in the original manuscript have been corrected in the current version.

Reviewer #1 (Public Review):

The manuscript investigates the binding of PHD-BD, a tandem of reader domains in the C-terminus of BPTF, to modified histone tail peptides and nucleosomes. It focuses on the differences in binding affinity between peptide and nucleosome substrates for BPTF PHD-BD. Using the dCypher approach, they find that multi-modified peptide substrates (both acetylation and methylation) do not increase PHD-BD binding affinity. They argue that histone peptide substrates do not support the histone code model, which champions that multivalent engagement by PHD-BD with a multi-modified substrate would lead to stronger binding when compared to the engagement of each domain alone. In contrast, when using nucleosome substrates, even though the overall affinity is reduced, the affinity for H3K4me3triac (double modification) is tighter than either modification on its own. This is consistent with the histone code model.

A strength of the manuscript is that it further delineates the contribution of each domain by again using dCypher to compare peptide and nucleosome binding of the PHD and BD domains alone, as well as tandem domain constructs where each domain has been inactivated by a point mutation (W2891A for the PHD and N3007A for the BD). PHD alone had a lower affinity for nucleosomes than peptides overall. With peptide substrates, PHD had the highest affinity for H3K4me3 and reduced affinity for H3K4me3triac; while with nucleosomes this trend was reversed. BD alone showed an affinity for acetylated H3 and H4 peptides but surprisingly was unable to bind nucleosomes. PHD requires the combination of H3K4 methylation and H3 tail acetylation for binding, and when partnered with BD, which is not able to bind nucleosomes alone, interestingly confers specificity for K14ac and K18ac. The in vivo relevance is argued using CUT&RUN analysis.

NMR spectroscopy is further used to show that PHD-BD binds acetylated H3 in a multivalent manner while forming a unique complex with H3K4me3triac. Deleting the N-terminal A1 region of H3 abolishes the binding of PHD-BD, implying its importance for recognition. The authors also discuss a "fuzzy complex" that forms between H3 and DNA, as well as H4 and DNA, which explains the occlusion of histone tail accessibility in the nucleosome. By changing the sidechain charge, such as with PTMs, this interaction can be weakened and allow PHD in this case to bind to the modified H3 tail. Comparisons between spectra of the H4 tail, H4 tail with DNA, and the H4 tail in the nucleosome are made and used to argue for H4-DNA interactions in the nucleosome.

The conclusions of the manuscript are very well-supported by the data and reveal a lot of insight into how the two reader domains of BPTF interact with modified nucleosomes. In many places, however, the manuscript is written more generally as if the conclusions apply in all cases (e.g. the title, abstract, and introduction) and this remains to be determined. It is also overstated that there is a belief that peptides perfectly recapitulate nucleosomes. It should also be pointed out that the nucleosomes are multi-valent and the data cannot discriminate binding of a single PHD-BD to single or multiple tails, and that the work is limited as it is using a construct of BPTF and in fact, there is at least one other reader domain involved.

Reviewer #2 (Public Review):

This manuscript by Musselman and coworkers uses a commercial library of modified histone peptides and mononucleosomes to probe the substrate specificity of the PHD-bromodomain combination of the BPTF protein. They arrive at the conclusion that BPTF preferably binds H3K4me3 and H3K18ac in the H3 tail. By using NMR with lableled H4 protein in nucleosomes they show that the H4 tail interacts with DNA, which may limit its ability to interact with BPTF. Finally, experiments in cells demonstrate that BPTF, H3K4me3, and H3K18ac occupy overlapping regions of chromatin. The authors suggest that recruitment of BPTF to specific regions of chromatin is driven by the co-binding of H3K4me3 and H3K18ac by BPTF. This study is of interest to readers interested in understanding the functions of the BPTF protein in cells.

In this reviewer's opinion, the manuscript needs some revision and the inclusion of some missing information.

1) The authors seem to have overlooked the fact that mononucleosome substrates have been in use for determining the substrate specificity and mechanisms of quite a few enzymes that simply do not act on peptide substrates. For example, Dot1L doesn't do anything with peptides nor does COMPASS/Set1, both of which require intact nucleosomal substrates to measure their activity in response to ubiquitylated H2B. Thus, the authors' refinement of the "histone code hypothesis" is unnecessary and overdone. I would suggest that they instead cite examples where nucleosome substrates have provided answers that cannot be obtained from peptide substrates alone. For example, extensive work from the Muir and Allis labs.

2) Ruthenburg and Allis in Cell 2011 conducted similar experimentation and concluded that H3K4me3-H4K16ac is a modification state bound by BPTF in cells. They also showed co-localization in ChIP-seq experiments and demonstrated preferential pulldowns with BPTF and semisynthetic methylated and acetylated nucleosomes. The authors have entirely ignored these previous results in their own discussions. Readers would benefit from a side-by-side comparison of the two acetylation states to get a sense of which is a stronger interaction and why both seemingly correlate in CUTnRUN or ChIP-seq.

3) The idea that electrostatics may modulate tail accessibility was reported by Musselman and coworkers for the H3 tail in eLife 2018. Yet the PHD domain of BPTF clearly binds H3K4me3 in nucleosomes. In light of this prior observation, the NMR experiments now with H4 tail seem repetitive and not informative regarding BPTF's bromodomain binding. Also, missing is the effect of H4K16acetylation on H4 tail dynamics, which would be pertinent to addressing the hypothesis regarding the BPTF bromodomain binding H4K16ac

4) The NMR experiments are all undertaken with 150mM KCl with no NaCl present. While NMR experimental constraints are understandable, the authors should avoid sweeping statements from NMR experiments regarding the dynamism of histone tails in chromatin, unless specific experiments are cited/conducted to demonstrate the same in cells. Many factors may contribute to the exclusion of BPTF from modified histone tails in cells, including the binding of other reader proteins, and the precise genomic localization of these modifications vis-a-vis BPTF. The important role of anchoring proteins must also be taken into account when considering binding/non-binding of substrates by CAPs. Thus, the NMR experiments presented in the manuscript do not report on whether BPTF binds H4K16ac in cells or indeed in vitro. If the PHD domain is capable of ultimately binding the H3 tail despite the tail's fuzzy interaction with DNA, the question remains as to why the bromodomain may not do so for acetylated H4 tails?

This manuscript reports several interesting elements regarding BPTF regulation, but as presented it is missing some key comparisons with prior information that makes it hard for readers to assess the relevance of the results presented.

Reviewer #1 (Public Review):

This paper combines an array of techniques to study the role of cholecystokinin (CCK) in motor learning. Motor learning in a pellet reaching task is shown to depend on CCK, as both global and locally targeted CCK manipulations eliminate learning. This learning deficit is linked to reduced plasticity in the motor cortex, evidenced by both slice recordings and two-photon calcium imaging. Furthermore, CCK receptor agonists are shown to rescue motor cortex plasticity and learning in knockout mice. While the behavioral results are clear, the specific effects on learning are not directly tested, nor is the specificity pathway between rhinal CCK neurons and the motor cortex. In general, the results present interesting clues about the role of CCK in motor learning, though the specificity of the claims is not fully supported.

Since all CCK manipulations were performed throughout learning, rather than after learning, it is not clear whether it is learning that is affected or if there is a more general motor deficit. Related to this point, Figure 1D appears to show a general reduction in reach distance in CCK-/- mice. A general motor deficit may be expected to produce decreased success on training day 1, which does not appear to be the case in Figure 1C and Figure 2B, but may be present to some degree in Figure 5B. Or, since the task is so difficult on day 1, a general motor deficit may not be observable. It is therefore inconclusive whether the behavioral effect is learning-specific.

The paper implicates motor cortex-projecting CCK neurons in the rhinal cortex as being a key component in motor learning. However, the relative importance of this pathway in motor learning is not pinned down. The necessity of CCK in the motor cortex is tested by injecting CCK receptor antagonists into the contralateral motor cortex (Figure 2), though a control brain region is not tested (e.g. the ipsilateral motor cortex), so the specificity of the motor cortex is not demonstrated. The learning-related source of CCK in the motor cortex is also unclear, since even though it is demonstrated that CCK neurons in the rhinal cortex project to the motor cortex in Figure 4D, Figure 4C shows that there is also a high concentration of CCK neurons locally within the motor cortex. Likewise, the importance of the projection from the rhinal cortex to the motor cortex is not specifically tested, as rhinal CCK neurons targeted for inactivation in Figure 5 include all CCK cells rather than motor cortex-projecting cells specifically.

CCK is suggested to play a role in producing reliable activity in the motor cortex through learning through two-photon imaging experiments. This is useful in demonstrating what looks like normal motor cortex activity in the presence of CCK receptor antagonist, indicating that the manipulations in Figure 2 are not merely shutting off the motor cortex. It is also notable that, as the paper points out, the activity appears less variable in the CCK manipulations (Figure 3G). However, this could be due to CCK manipulation mice having less-variable movements throughout training. The Hausdorff distance is used for quantification against this point in Figure 1E, though the use of the single largest distance between trajectories seems unlikely to give a robust measure of trajectory similarity, which is reinforced by the CCK-/- traces looking much less variable than WT traces in Figure 1D. The activity effects may therefore be expected from a general motor deficit if that deficit prevented the mice from normal exploratory movements and restricted the movement (and activity) to a consistently unsuccessful pattern.

Finally, slice experiments are used to demonstrate the lack of LTP in the motor cortex following CCK knockout, which is rescued by CCK receptor agonists. This is a nice experiment with a clear result, though it is unclear why there are such striking short-term depression effects from high-frequency stimulation observed in Figure 6A that are not observed in Figure 1H. Also, relating to the specificity of the proposed rhinal-motor pathway, these experiments do not demonstrate the source of CCK in the motor cortex, which may for example originate locally.

Reviewer #2 (Public Review):

This study aims to test whether and if so, how cholecystokinin (CCK) from the mice rhinal cortex influences neural activity in the motor cortex and motor learning behavior. While CCK has been previously shown to be involved in neural plasticity in other brain regions/behavioral contexts, this work is the first to demonstrate its relationship with motor cortical plasticity in the context of motor learning. The anatomical projection from the rhinal cortex to the motor cortex is also a novel and important finding and opens up new opportunities for studying the interactions between the limbic and motor systems. I think the results are convincing to support the claim that CCK and in particular CCK-expressing neurons in the rhinal cortex are critical for learning certain dexterous movements such as single pellet reaching. However, more work needs to be done, or at least the following concerns should be addressed, to support the hypothesis that it is specifically the projection from the rhinal cortex to the motor cortex that controls motor learning ability in mice.

1) Because CCK is expressed in multiple brain regions, as the authors recognized, results from the CCK knock-out mice could be due to a global loss of neural plasticity. In comparison, the antagonist experiment is in my opinion the most convincing result to support the specific effect of CCK in the motor cortex. However, it is unclear to me whether the CCK knock-out mice exhibited an impaired ability to learn in general, i.e., not confined to motor skills. For instance, it would be very valuable to show whether these mice also had severe memory deficits; this would help the field to understand different or similar behavioral effects of CCK in the case of global vs. local loss of function. If the CCK knock-out mice only exhibited motor learning deficits, that would be surprising but also very interesting given previous studies on its effect in other brain areas.

2) Related to my last point, I believe that normal neural plasticity should be essential to motor skill learning throughout development not just during the current task. Thus, it would be important to show whether these CCK knock-out mice present any motor deficits that could have resulted from a lack of CCK-mediated neural plasticity during development. If not, the authors should explain how this normal motor learning during development is consistent with their major hypothesis in this study (e.g., is CCK not critical for motor learning during early development).

3) Lines 198-200 and Fig. 2C: The authors found that the vehicle group showed significantly increased "no grasp" behavior, and reasoned that the implantation of a cannula may have caused injuries to the motor cortex. In order to support their reasoning and make the control results more convincing, I think it would be helpful to show histology from both the antagonist and control groups and demonstrate motor cortical injury in some mice of the vehicle group but not the antagonist group. Otherwise, I'm a bit concerned that the methods used here could be a significant confounding factor contributing to motor deficits.

4) The authors showed that chemogenetic inhibition of CCK neurons in the rhinal cortex impaired motor skill learning in the pellet-reaching task. However, we know that the rhinal cortex projects to multiple brain regions besides the motor cortex (e.g., other cortical areas and the hippocampus). Thus, the conclusion/claim that the observed behavioral deficits resulted from inhibited rhinal-motor cortical projections is not strongly supported without more targeted loss-of-function or rescue experiments.

It would also be very informative to the field to compare the specific behavioral deficits, if any, of inhibiting specific downstream targets of the rhinal CCK neurons. As a concrete example, the hippocampus may be involved in learning more sophisticated motor skills (as the authors pointed out in the Discussion) besides the motor cortex. It would be a critical result if the authors could either show or exclude the possibility that the motor learning deficits observed in CCK-/- mice were at least partially due to the inhibition of hippocampal plasticity. This echoes my earlier point (point 1) that it is unclear whether the effect of lacking CCK in knock-out mice is specific in the motor cortex or engages multiple brain regions.

Lastly, because Fig. 4 only showed histology in the rhinal and motor cortices, I am not sure whether the motor cortex solely receives CCK input from the rhinal cortex. A more comprehensive viral tracing result could be important to both supporting the circuit-specificity of the observed behavior in this study and providing a clearer picture of where the motor cortex receives CCK inputs.

5) I am glad to see the CCK4 rescue experiment to demonstrate the sufficiency of CCK in promoting motor learning. However, the rescue experiment lacked specificity: IP injection did not allow specific "gain of function" in the motor cortex but instead, the improved learning ability in CCK knock-out mice could be a result of a global effect of CCK4 across multiple brain regions. CCK4 injection specifically targeted at the motor cortex would be necessary to support the sufficiency of CCK-regulated neuroplasticity in the motor cortex to promote motor learning.

Reviewer #1 (Public Review):

This is a review of the manuscript entitled "Pharmacologic hyperstabilisation of the HIV-1 capsid lattice induces capsid failure" by Faysal et al., in this manuscript the authors used an elegant single virion fluorescence assay based on TIRF to measure the stability of mature HIV cores. Virions were biotinylated and captured onto glass coverslips through specific Biotin-Avidin interactions. Immobilized virions were then introduced to the imaging buffer which contained the pore-forming protein DLY, and fluorescently labeled CypA. Mature virions were identified through the binding of CypA which had a red fluorescent tag allowing them to measure the dynamics of GFP trapped within the mature cores as well as the CypA bound outside the core. The authors show that the addition of LEN starting from about 50nM stabilized the mature cores even after cores have ruptured and released their internal GFP. Higher concentration of Len results in ultrastabilization of the cores and rapid rupture leading to the release of GFP at an earlier timepoint. A biochemical assembly assay was performed which showed uM quantities of Len synergized with IP6 to promote CA assembly. Purified mature virions were also treated with 700nM of Len and analyzed by CryoET, this analysis showed an increased representation of irregular cores within the Len-treated sample. Putting all of this together, the authors concluded that Len facilitates core rupture through hyperstabilization of HIV cores, as described in the title.

While I have found this work technically well performed and well explained, I do not believe that the presented data supports the conclusions reached by the authors.

Reviewer #3 (Public Review):

In this article, Faisal et. al., use a combinatorial approach to look at the mechanisms of HIV-capsid inhibition by the highly potent drug Lenacepavir (LEN). The authors conclude that LEN induces capsid opening, but hyper-stabilizes the remaining capsid lattice during the early stages, and adversely affects the assembly of capsids during late stages of HIV-1 infection. Additionally, they suggest that hyper-stabilization effects of LEN on the capsid-lattice are induced by a low occupancy of this highly potent drug, while less potent inhibitors like PF74 need high occupancy on the lattice to induce similar effects. Taken together their findings shine a light on the importance of the capsid binding pocket targeted by multiple inhibitors including LEN, PF74, BI-2, and host-factor CPSF6 on overall capsid assembly, its stability in cells, and its role in HIV-1 infection.

Strengths:<br /> 1. Combinatorial approach using single-molecule imaging, cryoET and cellular assays show the adverse effects of LEN on HIV-1 capsid assembly, capsid disassembly, and block to virus infectivity.<br /> 2. Several novel insights are obtained in this paper, including the cryoET-data showing 2-layers of capsid formation in the presence of LEN. CPSF6-peptide binding to capsids, and their effect on stability.

Weakness:<br /> 1. Interpretation of the capsid stability data is focused on single virus traces rather than population analysis, which might paint a different picture of the conclusions.<br /> 2. The description and interpretation of the data in the results sections and the conclusions are inconsistent, and somewhat confusingly presented for the general non-expert audience.

Reviewer #2 (Public Review):

The authors provide a nice resource of putative direct BMP target genes in Nematostella vectensis by performing ChIP-seq with an anti-pSmad1/5 antibody, while also performing bulk RNA-seq with BMP2/4 or GDF5 knockdown embryos. Genes that exhibit pSmad1/5 binding and have changes in transcription levels after BMP signaling loss were further annotated to identify those with conserved BMP response elements (BREs). Further characterization of one of the direct BMP target genes (zswim4-6) was performed by examining how expression changed following BMP receptor or ligand loss of function, as well as how loss or gain of function of zswim4-6 affected development and BMP signaling. The authors concluded that zswim4-6 modulates BMP signaling activity and likely acts as a pSMAD1/5 dependent co-repressor. However, the mechanism by which zswim4-6 affects the BMP gradient or interacts with pSMAD1/5 to repress target genes is not clear. The authors test the activity of a zswim4-6 homologue in zebrafish (zswim5) by over-expressing mRNA and find that pSMAD1/5/9 labeling is reduced and that embryos have a phenotype suggesting loss of BMP signaling, and conclude that zswim4-6 is a conserved regulator of BMP signaling. This conclusion needs further support to confirm BMP loss of function phenotypes in zswim5 over-expression embryos.

Major comments

1. The BMP direct target comparison was performed between Nematostella, Drosophila, and Xenopus, but not with existing data from zebrafish (Greenfeld 2021, Plos Biol). Given the functional analysis with zebrafish later in the paper it would be nice to see if there are conserved direct target genes in zebrafish, and in particular, is zswim5 (or other zswim genes) are direct targets. Since conservation of zswim4-6 as a direct BMP target between Nematostella and Xenopus seemed to be part of the rationale for further functional analysis, it would also be nice to know if this is a conserved target in zebrafish.

Related to this, in the discussion it is mentioned that zswim4/6 is also a direct BMP target in mouse hair follicle cells, but it wasn't obvious from looking at the supplemental data in that paper where this was drawn from.

2. The loss of zswim4-6 function via MO injection results in changes to pSmad1/5 staining, including a reduction in intensity in the endoderm and gain of intensity in the ectoderm, while over-expression results in a loss of intensity in the ectoderm and no apparent change in the endoderm. While this is interesting, it is not clear how zswim4-6 is functioning to modify BMP signaling, and how this might explain differential effects in ectoderm vs. endoderm. Is the assumption that the mechanism involves repression of chordin? And if so one could test the double knockdown of zswim4-6 and chordin and look for the rescue of pSad1/5 levels or morphological phenotype.

3. Several experiments are done to determine how zswim4-6 expression responds to the loss of function of different BMP ligands and receptors, with the conclusion being that swim4-6 is a BMP2/4 target but not a GDF5 target, with a lot of the discussion dedicated to this as well. However, the authors show a binary response to the loss of BMP2/4 function, where zswim4-6 is expressed normally until pSmad1/5 levels drop low enough, at which point expression is lost. Since the authors also show that GDF5 morphants do not have as strong a reduction in pSmad1/5 levels compared to BMP2/4 morphants, perhaps GDF5 plays a positive but redundant role in swim4-6 expression. To test this possibility the authors could inject suboptimal doses of BMP2/4 MO with GDF5 MO and look for synergy in the loss of zswim4-6 expression.

4. The zswim4-6 morphant embryos show increased expression of zswim4-6 mRNA, which is said to indicate that zswim4-6 negatively regulates its own expression. However in zebrafish translation blocking MOs can sometimes stabilize target transcripts, causing an artifact that can be mistakenly assumed to be increased transcription (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7162184/). Some additional controls here would be warranted for making this conclusion.

5. Zswim4-6 is proposed to be a co-repressor of pSmad1/5 targets based on the occupancy of zswim4-6 at the chordin BRE (which is normally repressed by BMP signaling) and lack of occupancy at the gremlin BRE (normally activated by BMP signaling). This is a promising preliminary result but is based only on the analysis of two genes. Since the authors identified BREs in other direct target genes, examining more genes would better support the model.

6. The rationale for further examination of zswim4-6 function in Nematostella was based in part on it being a conserved direct BMP target in Nematostella and Xenopus. The analysis of zebrafish zswim5 function however does not examine whether zswim5 is a BMP target gene (direct or indirect). BMP inhibition followed by an in situ hybridization for zswim5 would establish whether its expression is activated downstream of BMP.

7. Although there is a reduction in pSmad1/5/9 staining in zebrafish injected with zswim5 mRNA, it is difficult to tell whether the resulting morphological phenotypes closely resemble zebrafish with BMP pathway mutations (such as bmp2b). More analysis is warranted here to determine whether stereotypical BMP loss of function phenotypes are observed, such as dorsalization of the mesoderm and loss of ventral tail fin.

Reviewer #3 (Public Review):

To identify direct targets of BMP signal in Nematostella, the authors performed ChIP-seq using an antibody against phosphorylated SMAD1/5 (pSMAD1/5) at late gastrula and late planula stages. In accordance with the highly dynamic BMP activity detected using immunofluorescence, pSMAD1/5 binding profiles change drastically as the larvae develop, with only a fraction of target genes shared between these two time points. The authors then followed up with RNA-seq in control versus BMP2/4 KD embryos and identified significant expression changes in many transcription factors and signaling molecules, including the Gbx-Hox genes, which are known to regulate endoderm patterning. These results, in conjunction with a thorough validation using in situ hybridization, strongly support the authors' claim that the BMP signal in Nematostella directly controls a small set of second-tier targets which in turn execute the morphogenic functions.

Next, the authors explored the conservation of BMP downstream targets by intersecting their candidate list with two published datasets from Drosophila (2-3hpf) and Xenopus (NF20 stage). Results from such an analysis should be taken with a grain of salt, as the developmental time points and biological context examined here are not necessarily comparable. Furthermore, whole genome duplication in vertebrates means multiple copies of transcription factors and signaling molecules belonging to the same family exist in Xenopus, making a homology-based comparison difficult. A handful of shared targets were identified between different species, although no statics were provided to support the significance of such an observation.

The authors then focused on Zswim4-6, one of the identified BMP targets with a high pSMAD1/5 enrichment level, and dissected its regulatory properties on BMP activity. Using complimentary knockdown and overexpression experiments, the authors rigorously demonstrated that Zswim4-6 is crucial to maintaining the proper pSMAD1/5 gradient at the late gastrula stage. By ectopically overexpressing a GFP tagged form of Zswim4-6, the authors performed low input ChIP-qPCR and confirmed that Zswim4-6 selectively binds to a regulatory region of a BMP-repressed gene, suggesting it may function as a co-repressor for certain BMP targets.<br /> Lastly, the authors examined the effect of Zswim5, a bilaterian homolog of Zswim4-6, during zebrafish D-V axis establishment. Overexpression of Zswim5 leads to a dampened pSMAD1/5 gradient and dorsalization of the fish larvae, hinting at the possibility that Zswim5 may function as a BMP modulator in zebrafish as well.

Overall, despite certain caveats, the experimental evidence supports the claims from the authors that Zswim4-6 is directly activated by and reciprocally modulates the BMP activity in Nematostella. The work presented here opens exciting possibilities to further dissect the gene regulatory networks downstream of the cnidarian BMP signaling pathway and expands our knowledge on the evolution of a bilaterally symmetric body plan.

Reviewer #1 (Public Review):

Summary:

Through a series of psychophysical experiments, Merkel et al examined the process of feature-based resource allocation during parallel feature value tracking, where subjects are asked to simultaneously track changing but spatially inseparable color streams. They find that tracking precision is highly imbalanced between streams, and the tracking precision changes over time by alternating between streams at a rate of ~1Hz.

Strengths:

The study addresses an intriguing research question that fills a gap in existing literature, and was carefully designed and well-executed, with a series of experiments and control experiments.

Weaknesses:

1. My main concern is the null effect of precision estimation pattern between cued and un-cued trials. It is well established that relative to the un-cued stimuli, the cued stimuli obtain more attentional resource and this study claimed serial attentional resource allocation during parallel feature value tracking. However, all Experiments 3a-c did not find any difference in precision estimates between these two types of trials.<br /> 2. Results of Exp.1 in the main text were different from those in Figure.<br /> 3. It would be helpful to add more details for the assignation of response 1 and response 2 to target 1 and target 2, respectively, in all experiments.

Reviewer #2 (Public Review):

The authors asked the question about whether and how changing feature values within the same feature dimensions are tracked. Using a series of behavioral studies combined with modeling approaches, the authors report interesting results regarding a robust, uneven distribution of attentional resources between two changing feature values (in a 2:1 ratio), alternating at 1 Hz. Although the results are clear, it is important to rule out the possible biases due to computational processes. The results advanced our understanding of how parallel tracking of multiple feature values within the same dimension is achieved.

Reviewer #3 (Public Review):

The study is interesting and the results are informative in how well people can report colors of two superimposed dot clouds. It reveals that there are trade-offs between reporting two colors. However, I have a few basic but major concerns with the present study and its conclusions about people's abilities to continuously track color values and the rate at which attention may be allocated across the two streams which I am outlining below.

1) The first concern regards the task that was used to measure continuous tracking of feature values, which in my view is ambiguous in whether it truly assesses active tracking of features or rather short-term memory of the last-seen colors. Specifically, participants were viewing two colored dot clouds that then turned gray, and were asked to report each of the colors they saw using continuous report. The test usually occurred after 6-8s (in Exp. 1 &2), so while not completely predictable, participants could easily perform the task without tracking both feature streams continuously and simply perform the color report based on the very last colors they saw. In other words, it does not seem necessary to know which color belonged to which stream, or what color it was before, to perform the task successfully. Thus, it is unclear to what extent this task is actually measuring active tracking, the same way tracking of spatial locations in multiple-object tracking tasks has been studied, which is the literature that the authors are trying to draw parallels to. In multiple-object tracking tasks, targets and nontarget objects look identical and so to keep track of which of the moving objects are targets, participants need to attend to them actively and selectively. (Similarly, the original feature-tracking study by Blaser et al., at least in their main experiment, people were asked to track an object superimposed on a second object which required continuous and selective tracking of that object).

2) The main claim that tracking two colors relies on a shared and strictly limited resource is primarily based on the relation between the two responses people give, such that the first response about one color tends to be higher accuracy than for the second response of the other color across participants. In my view, this is a relatively weak version of looking at trade-offs in resources, and it would have been more compelling to show such trade-offs at a single-trial level, or assess them with well-established methods that have been developed to look at attentional bottlenecks such as attention-operating characteristics that allow quantifying the cost of adding an additional task in a precise and much more direct manner.

3) Finally, the data of the last experiment is taken as evidence that feature-based selection oscillates at 1Hz between the two streams. This is based on response errors changing across time points with respect to an exogenous cue that is thought to "reset" attentional allocation to one stream. Only one of three data sets (which uses relatively sparse temporal sampling) shows a significant interaction between cue and time, and given that there was no a priori prediction of when such interaction should occur, this result begs for a replication to ensure that this is not a false positive result. Furthermore, based on the analyses done in the paper, it may very well be the case that the presumed "switching rate" is entirely non-oscillatory based on a recent very important paper by Geoffrey Brookshire (2022, Nature Human Behavior) that demonstrates that frequency analysis are not just sensitive to periodic but also aperiodic temporal structures. The paper also has a series of suggested analyses that could be used here to further test the current conclusions.

Reviewer #3 (Public Review):

This paper studies the role of the core PCP pathway on tissue morphogenesis of the Drosophila pupil wing. The authors used three different core PCP mutants to compare the cell dynamics with the wild type and conclude that core PCP does not guide the global patterns of cell dynamics during pupal wing morphogenesis. They use the previously published "triangle method" to extract modes of deformation (total shear, cell elongation, cell rearrangements) and find that they are the same (to within error) in the core PCP mutants. Moreover, the global shape of the wing at the end of the process is nearly the same, too.

Using laser ablation and a rheological model, the paper also investigates the effect of the core PCP pathway on the short-time mechanical properties of the tissue. The authors find that the short-time mechanical response is different in core PCP mutants. This is surprising, as most researchers in the field assume that the short-time recoil velocity is a proxy for tissue mechanics, and therefore also predictive of global tissue deformations. So the observation that the short-time recoils are different, while the global response is the same, is important for the field to understand.

A challenge with the paper as written is that it does not clearly explain how to reconcile these two observations, stating in the discussion that "the proportionality factor [which relates short-time recoil to tissue mechanics] can depend on the genotype and can change in time". It is possible that the data and model in the paper could be used to make a more convincing and clear statement.

The paper is conceptually interesting, methodologically sound, and likely impactful to the broad area of tissue mechanics and mechanobiology.

Reviewer #1 (Public Review):

Mohibi et al. utilized genetic approaches to determine the role of FDX1 in the regulation of development, oncogenesis, and metabolism. The strengths of the current study are the utilization of both in vivo and in vitro methods coupled to classical biochemical/molecular biology tools and lipidomic screening. The data provided is convincing demonstrating genetic loss of even one allele of FDX1 promotes premature death, increased incidence of adenocarcinoma, and dysregulated lipid metabolism. The authors provide further mechanistic evidence showing enhanced SREBP2 activation, which could potentially be underlying the altered lipid metabolism observed in their model. These findings are likely to provide a novel target for the amelioration to lipid metabolic disorders as the authors show genetic overexpression of FDX1 can reduce intracellular lipid accumulation.

Reviewer #2 (Public Review):

In this manuscript, the Chen group aimed to understand the role of FDX1 in vivo. While its role in the biogenesis of steroids and bile acids, Vitamin A/D metabolism, and lipoylation of TCA enzymes has been extensively studied biochemically, its role in physiology and lipid metabolism is still unknown. The authors established a conditional Fdx1 KO mice and performed a series of experiments to demonstrate the physiological role of Fdx1 in mice. The obtained evidence convincingly supports the major conclusion of the study. The manuscript is well and concisely written.

Strengths:<br /> • Solid data showing that Fdx1+/- mice are prone to steatohepatitis and Fdx1+/- cells accumulate lipids<br /> • Untargeted MS profiling the changes of lipids upon Fdx1 KO.<br /> • Clear evidence indicating that the ABCA1-SREBP1/2 pathway is involved in the function of Fdx1 in lipid metabolism.

Weaknesses:<br /> • use of Fdx1+/- MEFs, instead of using Fdx1-/- MEFs, could be well justified.

Reviewer #1 (Public Review):

Weber et al. collect locus coeruleus (LC) tissue blocks from 5 neurotypical European men, dissect the dorsal pons around the LC, and prepare 2-3 tissue sections from each donor on a slide for 10X spatial transcriptomics. From three of these donors, they also prepared an additional section for 10x single nucleus sequencing. Overall, the results validate well-known marker genes for the LC (e.g. DBH, TH, SLC6A2), and generate a useful resource that lists genes that are enriched in LC neurons in humans, with either of these two techniques. A comparison with publicly available mouse and rat datasets identifies genes that show reliable LC enrichment across species. Their analyses also support recent rodent studies that have identified subgroups of interneurons in the region surrounding the LC, which show enrichment for different neuropeptides. In addition, the authors claim that some LC neurons co-express cholinergic markers and that a population of serotonin (5-HT) neurons is located within or near the LC. These last two claims must be taken with great caution, as several technological limitations restrict the interpretation of these results. Technical limitations currently limit the ability to integrate spatial and single-nucleus sequencing, yet the manuscript presents a valuable resource on the gene expression landscape of the human LC.

Reviewer #2 (Public Review):

The data generated for this paper provides an important resource for the neuroscience community. The locus coeruleus (LC) is the known seed of noradrenergic cells in the brain. Due to its location and size, it remains scarcely profiled in humans. Despite the physically minute structure containing these cells, its impact is wide-reaching due to the known neuromodulatory function of norepinephrine (NE) in processes like attention and mood. As such, profiling NE cells has important implications for most neurological and neuropsychiatric disorders. This paper generates transcriptomic profiles that are not only cell-specific but which also maintain their spatial context, providing the field with a map for the cells within the region.

Strengths:

Using spatial transcriptomics in a morphologically distinct region is a very attractive way to generate a map. Overlaying macroscopic information, i.e. a region with greater pigmentation, with its corresponding molecular profile in an unbiased manner is an extremely powerful way to understand the specific cellular and molecular composition of that brain structure.

The technologies were used with an astute awareness of their limitations, as such, multiple technologies were leveraged to paint a more complete and resolved picture of the cellular composition of the region. For example, the lack of resolution in the spatial transcriptomic platform was compensated by complementary snRNA-seq and single molecule FISH.

This work has been made publicly available and accessible through a user-friendly application such that any interested researcher can investigate the level of expression of their gene of interest within this region.

Two important implications from this work are 1) the potential that the gene regulatory profiles of these cells are only partially conserved across species, humans, and rodents, and 2) that there may be other neuromodulatory cell types within the region that were otherwise not previously localized to the LC

Weaknesses:

Given that the markers used to identify cells are not as specific as they need to be to definitively qualify the desired cell type, the results may be over-interpreted. Specifically, TH is the primary marker used to qualify cells as noradrenergic, however, TH catalyzes the synthesis of L-DOPA, a precursor to dopamine, which in turn is a precursor for epinephrine and norepinephrine suggesting some of the cells in the region may be dopaminergic and not NE cells. Indeed, there are publications to support the presence of dopaminergic cells in the LC (see Kempadoo et al. 2016, Takeuchi et al., 2016, Devoto et al. 2005). This discrepancy is further highlighted by the apparent lack of overlap per given Visium spots with TH, SCL6A2, or DBH. While the single-nucleus FISH confirms that some of the cells in the region are noradrenergic, others very possibly represent a different catecholamine. As such it is suggested that the nomenclature for the cells be reconsidered.

The authors are unable to successfully implement unsupervised clustering with the spatial data, this greatly reduces the impact of the spatial technology as it implies that the transcriptomic data generated in the study did not have enough resolution to identify individual cell types.

The sample contribution to the results is highly unbalanced, which consequently, may result in ungeneralizable findings in terms of regional cellular composition, limiting the usefulness of the publicly available data.

This study aimed to deeply profile the LC in humans and provide a resource to the community. The combination of data types (snRNA-seq, SRT, smFISH) does in fact represent this resource for the community. However, due to the limitations, of which, some were described in the manuscript, we should be cautious in the use of the data for secondary analysis. For example, some of the cellular annotations may lack precision, the cellular composition also may not reflect the general population, and the presence of unexpected cell types may represent the accidental inclusion of adjacent regions, in this case, serotonergic cells from the Raphe nucleus.

Nonetheless having a well-developed app to query and visualize these data will be an enormous asset to the community especially given the lack of information regarding the region in general.

Reviewer #3 (Public Review):

In this study, the authors present the first comprehensive transcriptome map of the human locus coeruleus using two independent but complementary approaches, spatial transcriptomics and single-nucleus RNA sequencing. Several canonical features of locus coeruleus neurons that have been described in rodents were conserved, but potentially important species differences were also identified. This work lays the foundation for future descriptive and experimental approaches to understanding the contribution of the locus coeruleus to healthy brain function and disease.

This study has many strengths. It is the first reported comprehensive map of the human LC transcriptome and uses two independent but complementary approaches (spatial transcriptomics and snRNA-seq). Some of the key findings confirmed what has been described in the rodent LC, as well as some intriguing potential genes and modules identified that may be unique to humans and have the potential to explain LC-related disease states. The main limitations of the study were acknowledged by the authors and include the spatial resolution probably not being at the single cell level and the relatively small number of samples (and questionable quality) for the snRNA-seq data. Overall, the strengths greatly outweigh the limitations. This dataset will be a valuable resource for the neuroscience community, both in terms of methodology development and results that will no doubt enable important comparisons and follow-up studies.

Reviewer #1 (Public Review):

The work by Ohigashi and colleagues addresses the developmental and lineage relationship of a newly characterized thymus epithelial cell (TEC) progenitor subset. The authors take advantage of an elegant and powerful set of experimental approaches to demonstrate that CCL21-expressing TECs appear early in thymus organogenesis and that these cells, which are centrally located, go on to give rise to medullary (m)TECs. What makes the findings intriguing is that these CCL21-expressing mTECs are a distinct subset, which do not express RANK or AIRE, and transcriptomic and lineage tracing approaches point to these cells as potential mTEC progenitor-like cells. Of note, using in vitro and in vivo precursor-product cell transfer experiments, the authors show that this subset has a developmental potential to give rise to AIRE+ self-antigen-displaying mTECs, revealing that CCL21-expressing mTECs can give rise to distinct mTEC subsets. This functional duality provides an attractive rationale for the necessary function of mTECs, which is to attract CCR7+ thymocytes that have just undergone positive selection in the thymus cortex to enter the medulla to undergo tolerance-induction against self-antigen-displaying mTECs. Overall, the work is well supported and offers new insights into the diverse functions of the medullary compartment, and how two distinct subsets of mTECs can achieve it.

Reviewer #2 (Public Review):

Summary:

The authors set out to discover a developmental pathway leading to functionally diverse mTEC subsets. They show that Ccl21 is expressed early during thymus ontogeny in the medullary area. Fate-mapping gives evidence for the Ccl21 positive history of Aire positive mTECs as well as of thymic tuft cells and postnatally of a certain percentage of cTECs. Therefore, the differentiation potential of Ccl21+ TECs is tested in reaggregate thymus experiments - using embryonic or postnatal Ccl21+ TECs. From these experiments, the authors conclude that at least embryonic mTECs in large part pass through a Ccl21 positive stage prior to differentiation towards an Aire expressing or tuft cell stage.

The authors are using Ccl21a as a marker for a bipotent progenitor that is detectable in the embryonic thymus and is still present at the adult stage mainly giving rise to mTECs. The choice of this marker gene is very interesting since Ccl21 expression can directly be linked to an important aspect in thymus biology: the expression of Ccl21 by cells in the thymic medulla allows trafficking of T cells into the medulla in order to undergo T cell selection.

Making use of the Ccl21 detection, the authors can nicely show that cells actively expressing Ccl21 are localized throughout the medulla at an embryonic stage but also in adult thymus tissue. This suggests, that this progenitor is not accumulating at a specific area inside the medulla. This is a new finding.

Moreover, the finding that a Ccl21+ progenitor population plays a functional role in thymocyte trafficking towards the medulla has not been described. Thus, Ccl21 expression may be used to localize a late bipotent progenitor in the thymic lobes.<br /> In addition, in Fig.8, the authors provide evidence that these progenitor cells have the potential to self-maintain as well as to differentiate in reaggregate experiments at E17 (not at 4 weeks of age). The first point is of great interest and importance since these cells in theory can be of therapeutic use.

Overall assessment:

The authors highlight a developmental pathway starting from a Ccl21-expressing TEC progenitor that contributes to a functionally diverse mTEC repertoire. This is a welcome addition to current knowledge of TEC differentiation.

Reviewer #3 (Public Review):

In this manuscript, the authors define the developmental trajectory resulting in a diverse mTEC compartment. Using a variety of approaches, including a novel CCL21-fate mapping model, data is presented to argue that embryonic CCL21-expressing thymocyte attracting mTECs naturally convert to into self-antigen displaying mTEC subsets, including Aire+ mTECs and thymic tuft cells. Perhaps somewhat surprisingly, a large fraction of cTECs were also marked for having expressed CCL21, suggesting that there exists some conversion of mTEC (progenitors) into cTEC, a developmentally interesting observation that could be followed up later. Overall, the experimental setup, writing, and conclusions, are all outstanding.

Reviewer #1 (Public Review):

Summary: A description of a modern protocol for cervical screening that likely could be used in any country of the world, based on self-sampling, extended HPV genotypinng and AI-assisted visual inspection - which is probably the best available combination today.

Strengths: Modern, optimised protocol, designed for global use. Innovative.

Weaknesses: The protocol is not clear. I could not even find how many women were going to be enrolled, the timelines of the study, the statistical methods ("comparing" is not statistics) or the power calculations.<br /> Tables 2 and 3 are too schematic - surely the authors must have an approximate idea of what the actual numbers are behind the green, red and yellow colors.<br /> Figure 1 comparing screening and vaccination is somewhat misleading. They screen 20 birth cohorts but vaccinate only 5 birth cohorts. Furthermore, the theoretical gains of screening has not really been attained in any country in practise. Modelling can be a difficult task and the commentary does not provide any detail on how to evaluate what was done. It just seems unnecessary to attack vaccination as a motivation on why screening needs to be modernised.

Reviewer #2 (Public Review):

Summary:

This manuscript describes the study protocol, structure and logic of the PAVE strategy. The PAVE study is a multicentric study to evaluate a novel cervical screen-triage-treat strategy for resource-limited settings as part of a global strategy to reduce cervical cancer burden. The PAVE strategy involves: 1) screening with self-sampled HPV testing; 2) triage of HPV-positive participants with a combination of extended genotyping and visual evaluation of the cervix assisted by deep-learning-based automated visual evaluation (AVE); and 3) treatment with thermal ablation or excision (Large Loop Excision of the Transformation Zone). The PAVE study has two phases: efficacy (2023-2024) and effectiveness (planned to begin in 2024-2025). The efficacy phase aims to refine and validate the screen-triage portion of the protocol. The effectiveness phase will examine few implementation of the PAVE strategy into clinical practice. In following phases implementation will further explored.

Strengths and weaknesses

The Pave Study develops and evaluates a novel strategy that combines HPV self-collection -that has been proven effective to increase screening coverage in different settings-, with genotyping and Automated Visual Evaluation as triage. The proposed strategy combined three key innovations to improve an important step in the cervical cancer care continuum. If the strategy is effective it will contribute to enhance cervical cancer prevention in low resource settings.

As authors mentioned, despite the existence of effective preventive technologies (e.g., HPV vaccine and HPV test) translation of the HPV prevention methods has not yet occurred in many Low-Middle-Income Countries. So, in this context, new screen-triage-treat strategies are needed and if PAVE strategy were effective, it could be a landmark for cervical cancer prevention.

The PAVE Study is a solid and important study that is aimed to be carried out in nine countries and recruit tens thousands of women. It is a study with a large and diverse sample that can provide useful information for the development of this new screen-triage-treat strategy. Another strength is the fact that the PAVE project is integrated into the screening activities placed in the selected countries that will allow to evaluate efficacy and effectiveness in real-word context.

The manuscript does not present results because its aim is to describe the study protocol, structure and logic of the PAVE strategy.

Phase 1 aims to evaluate efficacy of the strategy. Methods are well described and are consistent with the study aims.

Phase 2 aims to evaluate the implementation of the PAVE strategy in clinical practice. The inclusion of implementation evaluation in this type of studies is an important milestone in the field of cervical cancer prevention. It has been shown that many strategies that have proven to be effective in controlled studies face barriers when they are implemented in real life. In that sense, results of phase 2 are key to ensure the future implementation of the strategy.

Reviewer #3 (Public Review):

Summary: Despite being preventable and treatable, cervical cancer remains the second most common cause of cancer death globally. This cancer, and associated deaths, occur overwhelmingly in low- and middle-income countries (LMIC), reflecting a lack of access to vaccination, screening and treatment services. Cervical screening is the second pillar in the WHO strategy to eliminate cervical cancer as a public health problem and will be critical in delivering early gains in cervical cancer prevention as the impact of vaccination will not be realized for several decades. However, screening strategies implemented in high income countries are not feasible or affordable in LMICs. This ambitious multi-center study aims to address these issues by developing and systematically evaluating a novel approach to cervical screening. The approach, based on primary screening with self-collected specimens for HPV testing, is focused on optimizing triage of people in whom HPV is detected, so that sensitivity for the detection of pre-cancer and cancer is maximized while treatment of people without pre-cancer or cancer is minimized.

Strengths:

The triage proposed for this study builds on the authors' previously published work in designing the ScreenFire test to appropriately group the 13 detected genotypes into four channels and to develop automated visual evaluation (AVE) of images of the cervix, taken by health workers.

The move from mobile telephone devices to a dedicated device to acquire and evaluate images, overcomes challenges previously encountered whereby updates of mobile phone models required retraining of the AVE algorithm.

The separation of the study into two phases, an efficacy phase in which screen positive people will be triaged and treated according to local standard of care and the performance of AVE will be evaluated against biopsy outcomes will be followed by the second phase in which the effectiveness, cost-effectiveness, feasibility and acceptability will be evaluated.

The setting in a range of low resource settings which are geographically well spread and reflective of where the global cancer burden is highest.

Weaknesses:

Potential ascertainment bias due to the lack of specified biopsy (such as small four quadrant biopsies or small biopsies across the transformation zone) when aceto-white areas are not identified. This has the potential lead to lead to an over-estimate of sensitivity of the triage approach, particularly in the setting of VIA as compared to colposcopy. While the authors specify endocervical sampling in this setting, using curette or brush (for cytology), this may not be as sensitive unless clinicians are experienced in endocervical curette procedures.

Reviewer #1 (Public Review):

Summary:<br /> The presented study focuses on the role of formin-like 2 (FMNL2) in oocyte meiosis. The authors assessed FMNL2 expression and localization in different meiotic stages and subsequently, by using siRNA, investigated the role of FMNL2 in spindle migration, polar body extrusion, and distribution of mitochondria and endoplasmic reticulum (ER) in mouse oocytes.

Strengths:<br /> Novelty in assessing the role of formin-like 2 in oocyte meiosis.

Weaknesses:<br /> Methods are not properly described.<br /> Overstating presented data.<br /> It is not clear what statistical tests were used.

My main concern is that there are missing important details of how particular experiments and analyses were done. The material and methods section is not written in the way that presented experiments could be repeated - it is missing basic information (e.g., used mouse strain, timepoints of oocytes harvest for particular experiments, used culture media, image acquisition parameters, etc.). Some of the presented data are overstated and incorrectly interpreted. It is not clear to me how the analysis of ER and mitochondria distribution was done, which is an important part of the presented data interpretation. I'm also missing important information about the timing of particular stages of assessed oocytes because the localization of both ER and mitochondria differs at different stages of oocyte meiosis. The data interpretation needs to be justified by proper analysis based on valid parameters, as there is considerable variability in the ER and mitochondria structure and localization across oocytes based on their overall quality and stage.

Reviewer #2 (Public Review):

Summary:<br /> This research involves conducting experiments to determine the role of Fmnl2 during oocyte meiosis I.

Strengths:<br /> Identifying the role of Fmnl2 during oocyte meiosis I is significant.

Weaknesses:<br /> The quantitative analysis and the used approach to perturb FMNL2 function are currently incomplete and would benefit from more confirmatory approaches and rigorous analysis.

1- Most of the results are expected. The new finding here is that FMNL2 regulates cytoplasmic F-actin in mouse oocytes, which is also expected given the role of FMNL2 in other cell types. Given that FMNL2 regulates cytoplasmic F-actin, it is very expected to see all the observed phenotypes. It is already established that F-actin is required for spindle migration to the oocyte cortex, extruding a small polar body and normal organelle distribution and functions.

2-The authors used Fmnl2 cRNA to rescue the effect of siRNA-mediated knockdown of Fmnl2. It is not clear how this works. It is expected that the siRNA will also target the exogenous cRNA construct (which should have the same sequence as endogenous Fmnl2) especially when both of them were injected at the same time. Is this construct mutated to be resistant to the siRNA?

3-The authors used only one approach to knockdown FMNL2 which is by siRNA. Using an additional approach to inhibit FMNL2 would be beneficial to confirm that the effect of siRNA-mediated knockdown of FMNL2 is specific.

Reviewer #3 (Public Review):

Summary:<br /> The authors focus on the role of formin-like protein 2 in the mouse oocyte, which could play an important role in actin filament dynamics. The cytoskeleton is known to influence a number of cellular processes from transcription to cytokinesis. The results show that downregulation of FMNL2 affects spindle migration with resulting abnormalities in cytokinesis in oocyte meiosis I.

Weaknesses:<br /> The overall description of methods and figures is overall dismissively poor. The description of the sample types and number of replicate experiments is impossible to interpret throughout, and the quantitative analysis methods are not adequately described. The number of data points presented is unconvincing and unlikely to support the conclusions. On the basis of the data presented, the conclusions appear to be preliminary, overstated, and therefore unconvincing.

Reviewer #1 (Public Review):

Summary:<br /> Fukuhara, Maenaka, and colleagues report a crystal structure of the canine distemper virus (CDV) attachment hemagglutinin protein globular domain. The structure shows a dimeric organization of the viral protein and describes the detailed amino-acid side chain interactions between the two protomers. The authors also use their best judgement to comment on predicted sites for the two cellular receptors - Nectin-4 and SLAM - and thus speculate on the CDV host tropism. A complementary AFM study suggests a breathing movement at the hemagglutinin dimer interface.

Strengths:<br /> The study of CDV and related Paramyxoviruses is significant for human/animal health and is very timely. The crystallographic data seem to be of good quality.

Weaknesses:<br /> While the recent CDV hemagglutinin cryo-EM structure is mentioned, it is not compared to the present crystal structure, and thus the context of the present study is poorly justified. Additionally, the results of the AFM experiment are not unexpected. Indeed, other paramyxoviral RBP/G proteins also show movement at the protomer interface.

Reviewer #2 (Public Review):

Summary:<br /> The authors solved the crystal structure of CDV H-protein head domain at 3,2 A resolution to better understand the detailed mechanism of membrane fusion triggering. The structure clearly showed that the orientation of the H monomers in the homodimer was similar to that of measles virus H and different from other paramyxoviruses. The authors used the available co-crystal strictures of the closely related measles virus H structures with the SLAM and Nectin4 receptors to map the receptor binding site on CDV H. The authors also confirmed which N-linked sites were glycosylated in the CDV H protein and showed that both wildtype and vaccine strains of CDV H have the same glycosylation pattern. The authors documented that the glycans cover a vast majority of the H surface while leaving the receptor binding site exposed, which may in part explain the long-term success of measles virus and CDV vaccines. Finally, the authors used HS-AFM to visualize the real-time dynamic characteristics of CDV-H under physiological conditions. This analysis indicated that homodimers may dissociate into monomers, which has implications for the model of fusion triggering.

The structural data and analysis were thorough and well-presented. However, the HS-AFM data, while very exciting, was not presented in a manner that could be easily grasped by readers of this manuscript. I have some suggestions for improvement.

1) The authors claim their structure is very similar to the recently published croy-EM structure of CDV H. Can the authors provide us with a quantitative assessment of this statement?

2) The results for the HS-AFM are difficult to follow and it is not clear how the authors came to their conclusions. Can the authors better explain this data and justify their conclusions based on it?

3) The fusion triggering model in Figure 8 is ambiguous as to when H-F interactions are occurring and when they may be disrupted. The authors should clarify this point in their model.

Reviewer #1 (Public Review):

In the manuscript, the authors tried to explore the molecular alterations of adipose tissue and skeletal muscle in PCOS by global proteomic and phosphorylation site analysis. In the study, the samples are valuable, while there are no repeats for MS and there are no functional studies for the indicted proteins, phosphorylation sites. The authors achieved their aims to some extent, but not enough.

Reviewer #2 (Public Review):

This study provides the proteomic and phosphoproteomics data for our understanding of the molecular alterations in adipose tissue and skeletal muscle from women with PCOS. This work is useful for understanding of the characteristics of PCOS, as it may provide potential targets and strategies for the future treatment of PCOS. While the manuscript presents interesting findings on omics and phenotypic research, the lack of in-depth mechanistic exploration limits its potential impact.

The study primarily presents findings from omics and phenotypic research, but fails to provide a thorough investigation into the underlying mechanisms driving the observed results. Without a thorough elucidation of the mechanistic underpinnings, the significance and novelty of the study are compromised.

Reviewer #1 (Public Review):

In this revised preprint the authors investigate whether a presumably allosteric P2RX7 activating compound that they previously discovered reduces fibrosis in a bleomycin mouse model. They chose this particular model as publicly available mRNA data indicate that the P2RX7 pathway is downregulated in idiopathic pulmonary fibrosis patients compared to control individuals. In their revised manuscript, the authors use three proxies of lung damage, Ashcroft score, collagen fibers, and CD140a+ cells, to assess lung damage following the administration of bleomycin. These metrics are significantly reduced on HEI3090 treatment. Additional data implicate specific immune cell infiltrates and cytokines, namely inflammatory macrophages and damped release of IL-17A, as potential mechanistic links between their compound and reduced fibrosis. Finally, the researchers transplant splenocytes from WT, NLRP3-KO, and IL-18-KO mice into animals lacking the P2RX7 receptor to specifically ascertain how the transplanted splenocytes, which are WT for P2RX7 receptor, respond to HEI3090 (a P2RX7 agonist). Based on these results, the authors conclude that HEI3090 enhanced IL-18 production through the P2RX7-NLRP3 inflammasome axis to dampen fibrosis.

These findings could be interesting to the field, as there are conflicting results as to whether NLRP3 activation contributes to fibrosis and if so, at what stage(s) (e.g., acute damage phase versus progression). The revised manuscript is more convincing in that three orthogonal metrics for lung damage were quantified. However, major weaknesses of the study still include inconsistent and small effect sizes of HEI3090 treatment versus either batch effects from transplanted splenocytes or the effects of different genetic backgrounds. Moreover, the fundamental assumption that HEI3090 acts specifically and functionally through the P2RX7 pathway in this model cannot be directly tested, as the authors now provide results indicating that P2RX7 knockout mice do not establish lung fibrosis on bleomycin treatment.

In order to provide clear evidence that HEI3090 functions through P2RX7, a different lung fibrosis model that does not require P2RX7 would be necessary. For example, in such a system the authors could demonstrate a lack of HEI3090-mediated therapeutic effect on P2RX7 knockout. Molecularly, additional evidence on specificity, such as thermal proteome profiling and direct biophysical binding experiments, would also enhance the authors' argument that the compound indeed binds P2RX7 directly and specifically. Since all small molecules have some degree of promiscuity, the absence of an additional P2RX7 modulator, or direct recombinant IL-18 administration (as suggested by another reviewer), is needed to orthogonally validate the functional importance of this pathway. Another way the authors could probe pathway specificity would involve co-administering α-IL-18 with HEI3090 in several key experiments (similar to Figure 4L).

Reviewer #2 (Public Review):

In the study by Hreich et al, the potency of P2RX7-specific positive modulator HEI3090, developed by the authors, for the treatment of Idiopathic pulmonary fibrosis (IPF) was investigated. Recently, the authors have shown that HEI3090 can protect against lung cancer by stimulating dendritic cell P2RX7, resulting in IL-18 production that stimulates IFN-γ production by T and NK cells (DOI: 10.1038/s41467-021-20912-2). Interestingly, HEI3090 increases IL-18 levels only in the presence of high eATP. Since the treatment options for IPF are limited, new therapeutic strategies and targets are needed. The authors first show that P2RX7/IL-18/IFNG axis is downregulated in patients with IPF. Next, they used a bleomycin-induced lung fibrosis mouse model to show that the use of a positive modulator of P2RX7 leads to the activation of the P2RX7/IL-18 axis in immune cells that limits lung fibrosis onset or progression. Mechanistically, treatment with HEI3090 enhanced IL-18-dependent IFN-γ production by lung T cells leading to a decreased production of IL-17 and TGFβ, major drivers of IPF. The major novelty is the use of the small molecule HEI3090 to stimulate the immune system to limit lung fibrosis progression by targeting the P2RX7, which could be potentially combined with current therapies available. Overall, the study was well performed and the manuscript is clear. However, there is need for more details on the description and interpretation of the adoptive transfer experiments, as well as the statistical analyses and number of replicate independent experiments.

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors observed that miR-199b-5p is elevated in osteoarthritis (OA) patients. They also found that overexpression of miR-199b-5p induced OA-like pathological changes in normal mice and inhibiting miR-199b-5p alleviated symptoms in knee OA mice. They concluded that miR-199b-5p is not only a potential micro-target for knee OA but also provides a potential strategy for the future identification of new molecular drugs.

Strengths:

The data are generated from both human patients and animal models.

Weaknesses:

The data presented in this manuscript is not solid enough to support their conclusions. There are several questions that need to be addressed to improve the quality of this study.

The following questions that need to be addressed to improve the quality of the study.

1. Exosomes were characterized by electron microscopy and western blot analysis (for CD9, 264 CD63, and CD81). However, figure S1 only showed two sample WB results and there is no positive and negative control as well as the confused not clear WB figure.

2. The sequencing of miRNAs in serum exosomes showed that 88 miRNAs were upregulated and 89 miRNAs were downregulated in KOA patients compared with the control group based on fold change > 1.5 and p < 0.05. Figure 2 legend did not clearly elucidate what those represent and why the authors chose those five miRNAs to further validate although they did mention it with several words in line 108 'based on the p-value and exosomal'.

3. In Figure 3 legend and methods, the authors did not mention how they performed the cell viability assay. What cell had been used? How long were they treated and all the details? Other figure legends have the same problem without detailed information.

4. The authors claimed that Gcnt2 and Fzd6 are two target genes of miR-199b-5p. However, there is no convincing evidence such as western blot to support their bioinformatics prediction.

5. To verify the binding site on 3'UTR of two potential targets, the authors designed a mouse sequence for luciferase assay, but not sure if it is the same when using a human sequence.

Reviewer #2 (Public Review):

Summary:

The authors identified miR-199b-5p as a potential OA target gene using serum exosomal small RNA-seq from human healthy and OA patients. Their RNA-seq results were further compared with publicly available datasets to validate their finding of miR-199b-5p. In vitro chondrocyte culture with miR-199b-5p mimic/inhibitor and in vivo animal models were used to evaluate the function of miR-199b-5p in OA. The possible genes that were potentially regulated by miR-199b-5p were also predicted (i.e., Fzd6 and Gcnt2) and then validated by using Luciferase assays.

Strengths:

1. Strong in vivo animal models including pain tests.<br /> 2. Validates the binding of miR-199b-5p with Fzd6 and binding of miR-199b-5p with Gcnt2.

Weaknesses:

1. The authors may overinterpret their results. The current work shows the possible bindings between miR-199b-5p and Fzd6 as well as bindings between miR-199b-5p and Gcnt2. However, whether miR-199b-5p truly functions through Fzd6 and/or Gcnt2 requires genetic knockdown of Fzd6 and Gcnt2 in the presence of miR-199b-5p.<br /> 2. In vitro chondrocyte experiments were conducted in a 2D manner, which led to chondrocyte de-differentiation and thus may not represent the chondrocyte response to the treatments.<br /> 3. There is a lack of description for bioinformatic analysis.<br /> 4. There are several errors in figure labeling.