Reviewer #3 (Public Review):

Although the response to stress has been extensively studied in pulmonary epithelium and mesenchyme, the post-injury proliferation and subsequent regeneration of pulmonary capillary endothelial cells remain poorly understood. Following their previous study on identifying mouse lung endothelial cell heterogeneity, Niethamer et al. reported a lung capillary subpopulation, CAP1_B with highly enriched Atf3. This capillary subpopulation expanded and increased the expression of genes involved in vascular regeneration in response to influenza-induced lung injury. Loss of Atf3 in lung endothelial cells led to abnormal alveoli structure and loss of endothelial cells through inhibiting cell proliferation and inducing apoptosis. This manuscript provided strong evidence to demonstrate the importance of Atf3 in mediating endothelial response to lung injury, which is novel to the field.

Joint Public Review:

The manuscript "Monoallelically-expressed Noncoding RNAs form nucleolar territories on NOR-containing chromosomes and regulate rRNA expression" reports the discovery of a family of ncRNAs they call SNULs for Single NUcleolus Localized RNA and examine their localization with respect to nucleoli and reports that the RNAs they are examining are monoallelically expressed in a mitotically stable manner similar to what happens in X inactivation.

These RNAs come from a screen which is not well described and the descriptions of the sequence analyses are unclear, so it is difficult to know exactly what they are analyzing in the manuscript. If these are RNAs with reasonable abundance, then they should be findable without the extensive PCR amplification they appear to have done for the PacBio sequencing (the methods section is not clear on exactly how many rounds of PCR were performed). Moreover, given the acknowledged sequence similarities of the SNULs with other RNAs, the possibility of chimaera formation during PCR amplification is high. They are clearly detecting RNAs associated with nucleoli but exactly what they are examining is unclear. It is possible that a clear determination of the genomic origin of these RNAs will be complicated by the repetitive sequences in the regions of the genome where they reside.

Note also that the idea of monoallelic expression from rRNA encoding loci is interesting, but has been established in 2009. Title: Allelic inactivation of rDNA loci. Genes Dev. 2009 Oct 15;23(20):2437-47. doi: 10.1101/gad.544509.

Reviewer #1 (Public Review):

Jordan and Keller investigated the possibility that sensorimotor prediction error (mismatch between expected and actual inputs) triggers locus coeruleus (LC) activation, which in turn drives plasticity of cortical neurons that detect the mismatch (e.g. layer 2/3 neurons in V1), thus updating the internal presentation (expected) to match more the sensory input. Using genetic tools to selectively label LC neurons in mice and in vivo imaging of LC axonal calcium responses in the V1 and motor cortex in awake mice in virtual reality training, they showed that LC axons responded selectively to a mismatch between the visual input and locomotion. The greater the mismatch (the faster the locomotion in relation to the visual input), the larger the LC response. This seemed to be a global response as LC responses were indistinguishable between sensory and motor cortical areas. They further showed that LC drove learning (updating the internal model) despite that LC optical stimulation failed to alter acute cellular responses. Responses in the visual cortex increased with locomotion, and this was suppressed following LC phasic stimulation during visuomotor coupled training (closed loop). In the last section, they showed that artificial optogenetic stimulation of LC permitted plasticity over minutes, which would normally take days in non-stimulated mice trained in the visuomotor coupling mode. These data enhance our understanding of LC functionality in vivo and support the framework that LC acts as a prediction error detector and supervises cortical plasticity to update internal representations.

The experiments are well-designed and carefully conducted. The conclusions of this work are in general well supported by the data.

Reviewer #2 (Public Review):

The work presented by Jordan and Keller aims at understanding the role of noradrenergic neuromodulation in the cortex of mice exploring a visual virtual environment. The authors hypothesized that norepinephrine released by Locus Coeruleus (LC) neurons in cortical circuits gates the plasticity of internal models following visuomotor prediction errors. To test this hypothesis, they devised clever experiments that allowed them to manipulate visual flow with respect to locomotion to create prediction errors in visuomotor coupling and measure the related signals in LC axons innervating the cortex using two-photon calcium imaging. They observed calcium responses proportional to absolute prediction errors that were non-specifically broadcast across the dorsal cortex. To understand how these signals contribute to computations performed by V1 neurons in layers 2/3, the authors activated LC noradrenergic inputs using optogenetic stimulations while imaging calcium responses in cortical neurons. Although LC activation had little impact on evoked activity related to visuomotor prediction errors, the authors observed changes in the effect of locomotion on visually evoked activity after repeated LC axons activation that were absent in control mice. Using a clever paradigm where the locomotion modulation index was measured in the same neurons before and after optogenetic manipulations, they confirmed that this plasticity depended on the density of LC axons activated, the visual flow associated with running, and the concurrent visuomotor coupling during LC activation. Based on similar locomotion modulation index dependency on speed observed in mice that develop only with visuomotor experience in the virtual environment, the authors concluded that changes in locomotion modulation index are the result of experience-dependent plasticity occurring at a much faster rate during LC axons optogenetic stimulations.

The study provides very compelling data on a timely and fascinating topic in neuroscience. The authors carefully designed experiments and corresponding controls to exclude any confounding factors in the interpretation of neuronal activity in LC axons and cortical neurons. The quality of the data and the rigor of the analysis are important strengths of the study. I believe this study will have an important contribution to the field of system neuroscience by shedding new light on the role of a key neuromodulator. The results provide strong support for the claims of the study.

Peer review report

Title: Maintained imbalance of triglycerides, apolipoproteins, energy metabolites and cytokines in long-term COVID-19 syndrome (LTCS) patients

version: 1

Referee: Paola Turano

Institution: University of Florence

email: turano@cerm.unifi.it

ORCID iD: 0000-0002-7683-8614

General assessment

This is an integrated study reporting NMR-based metabolomics data and flow cytometry-based cytokine in the blood of 125 individuals (healthy controls (HC; n=73), COVID-19-recovered (n=12), COVID-19 acute (n=7) and LTCS (n=33)).

The main goal appears to be that of demonstrating alterations in the metabolome and immune markers of patients with long COVID. This condition is defined as the continuation or development of new symptoms 3 months after the initial SARS-CoV-2 infection, with these symptoms lasting for at least 2 months with no other explanation.

As admitted by the authors, the 4 groups are very unbalanced in terms of numbers of enrolled subjects; moreover, all numbers are low but those in the recovered groups and even more in the acute phase are extremely low. Therefore, the only reliable comparison appears to be that between HC and LTCS. And this is a pity because the most important comparison to define the signature associated with long-COVID symptoms would have been the one between recovered and LTCS subjects.

Another problem is that there is no information on the status of the LTCS before infection nor during the acute phase. This, combined with the low number of individuals, does not allow to draw a real trajectory of the alterations during the observed time line. It is therefore difficult to be 100% sure that alterations in certain metabolites of lipoproteins are a consequence of LTCS or instead intrinsic characteristics of a group of individual that make them more prone to develop LTCS.

These critical aspects have nothing to do with the experimental approach, which is powerful and carefully performed. Unfortunately, the available cohort is not the best to achieve the goal of a molecular characterization of LTCS.

In any case the present manuscript provides useful hints to be further investigated in future studies and therefore might deserve publication.

Essential revisions that are required to verify the manuscript

If it were possible to enlarge the cohort of patients, confirming the observed trends, this would lead to a significant improvement in the impact of the work. But I understand the practical difficulties in achieving this goal.

Decision

Verified with reservations: The content is academically sound but has shortcomings that could be improved by further studies and/or minor revisions.

Peer review report

Title: Maintained imbalance of triglycerides, apolipoproteins, energy metabolites and cytokines in long-term COVID-19 syndrome (LTCS) patients

version: 1

Referee: Christopher Gerner

Institution: University of Vienna

email: Christopher.gerner@univie.ac.at

ORCID iD: 0000-0003-4964-0642

General assessment

The manuscript of Berezhnoy et al. is a well written report regarding metabolomics and cytokines in long term COVID-19 syndrome patients. The applied methodology is of some interest and I cannot detect methodological errors. However, I have some concerns which need to be addressed before the manuscript should sent for journal publication.

Most importantly, the manuscript did not adhere to good scientific practice regarding literature research. There are papers about LTCS patients published more than a year ago following highly similar research strategies with quite similar results. It is not sufficient to cite them in subordinate clauses in the Discussion, they need to be cited in the Introduction accordingly, as well when discussing the results. Indeed, relevant similarities in the results would deserve some discussion, such as the dysregulation of cytokines in LTCS.

Another weakness is the structure of data interpretation. It is mentioned in the Introduction that several cell types were reported to show altered metabolism after a COVID-19 infection. I cannot see how plasma analysis should allow to verify such observations as it represents a mixture of all cell types in the body. This obvious challenge regarding data interpretation should be addressed.

This is in line with another weak aspect. The numerous findings a reported without a clear structure regarding potential pathomechanisms. As such, the manuscript is sometimes not easy to read.

To sum up, the manuscript reports interesting analysis results largely corroborating previous results, which deserved publication after some essential improvements.

Essential revisions that are required to verify the manuscript

An improved appreciation of existing literature is essential, as well as an improved data interpretation.

Other suggestions to improve the manuscript

A discussion of the pros and cons of NMR-based metabolomics in contrast to other techniques would be helpful.

Decision

Verified with reservations: The content is academically sound but has shortcomings that could be improved by further studies and/or minor revisions.

Reviewer #1 (Public Review):

The authors evaluate a number of stochastic algorithms for the generation of wiring diagrams between neurons by comparing their results to tentative connectivity measured in cell cultures derived from embryonic rodent cortices. They find the best match for algorithms that include a term of homophily, i.e. preference for connections between pairs that connect to an overlapping set of neurons. The trend becomes stronger, the older the culture is (more days in vitro).

From there, they branch off to a set of related results: First, that connectivity states reached by the optimal algorithm along the way are similar to connectivity in younger cultures (fewer days in vitro). Second, that connectivity in a more densely packed network (higher plating density) differs only in terms of shorter-range connectivity and even higher clustering, while other topological parameters are conserved. Third, blocking inhibition results in more unstructured functional connectivity. Fourth, results can be replicated to some degree in cultures of human neurons, but it depends on the type of cell.

The culturing and recording methods are strong and impressive. The connectivity derivation methods use established algorithms but come with one important caveat, in that they are purely based on correlation, which can lead to the addition of non-structurally present edges. While this focus on "functional connectivity" is an established method, it is important to consider how this affects the main results. One main way in which functional connectivity is likely to differ from the structural one is the presence of edges between neurons sharing common innervation, as this is likely to synchronize their spiking. As they share innervation from the same set of neurons, this type of edge is placed in accordance with a homophilic principle. In other words, this is not merely an algorithmic inaccuracy, but a potential bias directly related to the main point of the manuscript. This is not invalidating the main point, which the authors clearly state to be about the correlational, functional connectivity (and using that is established in the field). But it becomes relevant when in conclusion the functional connectivity is implicitly or explicitly equated with the structural one. Specifically, considering a long-range connection to be more costly implies an actual, structural connection to be present. Speculating that the algorithm reveals developmental principles of network formation implies that it is the actual axons and synapses forming and developing. The term "wiring" also implies structural rather than functional connectivity. One should carefully consider what the distinction means for conclusions and interpretation of results.

The main finding is that out of 13 tested algorithms to model the measured functional connectivity, one based on homophilic attachment works best, recreating with a simple principle the distributions of various topological parameters.<br /> First, I want to clear up a potential misunderstanding caused by the naming the authors chose for the four groups of generative algorithms: While the ones labelled "clustering" are based on the clustering coefficient, they do not necessarily lead to a large value of that measure nor are they really based on the idea that connectivity is clustered. Instead, the "homophilic" ones are a form of maximizing the measure (but balanced by the distance term). To be clear, their naming is not wrong, nor needs to be changed, but it can lead to misunderstandings that I wanted to clear up. Also, this means that the principle of "homophilic wiring" is a confirmation of previous findings that neuronal connectivity features increased values of the clustering coefficient. What is novel is the valuable finding that the principle also leads to matching other topological network parameters.

The main finding is based on essentially fitting a network generation algorithm by minimizing an energy function. As such, we must consider the possibility of overfitting. Here the authors provide additional validation by using measures that were not considered in the fitting (Fig 5, to a lesser degree Fig 3e), increasing the strength of the results. Also, for a given generative algorithm, only 2 wiring parameters were optimized. However, with respect to this, I was left with the impression that a different set of them was optimized for every single in-vitro network (e.g. n=6 sets for the sparse PC networks; though this was not precisely explained, I base this on the presence of distributions of wiring parameters in Fig 6c). The results would be stronger if a single set could be found for a given type of cell culture, especially if we are supposed to consider the main finding to be a universal wiring principle. At least report and discuss their variability.

Next, the strength of the finding depends on the strengths of the alternatives considered. Here, the authors selected a reasonably high number of twelve alternatives. The "degree" family places connections between nodes that are already highly connected, implementing a form of rich-club principle, which has been repeatedly found in brain networks. However, I do not understand the motivation for the "clustering" family. As mentioned above, they do not serve to increase the measure of the clustering coefficient, as the pair is likely not part of the same cluster. As inspiration, "Collective dynamics of 'small-world' networks" is cited, but I do not see the relation to the algorithm or results presented in that study. A clearly explained motivation for the alternatives (and maybe for the individual algorithms, not just the larger families) would strengthen the result. 

Related to the interpretation of results, as they are presented in Fig3a, bottom left: What data points exactly go into each colored box? Specifically, into the purple box? What exactly is meant by "top performing networks across the main categories" mean? Compared with Supp Fig S4, it seems as if the authors do not select the best model out of a family and instead pool the various models that are part of the same family, albeit each with their optimized gamma and eta. Otherwise, the purple box at DIV14 in Fig3 would be identical to "degree average" at DIV14 in S4. If true, I find this problematic, as visually, the performance of one family is made to look weaker by including weak-performing models in it. I am sure one could formulate a weak-performing homophily-based rule that drives the red box up. If such pooling is done for the statistical tests in Supp Tables 3-7, this is outright misleading! (for some cases "degree average" seems not significantly worse than the homophily rules).

The next finding is related to the development of connectivity over the days in vitro. Here, the authors compare the connectivity states the network model goes through as the algorithm builds it up, to connectivity in-vitro in younger cultures. They find comparable trajectories for two global topological parameters. <br /> Here, once again it is a strength that the authors considered additional parameters outside the ones used in fitting. However, it should be noted that the values for "global efficiency" at DIV14 (the very network that was optimized!) are clearly below the biological values plotted, weakening the generality of the previous result. This is never discussed in the text.

The conclusion of the authors in this part derives from values of modularity decreasing over time in both model and data, and global efficiency increasing. The main impact of "time" in this context is the addition of more connections, and increasing edge density. And there is a known dependency between edge density and the bounds of global efficiency. I am not convinced the result is meaningful for the conclusion in this state. If one were to work backwards from the DIV14 model, randomly removing connections (with uniform probabilities): Would the resulting trajectory match DIV12, DIV10, and DIV7 equally well? If so, the trajectory resulting from the "matching" algorithm is not meaningful.

Further, the conclusion of the authors implies that connections in the cultures are formed as in the algorithm: one after another over time without pruning. This could be simply tested: How stable are individual connections in vitro over time (between DIV)? 

The next finding is that at higher densities, the connections formed by the neurons still have very comparable structures, only differing in clustering and range; and that the same generative algorithm is optimal for modelling them. I think in its current state, the correlation analysis in Fig. 4a supports this conclusion only partially: Most of these correlations are not surprising. Shortest path lengths feature heavily in the calculation of small worldness and efficiency (in one case admittedly the inverse). Also for example network density has known relations with other measures. The analysis would be stronger if that was taken into account, for example showing how correlations deviate from the ones expected in an Erdos-Renyi-type network of equal sizes.

Yet, overall the results are supported by the depicted data and model fits in Supp. Fig S7. With the caveat that some of the numerical values depicted seem off: <br /> What are the units for efficiency? Why do they take values up to 2000? Should be < 1 as in 4b. Also, what is "strength"? I assume it's supposed to be the value of STTC, but that's not supposed to be >1. Is it the sum over the edges? But at a total degree of around 40, this would imply an average STTC almost three times higher than what's reported in Fig 1i. Also, why is the degree around 40, but between 1000 and 1500 in Fig S2? <br /> Finally, it should be mentioned that "degree average" seems (from the boxplot) to work equally well.

Further, the conclusion of the "matching" algorithm equally fitting both cases would be stronger if we were informed about the wiring parameters (η and γ) resulting in both cases. That way we could understand: Is it the same algorithm fitting both cases or very different variants of the same? It is especially crucial here, because the η and γ parameters determine the interplay between the distance- and topology-dependent terms, and this is the one case where a very different set of pairwise distances (due to higher density) are tested. Does it really generalize to these new conditions?

Conversely, the results relating to GABAa blocking show a case where the distances are comparable, but the topology of functional connectivity is very different. (Here again, the contrast between structural and functional connectivity could be made a bit clearer. How is correlational detection of connections affected by "bursty" activity?) The reduction in tentative inhibition following the application of the block is convincing.

The main finding is that despite of very different connectivities, the "matching" algorithm still holds best. This is adequately supported by applying the previous analyses to this case as well. <br /> The authors then interpret the differences between blocked and control by inspection of the η and γ parameters, finding that the relative impact of the distance-based term is likely reduced, as a lower (less negative) exponent would lead to more equal values for different distances. This is a good example of inspecting the internals of a generative algorithm to understand the modeled system and is confirmed by longer edge lengths in Supp Fig. S12C.

The authors further inspect the wiring probabilities used internally at each step of the algorithm and compare across conditions. They conclude from differences in the distribution of P_ij values that the GABAa-blocked network had a "more random" topology with "less specific" wiring. This is the opposite of the conclusion I would draw, given the depicted data. This may be partially because the authors do not clearly define their concept of "random" vs. "specific". I understand it to be the following: At each time step, one unconnected pair is randomly picked and connected, with probabilities proportional to P_ij, as in Akarca et al., 2021; "randomness" then refers to the entropy of that process. In that case, the "most random" or highest entropy case is given by uniform P_ij values, which would be depicted as a delta peak at 1 / n_pairs in the present plot. A flatter distribution would indicate more randomness if it was the distribution of P_ij over pairs of neurons (x-axis: pairs; y-axis P_ij). The conclusion should be clarified by the use of a mathematical definition and supported by data using that definition.

Next, the methods are repeated for various cultures of human neurons. I have no specific observations there.

In summary, while I think the most important methods are sound, and the main conclusions (reflected in the title of the paper) are supported, the analysis of more specific cases (everything from Fig 3e onwards, except for Fig 5) requires more work as in the current state their conclusions are not adequately supported.

Reviewer #2 (Public Review):

This work presents an exhaustive study of inferred functional networks from in vitro neuronal cultures across several modalities: primary rat cultures (with varying densities and longitudinal points), and human iPSC monolayers from different cell types and organoids. The authors first estimated the functional connectivity of these networks from their spontaneous activity (recorded with high-density MEAs) and then tried to find which wiring principle could better explain the observations. By deploying generative network models (with 13 different wiring principles) they observed that models with homophilic wiring principles were systematically outperforming the other ones. This proposes a universal rule for how neurons connect, which is that they tend to connect with neurons that have many common neighbors.

One of the major strengths of this study is its scope. They analyzed sparse and dense primary rat cultures at 4 different time points during development (from 7 to 28 DIV in total) as well as with the pharmacological application of GABAA blockers; 3 different cell lines: spinal-cord motor neurons, dopaminergic neurons, and glutamatergic neurons, and organoid slices. However, the big scope of this study is also one of its weaknesses, the techniques presented here to analyze the data are used inconsistently; for some preparations, there's much more detail than in others, and the constant jump between preparations and methodologies makes the findings hard to follow.

Similarly, the number of samples used in some preparations (ranging from 6 to 12) appears to be insufficient, since the study relies on multiple comparisons across the results from 13 different generative models. In many cases, it is not possible to identify which results are significant and which aren't. Most of the methodology used in this study has been used before in the context of the human connectome project (Betzel et al, Neuroimage 2016); in there they used data from 380 total participants, which made the comparisons across all the different models much more robust.

Most previous research with generative models for neural connectivity has focused on structural connectivity. In there, the link between wiring principles, energetic costs, and network topology can be made. This study, however, focuses on functional connectivity (measured by the spike time tiling coefficient), where the link between these quantities is unclear. Although the authors highlight this point in the manuscript, the constant comparisons to structural connectivity concepts and studies often lead to confusion. A clear example of this is the section where the authors explore the effect of chronic GABAA receptor blockade. It is unclear whether the authors are trying to claim that this protocol alters the development of the structural network or only the dynamics. The former could have needed additional controls.

The authors have been diligent and thorough with their statistical testing and their claims are commensurate with that. However, given the large number of different types of results and tests being presented, it is often difficult to find the corresponding explanation in the methods.

This is valuable work for experimental and computational neuroscientists studying the development of neuronal networks and the link between structural and functional connectivity. It would greatly benefit from homogenizing the results, methods, and statistics across the different experimental preparations. The conceptual similarities and differences between structural and functional wiring principles also need to be emphasized.

Reviewer #1 (Public Review):

This work deals with courtship behaviour in mice. Authors try to identify the acoustic features that influence the attractivity level of male courtship songs to females. Courtship songs are made of sequences of short ultrasound syllables emitted at a rate of 7-10Hz. Authors manipulated these syllables by changing either the spectrotemporal content of each syllable or the intersyllable intervals. The authors found that it was only when sequences of syllables were irregular (with highly variable intersyllable intervals) that the female was less attracted to the song. The data, therefore, brings evidence that the acoustic features of syllables account less than the song's temporal regularity for the attractivity of courtship songs. The authors suggest that temporal regularity of syllable emission, building on breathing patterns, could reflect male fitness. They also suggest that temporal regularity could be an acoustic cue compressing the complex acoustic information carried by songs.

Strengths:

The study is well-written, very straightforward, and easy to follow. Behavioral tasks are well-designed and many tests, on a large enough set of animals have been done to support the conclusions. Results are clearly presented and provide enough details to see individual points. The discussion makes interesting connections between syllable rhythms and animals' fitness or brain rhythms.

Weaknesses:

Although the study is easy to understand and provides interesting results, the data analysis remains incomplete, and the interpretation of results is not cautious enough.

For instance, Fig. 2 shows a preference for song playback but we cannot determine if it is a general preference for a sound or a specific preference for male songs because only the difference between the presence of song or silence is tested. I acknowledge that the authors did not overstate their results, but the experimental design is incomplete and hard to interpret in that respect. For instance, the expression "preferential approach to song" is ambiguous.

There is no analysis of individual preference across tests and we might have the feeling that the effect shown mostly depends on the preference of only a few animals. Indeed, it seems that roughly one-third of animals showed a strong preference for the intact song while another third showed a strong preference for the modified song, whatever the modification. A few animals are therefore "swing voters". It would have been interesting, if not pertinent, to have a deeper analysis of the behavior of these later animals. Do they choose less (i.e. spend less time close to speakers) or do they swing from one corner to another? What about the animals which always chose the modified song? Are these animals that already showed a weak or strong preference for silence, therefore showing they were not comfortable with the songs played? There is no discussion of these aspects either.

Also, on page 11, it is written "female listeners perceptually compress the high sensory dimensionality of male songs by selectively monitoring a reduced subset of meaningful acoustic features in isolation." This statement or hypothesis is questionable. After all, if someone would change the inter-syllable intervals in human speech, that would become cryptic or at least annoying for the listener. Humans would definitely prefer normal speech. Is this because we compress acoustic features? Not really. It is likely that this modified speech just differs too much from the set of parameters typically encountered and therefore understood/interpreted while learning a language in childhood. Thus, the hypothesis here is rather to determine, for a given acoustic feature, if there is a range within which the perception of the message carried by the song (courtship) is maintained. Interpretation of "compressed acoustic features" with regards to animals' preference seems an overinterpretation. Same remark at the end of the conclusion.

Reviewer #2 (Public Review):

In the present manuscript, Perrodin et al. investigated which properties of ultrasonic vocalizations determine their attractiveness for female mice. They collected a set of male courtship vocalizations and compared their attractiveness for female mice against a number of conditions, including silence, and a number of modified sequences.

The study has a clear design and used insightful modifications on the vocalization sequences, which allow the present results to be linked to previous results. The most interesting outcome of the study is that female mice prefer regularly timed sequences of vocalizations over less regularly timed sequences. This result is novel and adds to our understanding of the determinants of social communication between mice. Overall the study is likely underpowered, which was, however, hard to assess as animal numbers were largely not reported for the individual tests, and statistical analysis was carried out on the level of sessions only.

The study has a very good discussion embedding the current results with the previous literature, although the discussion steps beyond the results in a few respects, in particular when trying to determine the underlying reasons for the preference for regularly spaced sequences.

Methodologically the study is carried out at the appropriate level, although some improvements could be made to the experimental apparatus to avoid reflections.

The study will likely have a substantial impact on the field of mouse communication because the regularity of spacing has not been a focus of previous research. In addition, the confirmation that a lot of other modifications are less determining for the attractiveness of the vocalizations provides solid data on which to base future work.

Reviewer #1 (Public Review):

Tippett et al present whole cell and proteoliposome transport data showing unequivocally that purified recombinant SLC26A6 reconstituted in proteoliposomes mediates electroneutral chloride/bicarbonate exchange, as well as coupled chloride/oxalate exchange unassociated with detectable current. Both functions contrast with the uncoupled chloride conductance mediated by SLC26A9. The authors also present a novel cryo-EM structure of full-length human SLC26A6 chloride/anion exchanger. As part of the structure, they offer the first partial view of the STAS domain previously predicted to be unstructured. They further define a single Arg residue of the SLC26A6 transmembrane domain required for coupled exchange, mutation of which yields apparently uncoupled electrogenic chloride transport mechanistically resembling that of SLC26A9, although of lower magnitude. The authors further apply to proteoliposomes for the first time a still novel approach to the measurement of bicarbonate transport using a bicarbonate-selective Europium fluorophor. The evidence strongly supports the authors' claims and conclusions, with one exception.

The manuscript has numerous strengths.

As a structural biology contribution, the authors extend the range of SLC26 structures to SLC26A6, comparing it in considerable detail to the published SLC26A9 structure, and presenting for the first time the structure of a portion of the STAS IVS domain of SLC26A6 long considered unstructured.

The authors also apply a remarkably extensive range of creative technical approaches to assess the functional mechanisms of anion transport by SLC26A6, among them the first application of the novel, specific bicarbonate sensor Eu-L1+ to directly assess bicarbonate transport in reconstituted proteoliposomes. The authors also present the first (to this reviewer's knowledge) functional proteoliposome reconstitution of chloride-bicarbonate exchange mediated by an SLC26 protein. They define a residue in surrounding the anion binding pocket which explains part of the difference in anion exchange coupling between SLC26A6 and SLC26A9. In the setting of past conflicting results, the current work also contributes to the weight of previous evidence demonstrating that SLC26A6 mediates electroneutral rather than electrogenic Cl-/HCO3- exchange.

Each of these achievements constitutes a significant advance in our understanding.

The paper has only a few weaknesses. One is an incomplete explanation of the mechanistic determinants of anion exchange coupling in SLC26A6 vs. uncoupled anion transport by SLC26A9. A second minor weakness is the inconsistently repeated conclusion that SLC26A6 mediates strictly coupled chloride/oxalate exchange. The data presented do not measure the stoichiometry of Cl-/oxalate exchange. The AMCA proteoliposome assay documented extracellular oxalate-dependent proteoliposomal anion transport that was most simply interpreted as coupled exchange, whereas no stoichiometric coupled exchange was documented in the AMCA experiments as presented.

Overall, the manuscript represents an important advance in our understanding of the SLC26 protein family and of coupled vs uncoupled carrier-mediated anion transport.

Reviewer #2 (Public Review):

The eleven paralogs of SLC26 proteins in humans exhibit a remarkable range of functional diversity, spanning from slow anion exchangers and fast anion transporters with channel-like properties, to motor proteins found in the cochlear outer hair cells. In this study, the authors investigate human SLC26A6, which functions as a bicarbonate (HCO3-)/chloride (Cl-) and oxalate (C2O42-)/Cl- exchanger, combining cryo-electron microscopy, electrophysiology, and in vitro transport assays. The authors provide compelling evidence to support the idea that SLC26A6's exchange anions at equimolar stoichiometry, leading to the electroneutral and electrogenic transport of HCO3-/ Cl- and C2O42-/Cl-, respectively. Furthermore, the structure of SLC26A6 reveals a close resemblance to the fast, uncoupled Cl- transporter SLC26A9, with the major structural differences observed within the anion binding site. By characterizing an amino acid substitution within the SLC26A6 anion binding site (R404V), the authors also show that the size and charge variance of the binding pocket between the two paralogs could, in part, contribute to the differences in their transport mechanisms.

The strength of this work lies in the reductionist, in vitro approach that the authors took to characterize the transport process of SLC26A6. The authors used and developed an array of functional experiments, including two electrogenic transport assays - a fast kinetic (electrophysiology) and a slow-kinetic (fluorescent-based ACMA) - and two electroneutral transport assays, probing for Cl- (lucigenin) and HCO3- (europium), which are well executed and characterized. The structural data is also of high quality and is the first structure of an SLC26 coupled anion exchanger, providing essential information for clarifying our understanding of the functional diversity between the SLC26 family of proteins.

To my knowledge, the outward-facing conformational state has not been determined for any mammalian SLC26 paralog, which limits the mechanistic interpretation of transport and is a weaker point of this manuscript. However, this is a very minor point.

Reviewer #3 (Public Review):

The mechanistically diverse SLC26 transporters play a variety of physiological roles. The current manuscript establishes the SLC26A6 subtype as electroneutral chloride/bicarbonate exchanges and reports its high-resolution structure with chloride bound.

The claims in this manuscript are all well-supported by the data. Strengths include the comprehensive functional analysis of SLC26A6 in reconstituted liposome vesicles. The authors employ an array of assays, including chloride sensors, a newly developed fluorescent probe for bicarbonate, and assays to detect the electrogenicity of anion exchange. With this assortment of assays, the authors are able to establish the anion selectivity and stoichiometry of SLC26A6. Another strength of the manuscript is the functional comparison with SLC26A9, which permits fast, passive chloride transport, in order to benchmark the SLC26A6 activity. The structural analysis, including the assignment of the chloride binding site, is also convincing. The structural details and the chloride binding site are well-conserved among SLC26s. Finally, the authors present an interesting discussion comparing the structures of SLC26A5, SLC26A6, and SLC26A9, and how the details of the chloride binding site might influence the mechanistic distinctions between these similar transporters.

Reviewer #1 (Public Review):

In this study the authors first perform global knockout of the gene coding for the polarity protein Crumbs 3 (CRB3) in the mouse and show that this leads to perinatal lethality and anopthalmia. Next, they create a conditional knockout mouse specifically lacking CRB3 in mammary gland epithelial cells and show that this leads to ductal epithelial hyperplasia, impaired branching morphogenesis and tumorigenesis. To study the mechanism by which CRB3 affects mammary epithelial development and morphogenesis, the authors turn to MCF10A cells and find that CRB3 shRNA-mediated knockdown in these cells impairs their ability to form properly polarized acini in 3D cultures. Furthermore, they find that MCF10A cells lacking CRB3 display reduced primary ciliation frequency compared to control cells, which is in agreement with previous studies implicating CRB3 in primary cilia biogenesis. Using a combination of biochemical, molecular- and imaging approaches the authors then provid evidence indicating that CRB3 promotes ciliogenesis by mediating Rab11-dependent recruitment of gamma tubulin ring complex component GCP6 to the centrosome/ciliary base, and they also show that CRB3 itself is localized to the base of primary cilia. Finally, to assess the functional consequences of CRB3 loss on ciliary signaling function, the authors analyze the effect of CRB3 loss on Hedgehog and Wnt signaling using cell-based assays or a mouse model.

Overall, the described findings are interesting and in agreement with previous studies showing an involvement of CRB3 in epithelial cell biology, tumorigenesis and ciliogenesis. The results showing a role for CRB3 in mammary epithelial development and morphogenesis in vivo seem convincing. However, a major weakness of this study is that quantitative analysis of several key results is either lacking, not done appropriately, or is incompletely described. In addition, some of the cell-based experiments are lacking appropriate controls, and the claim that CRB3 directly binds to Rab11 is not supported by the data provided.

Reviewer #2 (Public Review):

In this work, the authors investigate the role of CRB3 in the formation of the primary cilium both in a mouse model and in human cells. They confirm in a conditional knock-out (KO) mouse model that Crb3 is necessary for the formation of the primary cilium in mammary and renal epithelial tissues and the new-born mice exhibit classical traits of ciliopathies. In the mouse mammary gland, the absence of Crb3 induces hyperplasia and tumorigenesis and in the human mammary tumor cells MCF10A the knock-down (KD) of CBR3 impairs ciliogenesis and the formation of a lumen in 3D-cultures with less apoptosis and spindle orientation defects during cell division.

To determine the subcellular localization of CRB3 the authors have expressed exogenously a GFP-CRB3 in MCF10A and found that this tagged protein localizes in cell-cell junctions and around pericentrin, a centrosome marker, while endogenous CRB3 localizes at the basal body. To dissect the molecular role of CRB3 the authors have performed proteomic analyses after a pull-down assay with the exogenous tagged-CRB3 and found that CRB3 interacts with Rab11 and is present in the endosomal recycling pathway. CRB3 KD also decreases the interactions between components of the γTuRC complex. In addition, the authors showed that CRB3 interacts with a tagged-Rab11 by its extracellular domain and that CRB3 promotes the interaction between Rab11 and CEP290 while CRB3 KD decreased the co-localization of GCP6 with Rab11 and γTub. Finally, the authors showed that CRB3 depletion cannot activate the Hh pathway as opposed to the Wnt pathway.

Reviewer #1 (Public Review):

In "Striatal ensemble activity in an innate behavior", Minkowicz et al. strive to characterize how the striatum, the primary input nucleus of the basal ganglia, represents grooming. Here, grooming is used as a paradigmatic habitual behavior. The pose dynamics of grooming are stereotyped: mice perform it spontaneously and prior work has shown that it is both represented and controlled by the striatum.

The manuscript presents a valuable contribution to the field by shedding light on how ensembles of neurons encode this innate behavior. Additionally, the use of supervised machine learning allowed the authors to collect and precisely align a large number of grooming repetitions, which enabled most of their downstream analysis.

I found the paper to be well-written and the conclusions are mostly well-supported. However, some of the data analysis was a bit opaque, and some more detail and reanalysis could substantially strengthen the authors' claims.

1) The authors identified grooming bouts using empirically defined thresholds and manual tweaking. Next, the boundaries of grooming were used for trial alignment and linear time warping. This is a completely sensible approach; however, in using only the boundaries of grooming episodes, the dynamics of grooming bouts are ignored. I am particularly concerned that pose dynamics of grooming bouts are most stereotyped at the boundaries (e.g. they always begin and end with specific paw movements). To play devil's advocate, if the striatum encodes pose dynamics and not boundaries and pose dynamics are noisy between the beginning and end of these bouts (either due to the dynamics of the behavior or how it was identified), then a "boundary-like" representation may emerge in the average. I strongly recommend re-running a subset of the analysis after accounting for variability in grooming dynamics. A simple thing to try would be to further cluster grooming bouts using 3D keypoint trajectories. Another would be to warp grooming bouts in a manner that accounts for keypoint trajectories (e.g. DTW or other recent time-warping variants).

2) The authors should consider if the correlation to grooming is due to (at least in part) a correlation with another aspect of movement, e.g. overall velocity, acceleration, height, or angular velocity. This should be straightforward to analyze with the current dataset. To start, I would simply take the velocity and acceleration of the mouse's centroid (head and body could be considered separately). Next, look at the correlation with DLS spiking. If a clear relationship emerges, then check to see how velocity (or another variable) maps onto grooming. It may be that DLS neurons appear to encode the boundaries of grooming when they (at least partially) encode other variables.

3) The ensemble analysis is potentially critical to our understanding of SPNs. Figure 4A suggests that ensembles encode grooming with a probabilistic code - ensembles appear to be engaged for a small number of grooming bouts in the session. First, a basic question is what is the probability a given ensemble is activated during grooming? Second, the more complex question is whether there is an explanation for why one ensemble is engaged for some trials and not others? Related to point 2, I wonder if another aspect of behavior - e.g. vigor, duration, or speed - determines this. I suggest some analysis to at least rule out some simple explanations.

Reviewer #2 (Public Review):

The manuscript by Minkowicz et al., investigates the presence of neuronal ensembles in the striatum that may encode grooming (as a model of a naturalistic behavior). They implemented a semi-automated detection of grooming, and by recording populations of striatal cells they show that individual neurons in the striatum contain activity modulations around the start, end, or during grooming. Then using this activity they identify ensembles of cells in individual sessions/animals at the start, end or during grooming.

The behavioral tracking and recordings are remarkable, the manuscript is clearly written and the finding mostly sound with the proposed conclusions, providing original findings in the field. Nonetheless some points are raised that need further clarification

1. When claiming that the findings show encoding of transitions into or out of grooming (and duration of grooming) one could expect to see specific regressions between the neuronal activity (of individual cells or ensembles) and the parameters mentioned besides the analysis shown in figure 3 and 5.<br /> 2. Was the detection of ensembles presented in figure 4 sensible to use less than 5 seconds before/after grooming. I am thinking that 5 seconds are times that could contain behaviors that may have their own ensembles. Why 5 seconds?<br /> 3. According to Figure 2-figure supplement 1. The recordings were performed covering the lateral and in some cases the central part of the striatum. Shall it be specified along the text where the specific recordings come from?

Reviewer #1 (Public Review):

In this manuscript by Douglas et al, the investigative team seeks to identify Staphylococcus aureus genes (and associated polymorphisms) that confer altered susceptibility to human serum, with the hypothesis that such genes might contribute to the propensity of a strain to cause bacteremia, invasive disease, and/or death. Using an innovative GWAS-like approach applied to a bank of over 300 well-characterized clinical S. aureus isolates, the authors discover SNPs in seven different staphylococcal genes that confer increased survival in the setting of serum exposure. The authors then mainly focus on one gene, tcaA, and illustrate a potential mechanism whereby modification of peptidoglycan structure and WTA display leads to altered susceptibility to serum, serum-derived antimicrobial compounds, and antibiotics. One particularly significant finding is that the identified tcaA SNP is significantly associated with patient mortality, in that patients infected with the SNP bearing isolate are less likely to die from infection. It is therefore hypothesized that this SNP represents an adaptive mutation that promotes serum survival while decreasing virulence and host mortality. In a murine model of infection, the strain bearing the WT allele of tcaA is significantly more virulent than the tcaA mutant, suggesting that the role of tcaA in bacteremia is infection-phase dependent.

This manuscript has many strengths. The triangulation of genomic analysis, patient outcomes data, and in vitro and in vivo mechanistic testing adds to the significance of the findings in terms of human disease. Testing the impact of mutating tcaA in multiple staphylococcal lineages and backgrounds also increases the rigor of the study. The identification of bacterial loci that impact susceptibility to both host antimicrobial compounds and commonly used antibiotics is also a strength of this work, given the evolutionary and treatment implications for such genes.

One moderate weakness is that the impact of the identified SNP in tcaA is only tested in some of the assays, whereas the majority of the testing is performed with a whole gene knockout. Additionally, for some experiments, rigor is lacking in that statistical measures are not deployed to support the conclusions of biologically meaningful changes based on data with very modest differences between groups. In some cases this results in more speculative conclusions that will require further testing to validate. Finally, there are instances of inter-experiment variability that require further explanation. All in all, this is an exciting manuscript that will be of interest to the broader research communities focused on staphylococcal pathogenesis, bacterial evolution, and host-pathogen interactions, as well as to clinicians who care for patients with invasive staphylococcal infection.

Reviewer #2 (Public Review):

The authors embarked on a study to identify SNPs in clinical isolates of S. aureus that influence sensitivity to serum killing. Through a phenotypic screen of 300 previously sequenced S. aureus bacteremia (SAB) isolates, they identified ~40 SNPs causing altered serum survival. The remainder of the study focuses of tcaA, a gene with unknown function. They show that when tcaA is disrupted, it results in increased resistance to glycopeptides and antimicrobial components of human serum.

They perform an elegant series of experiments demonstrating how a tcaA knockout is more resistant to killing by whole serum. arachadonic acid, LL-37 and HNP-1. They provide compelling evidence that in the absence of tcaA resistance to arachidonic acid is mediated through release of wall teichoic acids from the cell wall, which acts as a decoy and sequesters the fatty acid.

Similarly, they suggest that resistance to cationic antimicrobial peptides is through alteration of the net charge of the cell wall due to loss of negatively charged WTAs based on reduced cytochrome C binding.

They continue to show that tcaA is induced in the presence of human serum, which causes increased resistance to the glycopeptide teichplanin.

They propose that tcaA disruption causes altered cell wall structure based on morphologic changes on TEM and increased sensitivity to lysostaphin and increased autolysis via triton x-100 assay.

5, Finally, they propose that tcaA influences mortality in SAB based on raw differences in 30-day morality. Interestingly they do decreased fitness during murine bacteremia model compared to wild-type.

Strengths:

1. The manuscript is well-written and easy to follow<br /> 2. The identification of SNPs leading to altered serum killing is convincing and valuable data<br /> 3. The mechanism for tcaA-mediated resistance to arachadonic acid and AMPs is compelling and novel<br /> 4. The murine infection data demonstrating that tcaA mutants exhibit reduced virulence is important data

Weaknesses:

1. Some of the conclusions are not supported by the data shown (either missing or incomplete)<br /> 2. The authors conclude that tcaA mutants show reduced peptidoglycan crosslinking. This conclusion is based on qualitative TEM images and increased sensitivity to lysostaphyin/autolysis. While these data are suggestive. it is difficult to draw such a conclusion without analysis of the cell wall by LC-MS (such as http://doi.org/10.1371/journal.ppat.1009468).<br /> 3. The authors conclude "TcaA contributes to increased disease severity in mice and humans". While it seems biologically plausible that a polymorphism known to increase glycopeptide MIC affects mortality, the human data presented is based on raw 30-day mortality numbers. It is misleading to make the association with mortality without adjusting for confounding variables known to influence mortality in SAB (e.g. age, comorbidities, presence of sepsis, endocarditis, duration of bacteremia). Also, with just 12 patients in the SNP group, this is likely underpowered to detect any difference.

Overall, I think this is a good submission and the majority of their conclusions are supported by the data. The mechanism behind the clinically relevant tcaA mutation is important, given its known role in glycopeptide resistance and therefore likely clinical outcomes. This manuscript would benefit with the inclusion of some additional experiments to help support their finding.

Reviewer #3 (Public Review):

In this manuscript by Douglas et al., the authors used a functional genomics approach to understand how Staphylococcus aureus survives in the bloodstream to cause bacteraemia. They identified seven novel genes that affect serum survival. The study focused on tcaA, a gene associated with resistance to the antibiotic teicoplanin and is activated when exposed to serum and plays a role in producing a critical virulence factor called wall teichoic acids (WTA) in the cell envelope. This protein affects the bacteria's sensitivity to cell wall attacking agents, human defense fatty acids, and antibiotics, as well as autolytic activity and lysostaphin sensitivity. The data in this study suggested that TcaA play a role in the ligation or retention of WTA within the cell wall. However, more work is needed to clarify that part. Interestingly, despite making the bacteria more vulnerable to serum killing, tcaA contributes to S. aureus virulence by altering the cell wall architecture, as demonstrated by the wild type strain outcompeting the tcaA mutant in a Mouse Co-infection model. The study raises an important point that TcaA in S. aureus may represent a system balancing two scenarios: it makes the bacteria more susceptible to serum killing, potentially limiting bacteraemia and providing long-term benefits between hosts; however, once established in the bloodstream, the bacteria survive and thrive, causing successful bacteraemia, as per the short-sighted evolution of virulence hypothesis. This duality highlights the complex interplay between within-host and between-host fitness in bacterial evolution. I strongly suggest creating a graphical abstract to illustrate the complex relationship between within-host and between-host fitness scenarios involving TcaA. Having this visual representation in the discussion will enhance comprehension and provide a concise summary of the complex system for the reader.

In this manuscript, the authors achieved their aims, and the results support their conclusions. This work will be fundamental for understanding this complex system and for developing novel therapeutics and vaccines for S. aureus.

Reviewer #1 (Public Review):

The manuscript by Hussein et al. uses cryoEM structure, microscale thermophoresis (MST), and molecular dynamics simulations (conventional and CpHMD) to unravel the Zn2+ and proton role in the function of the Cation Diffusion Facilitator YiiP. First, they generate mutants that abolish each of the three Zn2+ models to study the role of each of them separately, both structurally and functionally. Next, they used a Monte Carlo approach refining the CpHMD data with the MST points to establish the Zn2+ or proton binding state depending on the pH. That predicted a stoichiometry of one Zn2+ to 2 or 3 protons (1:3 under lower pH values). Finally, they proposed a mechanism that involves first the binding of Zn2+ to one low-affinity site and then, after the Zn2+ migrates to the highest affinity site in the transmembrane portion of the protein. The lack of Zn2+ in the low-affinity site might induce occlusion of the transporter.

The manuscript is well-written it is of interest to the field of Cation Facilitator Transporters. It is also an excellent example of a combination of different techniques to obtain relevant information on the mechanism of action of a transporter.

I have only a few comments that might need clarification from the authors:

- If the unbinding of Zn2+ to site B triggers the occlusion (and maybe the OF state) and the external pH does not affect that binding, how is it prevented from being always bound to Zn2+ and thus occluded also while it should be transporting protons (B to C panels in Figure 5)? Are there some other factors that I am missing?<br /> - I am not an expert on experiments, but the results for mutants that abolish site C are difficult to understand. For D287A/H263A, the SEC columns data suggest a population of higher oligomers. Still, for the D70A/D287A/H263A and D51A/D287A/H263A, they showed a native dimer. I understand your suggestion that the Fab induces the domain swap, but how do you explain the double mutant SEC column result? Please elaborate.<br /> - Since in the D287A mutant, you are disrupting the preferred tetrahedral coordination of Zn2+, but it still binds, do you observe any waters that compensate for the missing aspartate? Maybe in the MD simulations?

Reviewer #2 (Public Review):

In this work, the authors reported cryo-EM structures of four types of zinc-binding site mutants of a bacterial Zn2+/H+ antiporter YiiP, and proposed distinct structural/functional roles of each of the binding sites in the intramolecular Zn2+ relay and the integrity of the homodimeric structure of YiiP. MST analysis using the mutants with a single Zn2+-binding site at different pH further clarified the pH dependence of Zn2+ binding affinity of each site. Moreover, the inverse Multibind approach refined the CpHMD pKa values of the key Zn2+-binding residues so that they agreed with the MST data. Consequently, energetic coupling of Zn2+ export to the proton-motive force has been suggested. These findings definitely provide new mechanistic insight into this Zn2+/H+ antiporter.

Regrettably, the resolutions of the cryo-EM structures presented in this work are, overall, not high enough to describe detailed structure of some specific regions including the Zn2+-binding sites, and the density is missing for some important regions including the kinked segment of TM5. Further attempts toward higher resolution cryo-EM maps would be beneficial to corroborate their conclusions. Additionally, it may, in a sense, appear that the MD simulations have been carried out forcibly so that the outcomes are compatible with or nicely explain the experimental data. Although this is not unusual or unacceptable, I am concerned that the determined pKa values of some residues, especially of Asp residues at Site A, are unusually high. These outcomes seem to need careful interpretation and discussion.

Reviewer #3 (Public Review):

This contribution focuses on the zinc(II) transporter YiiP, a widely used model system of the Cation Diffusion Facilitator (CDF) superfamily. CDF proteins function as dimers and are typically involved in the maintenance of homeostasis of transition metal ions in organisms from all kingdoms of life. The system investigated here, YiiP, is a prokaryotic zinc(II)/H+ antiporter that exports zinc(II) ions from the cytosol. The authors addressed multiple crucial questions related to the functioning of YiiP, namely the specific role of the three zinc(II) binding sites present in each protomer, the zinc(II):H+ stoichiometry of antiport, and the impact of protonation on the transport process. Clarity on all these aspects is required to reach a thorough understanding of the transport cycle.

The experimental approach implemented in this work consisted of a combination of site-directed mutagenesis, high-quality 3D structural determination by cryoEM, microscale electrophoresis, thermodynamic modeling and molecular dynamics. The mutants generated in this work removed one (for the structural characterization) or two (for microscale electrophoresis) of the three zinc(II) binding sites of YiiP, allowing the authors to unravel respectively the structural role of metal binding at each site and the metal affinity of every site individually. pH-dependent measurements and constant pH molecular dynamics simulations, together with the metal affinity data, provided a detailed per-site overview of dissociation constants and Ka values of the metal-binding residues, casting light on the interplay between protonation and metal binding along the transport cycle. This thermodynamic modeling constitutes an important contribution, whose impact is however limited by the lack of an evaluation of whether the measured affinities in the various mutants differ significantly vs the affinities in the WT protein. In particular, this is true for the mutations disrupting site C, which cause a large-scale change in the quaternary structure of the protein.

Overall the authors were successful in providing a model of the transport cycle (Figure 5) that is convincing and well supported by the experimental data. The demonstration that two protomers act asymmetrically during the cycle is another nice achievement of this work, confirming previous suggestions. This novel overview of the cycle can constitute a basis for future work on other systems such as human ZnT transporters, also exploiting a methodological approach for the thermodynamic of these proteins similar to the one deployed here. The latter approach may be applicable also to other superfamilies of metal transporters.

Reviewer #3 (Public Review):

This study sought to identify relations between parameters of the diffusion decision model (DDM) and concentration of the neurotransmitters glutamate and GABA, as measured by magnetic resonance spectroscopy, and to evaluate the possibility that age moderates these relations in a developmental sample spanning middle childhood through young adulthood. The authors find a set of age-by-neurotransmitter concentration interaction effects indicating that lower levels of glutamate and greater levels of GABA in the intraparietal sulcus are related to faster non-decision times (lower values of the Ter parameter of the DDM) for "younger" participants but have the opposite relations in "older" participants (although given the way that the results are reported, the reader has little indication of what age group the terms "younger" and "older" refer to). The authors find similar interaction effects regarding relations between neurotransmitter concentration and connectivity in a visuomotor network and between neurotransmitter concentration and a fluid intelligence test. They then test moderated mediation models to determine whether functional connectivity in the visual-motor network mediates relations between neurotransmitter concentration and Ter, and whether Ter mediates the relation between neurotransmitter concentration and intelligence.

Strengths of the study include the relatively large sample size and the unique combination of brain and behavioral measures. The reported bivariate associations indicate an intriguingly consistent pattern of age-related moderation effects on the relation between neurotransmitter concentrations and several variables relevant to cognition (Ter, visuomotor connectivity, intelligence test scores) that could provide valuable insights to the field about the interplay between neurotransmitters and cognitive processes across development. However, the inferences that can be drawn from this work are seriously limited by an array of conceptual and methodological concerns.

A major conceptual issue is that the study is motivated by the premise that the nondecision time parameter (Ter) of the DDM is a major mechanistic underpinning of intelligence during child and adolescent development. There are several reasons why this premise is not well-supported. Although Ter is sometimes found to have weak correlations with scores on intelligence tests, the clearest pattern of findings across multiple studies is instead that individual differences in intelligence are primarily related to the DDM's drift rate (v) parameter (e.g., Schmiedek et al., 2007; Schulz-Zhecheva et al., 2016; Schubert & Frischkorn, 2020). The authors highlight the earlier finding that Ter mediates the effect of age on intelligence in the Krause et al. (2020) paper, but this paper is of questionable relevance to the current study. Krause et al. (2020) investigated cognitive changes in aging (ages 18-62) which are quite different from the current study's focus on development from middle childhood through young adulthood (ages ~ 7-24). Aging in older adults is known to have limited and task-specific effects on drift rate but strong effects on boundary and Ter whereas development from childhood through young adulthood coincides with the rapid maturation of drift rate (as shown in both prior research and in the current study's supplemental plots). Beyond the relatively weak evidence that Ter is a major contributor to intelligence during development, it is important to note that Ter is a nonspecific "residual" parameter (Schubert & Frischkorn, 2020) that is, theoretically, the summation of a wide array of different processes that are difficult to dissociate (perceptual encoding, visual search, motor responding). Therefore, in contrast to the drift rate and boundary parameters, it is difficult to interpret Ter as indexing a unitary mechanistic process, which is consistent with earlier findings that Ter shows limited evidence of psychometric validity as a task-general trait (Schubert et al., 2016). Finally, it is notable that bivariate tests of DDM parameters' relations with intelligence in the current study's sample (Supplemental File 9) suggest that Ter does not show a robust relation with intelligence, whereas drift rate shows relatively strong relations with intelligence in every group except for "older" individuals, who have likely fully matured and may therefore have less variance in both v and intelligence.

There are several opaque and potentially problematic features of the EZ DDM analysis. The tasks have relatively few trials spread across multiple different conditions within each task and it is unclear whether the DDM parameters were estimated separately in each condition or were estimated from trial-level data that were collapsed across conditions. This is especially concerning for the ANT, which has 96 trials distributed across 12 conditions, or apparently only 8 trials per design cell. Given the relatively low number of trials (both per design cell and overall) it is also concerning that parameter recovery studies do not appear to have been completed to ensure that this number of trials is sufficient to reliably estimate DDM parameters. In addition, accuracy rates and other behavioral summary statistics are not reported for any of the tasks. As ceiling levels of accuracy (i.e., few error RTs) can also cause prevent accurate estimation of parameters, this is another indication that assessing parameter recovery could be critical for inferences in this study.

A broader concern related to the measurement of DDM parameters is that they are each assumed to reflect the same mechanistic process across the three different tasks, but this assumption is not explicitly modeled (e.g., as a latent factor). Although the fact that Ter parameters across all three tasks have similar patterns of results is consistent with this assumption, constructing a latent factor using EFA or CFA would provide an explicit, and critical, test of the assumption. Latent factors formed from DDM parameters across the three tasks would also have several key methodological advantages over single-task measures, including separating variance in the cross-task mechanism of interest from task-specific "method variance", increasing statistical power by improving measurement of the latent mechanism, and reducing the number of multiple comparisons that need to be corrected for. The last two points are particularly critical for this study because it is possible that poor (i.e., single task) measurement and the large number of comparisons that were corrected for may have resulted in a consequential Type II error, such as a failure to detect effects involving DDM parameters other than Ter (drift rate and boundary). Related to these points, it is generally difficult for readers to judge the study's claims about the cross-task relevance of each DDM parameter or about dissociations between the different parameters because no intercorrelations between the parameters (within and between tasks) are reported or discussed.

Although the setup of the bivariate and moderation tests of relations between neurotransmitter concentrations and other variables is generally rigorous, it is concerning that only linear effects of age appear to have been considered. There appears to be clear evidence of nonlinear age-related trends in the scatterplots of parameter values displayed in Supplementary File 2.

The mediation analyses are central to the study's claims, but their results are particularly difficult to draw conclusions from due to several problematic methodological details. First, the confidence interval (CI) used to evaluate the significance of effects in these analyses was a 90% CI, essentially changing the alpha level for these tests from the conventional p<.05 to p<.10. Although this is claimed, in the Methods section, to be justified because these were "follow-up analyses based on the significant results obtained in advance", it is a highly unusual change that appears likely to have been made post hoc. Another apparent post hoc change is also mentioned in Methods: "we additionally removed cases that fell beyond three standard deviations after running the multiple regression models". It is not clear what variable or residual score this statement refers to and it is also not clear why this outlier trimming step was carried out only at the mediation stage, and not prior to the earlier bivariate analyses. The combination of an unusually high effective alpha level and potential post hoc adjustments to researcher degrees of freedom seriously undermines confidence in the mediation results. Even if the statistical hypothesis tasks are taken at face value, though, the evidence for mediation still appears very weak because the standardized effects are small and only significant in one age group (either "older" or "younger" but not both).

A broader challenge for readers is that neither the absolute ages nor the general developmental period of participants is mentioned anywhere in the main text or main plots of the paper. "Younger" and "older" mean very different things when referring to an aging sample (e.g., in the cited Klaus et al. study) versus a developing sample that spans middle childhood through young adulthood. Even if the range of the current study's sample is known, plots that split groups up by plus or minus one SD of age obscure age-related trends because the ages of the subgroups are not known. It may be easier to interpret findings if groups are instead split by neurotransmitter levels and plotted by absolute age.

Reviewer #2 (Public Review):

Zacharopoulos et al. investigated the relationship between MR spectroscopy-detected neurotransmitter concentrations (GABA/glutamate) in the intra-parietal sulcus (IPS) and middle frontal gyrus (MFG), behaviourally measured indices of sensory and cognitive processing, and fMRI measured functional connectivity within the frontoparietal network. They find that increased IPS glutamate concentration is related to poorer visuomotor processing in younger participants and better performance in older participants, while IPS GABA predicts the opposite pattern. They further show that these relationships are mediated by frontoparietal functional connectivity. Finally, they show that IPS GABA and glutamate concentration are related to fluid intelligence and that this relationship is mediated by visuomotor processing and moderated by the developmental stage. These data add to our understanding of the dynamic role of excitatory and inhibitory neurotransmitter systems in cognitive processes throughout development.

Strengths:

The study employs an impressively large cross-sectional, multimodal, dataset, with almost 300 participants ranging from 6 to 18+ years old.

The main finding (i.e., the interaction between GABA/Glu, visuomotor processing, and age) is found across three behavioural tasks and replicated in a second dataset collected 1.5 years after the first.

The authors extensively report the results of the numerous analyses performed in the supplementary material.

Weaknesses:

Pre-registration of experimental and analytical plans should be the norm, e.g., to reduce so-called 'p-hacking'. I am by no means asserting that this behaviour has occurred in the current study; however, it is disappointing that there is no reported pre-registration for such a large-scale study, where the selection and order of analyses (and the subsequent corrections applied) can meaningfully influence the pattern of results.

Many tests were performed in the study using frequentist statistics, and the way the results are reported makes it difficult to discern how distinguishable those that were reported as meaningful are from those that were disregarded.

Insufficient analyses were conducted to describe the relationships between a) GABA and glutamate, b) repeated behavioural measures, and c) test-retest reliability. This reduces the strength of the claims, some of which could be accounted for by simpler, potentially less interesting, explanations.

Reviewer #1 (Public Review):

Zacharopoulos et al. present a multi-modal investigation into the developmental trajectories of cognitive processing, decision-making processing, and visuomotor processing in children and young adults, and attempt to relate them to neuroimaging measures of functional brain connectivity and neurotransmitter concentrations in two distinct brain regions.

Results suggest specific interactions between neurotransmitter concentrations and visuomotor task performance. Interestingly, GABA and Glu levels appear to have different relationships with task performance if the participant group is trichotomized into older, 'mean-age', and younger participants. These findings appear consistent across three different visuomotor processing tasks and replicate well between two time points at which task performance and MRS measures were established for each participant (1.5 years apart). Visuomotor connectivity (assessed with resting-state-fMRI) also showed age-group-specific relationships with neurotransmitter levels. Finally, the authors present evidence that visuomotor processing mediates the relationship between neurochemical levels and scores of fluid intelligence, but only for older participants.

STRENGTHS

The study has an astonishing sample size in the context of MRS research, a field that has historically struggled to aggregate large datasets because of a severe lack of methodological standardization. Longitudinal MRS data from close to 300 participants means that this is one of the largest MRS datasets to date, enabling the group to add another exciting piece of work to their six previously published manuscripts on relationships between cognitive performance and neurochemical measures from this powerful resource. MRS data quality appears excellent, owed to state-of-the-art acquisition and raw data processing. The authors are further to be commended for making the raw MRS data publicly available - they will serve as a fantastic resource for method developers and applied researchers in the field.

WEAKNESSES

There is generally little to no consideration or discussion concerning age trajectories of MRS-derived metabolite estimates during childhood and early adulthood, which are not clearly established at all. There is evidence for increasing GABA+macromolecules during childhood (Porges et al, eLife 2021, https://elifesciences.org/articles/62575), although it may be ascribed to macromolecules rather than GABA itself (Bell et al, Sci Rep 2021, https://pubmed.ncbi.nlm.nih.gov/33436899/). The findings should at least be discussed in the context of this literature, but I suggest going a step further. The authors have all the data to make a major contribution to the scarce body of evidence on metabolite changes between 6 and 18 years by examining whether GABA and Glu estimates actually appear to change systematically across the age range of their dataset (especially exciting since they have longitudinal data)! It would be immensely valuable to see an analysis like this.

With that said, a methodological weakness concerns the computation of neurochemical concentrations presented here. Firstly, the authors can provide more detail about the acquisition and data processing/modeling decisions. Secondly, and more importantly, MRS-derived estimates of concentration can never be absolute, and always require several assumptions about the relative contributions of tissue classes (GM, WM, CSF) to the measurement volume, tissue water content, water and metabolite MR relaxation times, MR visibility, etc. Quantitative MRS estimates therefore need to be interpreted with caution, especially when these confounding factors are likely to vary between observed groups, or with age, pathology, etc. - there is plenty of reason to assume that cortical maturation, iron accumulation, etc. contribute to changes in relative GM/WM/CSF fractions or relaxation time changes. The authors present two different correction methods to account for some of these aspects, but only present the results of one, stating that "The results showed the same general pattern across all quantification methods.", which is insufficient to assess what changed and what didn't. Interestingly, the authors have presented no less than *four* different quantification methods in a similar manuscript using the same dataset (Zacharopoulos et al, Human Brain Mapp 2021; https://onlinelibrary.wiley.com/doi/10.1002/hbm.25396), but they do not mention normalization to the internal creatine signal in this present work, or whether it yielded different results (which might indicate that their method of tissue correction introduces a confounder rather than correcting for it). There is no mention of whether any further analysis of the water T2 relaxation time estimates was performed, but it would be vital to understand whether they themselves change with age, since this would establish that they are likely to confound GABA and Glu estimation. Generally, the choice to perform additional subject-specific acquisitions to allow corrections for water T2 relaxation is understandable, but not clearly motivated or explained in the experimental section. The authors should further clarify whether the relative tissue volume fractions of GM, WM, and CSF are stable across the age range, or whether there is a systematic tissue composition change with age that may also confound the Glu and GABA estimation.

Finally, I am surprised to find no discussion of limitations at all. It is important to point out the methodological limitations of MRS, which are widely discussed in the MRS literature, but probably less obvious to those readers less intimately familiar with it. This concerns not only the confounding factors for quantification that I described above but also the challenges of the comparably low spectral resolution at 3 Tesla. Even with high-quality data as presented here, it remains unclear whether the small GABA signal can be reliably separated from glutamate, glutamine, and glutathione, all of which exhibit substantial spectral overlap with each other and other strong signals as well as the underlying macromolecular background. The limitations (and how they impact interpretation) ought to be mentioned and discussed in the context of the vast amount of literature. They should provide the reader with the appropriate context and the awareness that all MRS measures are extremely sensitive to many different experimental factors and modeling decisions.

Reviewer #2 (Public Review):

The mechanisms of action potential firing were studied by whole-cell patch-clamp recordings in acute brain slices of the zebra finch. The study builds on the initial finding by Zemel et al. (2021) that the action potentials of robustus arcopallialis projection neurons (RAPNs) have an exceptional small half-duration of about 0.2 ms at 40C. The authors, therefore, set out to investigate the mechanisms of action potential repolarization. They use an impressive set of complementary techniques including voltage clamp and current clamp recordings, pharmacological interventions with classical and novel subunit-specific blockers, in situ hybridization, and comparative genomics of the KCNC/Kv3 potassium channel genes. The data convincingly demonstrate that the Kv3.1 but not Kv3.2-Kv3.4 nor Kv1.1/1.2/1.6, Kv7, or BK channels mediate the rapid repolarization. The manuscript is clearly written and the data and the presentation of the data are of the highest scientific quality. The study is of interest to a broad readership because the zebra finch is a fascinating and novel model to investigate the mechanisms of rapid motor control. The similarities of these neurons of the zebra finch with the specialized Betz cells in the motor cortex of humans and other primates demonstrates the exciting advantages of this animal model in comparison with well-established rodent models to investigate the mechanisms of complex sensory-motor control in vertebrates.

Reviewer #3 (Public Review):

This work describes intracellular recordings from motor neurons of the zebrafinch. The authors use isolated brain slices allowing careful analysis of both voltage- and current-clamp recordings to document differences in action potentials in two motor cortical areas. RAPN neurons are associated with vocal commands that generate bird song, while Ald neurons are also motor neurons, but are not involved in song.

RAPN neurons are found to have much faster action potentials than Ald neurons, and pharmacological experiments provide evidence for the involvement of a particular class of voltage-gated potassium channels, Kv3, in RAPNs that presumably contributes to a faster rate of action potential repolarization and a concomitant narrowing of the action potential width. A set of experiments is included to verify that the findings obtained under normal ex vivo recording conditions (23 deg C) are retained under more physiological conditions (40 deg C). Consistent with the role of Kv3, the action potentials, and underlying potassium currents, are modified by imperfect pharmacological tools TEA, 4AP, and AUT5. Even though imperfect, together they provide support for the role of Kv3. Examination of transcripts for Kv3 family members documents that Kv3.1 is more highly expressed in RAPN than Ald neurons.

The experiments are adequately replicated and the paper is written very clearly. The authors claim that these cells are similar to Betz cells, highly specialized pyramidal neurons mainly found in the primate motor cortex and that they may play a similar role in primates and birds in generating fine motor behavior.

Some weaknesses include missing controls such as reversibility of pharmacological effects and improved statistical analysis. In addition, the linkage of RAPN neurons to Betz cells is not very strong.

Reviewer #1 (Public Review):

This manuscript presents evidence for Kv3 subunits being involved in shaping fast action potentials (APs) within the high-precision circuitry of the zebra finch song circuitry. The authors compare and contrast the morphology of Robustus Arcopallialis (RA) neurons with those in the adjacent intermediate arcopallium (AId) and compare their passive properties, action potential waveforms, and voltage-gated outward currents. Data using pharmacological agents known to interact with Kv3 channels reinforce their other observations.

Strengths:<br /> 1. Interesting avian model of cortical molecular mechanisms.<br /> 2. Comparative study at the level of cortical motoneurons showing those involved in fine motor control for vocalizations express high levels of Kv3.1.<br /> 3. Makes a case for convergent evolutionary utilization of Kv3.1 supporting fast spiking.<br /> 4. Clearly shows other Kv3 subunits are present in the nuclei under study.<br /> 5. Employs well-characterised pharmacological tools to support the physiology.

Weaknesses:<br /> 1. Comparison with Betz Cells comes across as of secondary importance and is perhaps a discussion point rather than the first introductory paragraph.<br /> 2. Fails to adequately quantify the absolute levels of Kv3 mRNA or protein in the zebra finch brain nuclei.<br /> 3. The comparison of % or fold differences between the two avian nuclei (RA and AId neuron) masks important quantitative evidence and the contribution of multiple subunits to functional channels is not well developed.<br /> 4. The voltage-clamp data suggests that the large TEA-sensitive current is too slow to dominantly contribute to the repolarization of a single AP (but would require sustained or cumulative depolarization to be activated), while the fast transient current which could contribute to single APs, is not sufficiently characterised.<br /> 5. It is not possible to conclude that the pharmacology is specific for Kv3.1, it is at best indicative, and the absence of more precise molecular tools (e.g. knockout or gene-edited animals) undermines the authors' justification of the zebra finch as an accessible model.<br /> 6. Although the authors acknowledge the presence of other Kv3 subunits, the report fails to explain whether they are functional, but focuses on Kv3.1 as being dominant, without sufficiently addressing how other subunits contribute (perhaps as heteromeric assemblies of subunits).

Reviewer #2 (Public Review):

This paper is an interesting and novel addition to our understanding of the link between ER stress and lipid homeostasis. Utilizing a genetic screen to determine modulators of the UPRER, Garcia, G., et al., determine C. elegans cannot activate the UPRER as strongly with knockdown of the putative hydroxysteroid dehydrogenase let-767. Additionally, let-767 knockdown results in smaller lipid droplets and changes to ER morphology. Both lipid droplet size and ER morphology size can be restored with supplementation of lipids, while the defect to UPRER activation persists. The authors elegantly show that one impact of let-767 knockdown on UPR is downstream of XBP1 splicing. The authors then go on to show that in mammalian cells, the lipid precursor 3-oxoacyl-CoA can cause a similar reduction to UPRER activation to that seen in C. elegans with let-767 knockdown. Some limitations of this study are that let-767 exact role in lipid metabolism is not well understood and it is unclear what the impact of let-767 knockdown in C. elegans has on lipid composition. It is also unclear mechanistically how let-767 is able to effect UPRER, as the authors show one potential mechanism is by blocking activation of the UPR downstream of XBP1 splicing. While the authors demonstrate that high levels of 3-oxoacyl-CoA can cause a reduction in the UPR response in mammalian cells, this finding is not recapitulated in C. elegans, nor does the study determine whether this compound accumulates in a let-767 knockdown.

Reviewer #3 (Public Review):

Here, the authors identify and characterize the role of C. elegans putative hydroxysteroid dehydrogenase gene let-767 to be essential for both lipid and endoplasmic reticulum (ER) homeostasis. They demonstrated that plays a role in lipid storage, maintaining ER morphology and that the lack of let-767 inhibits the unfolded protein response (UPR) upon proteotoxic stress, presumably by the accumulation of the predicted metabolite directly upstream of LET-767, 3-oxoacyl.

Strengths of the manuscript<br /> The complementary data in human cell line huh-7 that support the authors findings in C. elegans. The ablation of let-767 in C. elegans render the animal incapable of mounting a UPR response upon proteotoxic stress (tunicamycin). Similarly, supplementing the media of huh-7 cells with LET-767 precursor, 3-oxoacyl, attenuates the UPR activation by tunicamycin.

Overall, the experiments are well designed and in logical order throughout the manuscript.

Weakness of the manuscript<br /> The biggest weakness of this manuscript is the difficulty to appreciate the differences reported by the authors from the images provided. Providing images of higher quality or highlighting the differences to note within the figure panels will make the interpretation of data easier.

Additionally, many of the reported data are from biological duplicates. The lack of additional biological replicate might undermine the authors' findings.

Reviewer #1 (Public Review):

The underlying principle of the experimental system described here is to test potential candidate genes that intersect with the proteotoxic-induced UPR by screening an siRNA pool that diminishes the UPR transcription reporter activated by sec-11 RNAi-mediated ER proteotoxic stress. The authors specifically focused on genes reported to play roles in LD biology, instead of general lipid synthesis genes. Systematic evaluation of the LD genes with respect to the induction of the UPR provides important insights into the overall functions and mechanisms of the UPR.

Using this set-up, the authors identified the hydroxysteroid dehydrogenase gene let-767/HSD17B12. Subsequent analyses revealed that let-767-mediated signaling is a key component that establishes the orchestration of both ER lipid and protein homeostasis and ER organismal functions, including ER lipid storage and ER structural changes. In addition, the authors found that acs-1i, knockdown of a gene involved in metabolism of lipids such as LCFA and mmBCFA, also diminished UPRE-GFP levels induced by sec-11i, albeit to a lesser extent than let-767i. Supplementation of lipid metabolites such as LCFA and mmBCFA recovered not only the sec-11-induced UPRE-GFP reporter phenotypes in acs-1i worms, but also the ER size and morphology and the LD and body sizes.

In contrast, the UPRE-GFP reporter phenotype in let-767i worms was not recovered by exogenously added LCFA or mmBCFA, although it was recovered by spb-1 RNAi, knockdown of a major lipogenic enzyme/pathway. The system established by the authors allowed them to quantitatively dissect the involvement of the Ire1-Xbp1 splicing UPR signaling branch. Finally, the authors demonstrated similar effects in mammalian tissue culture cells, suggesting conservation of the mechanisms.

The conclusions of this manuscript are generally in agreement with the data and the authors' interpretations are reasonable. However, at this point, the work remains descriptive and does not provide a mechanistic understanding. Overall contributions/advances towards providing new insights into how the UPR pathway is wired with respect to lipid-associated perturbations remain somewhat limited.

Reviewer #2 (Public Review):

Aimon et al. used fast whole-brain imaging to investigate the relationship between walking and neural activity in adult fruit flies. They find that increases in brain-wide activity are tightly correlated with walking behavior, and not with grooming or flailing, and are independent of visual input. They reveal that excitatory, inhibitory, and neuromodulatory neurons all contribute to brain-wide increases in neural activity during walk. Aimon et al. extend their observations of brain-wide activity to reveal that activity in some inferior brain regions is more correlated with walk than in other brain regions. The authors further analyzed their imaging dataset to identify candidate brain regions and cell types that may be important for walking behavior, which will be useful in hypothesis generation in future studies. Finally, the authors show that brain-wide activity is similar between spontaneous and forced walk and that severing the connection between the ventral nerve cord and central brain abolishes walk-related increases in brain activity. These results suggest that increases in brain-wide activity during walking may be largely attributed to sensory and proprioceptive feedback ascending to the central brain from the ventral nerve cord rather than to top-down executive and motor control programs. The observations presented in this study suggest hypotheses that may be tested in future studies.

Strengths: This paper presents a rich imaging dataset that is well-analyzed and cataloged, which will be valuable for researchers who use this paper for future hypothesis generation. The comparison of many different reagents, imaging speeds, and behavioral conditions suggests that the observed increases in brain-wide activity during walking are quite robust to imaging methods in adult fruit flies.

Weaknesses: This study is largely observational, and the few experimental manipulations presented are insufficient to support the author's broad claims about the generation of brain-wide neural activity.

Notably, the authors suggest that their image analysis can reveal individual cell types that are important for walking by matching their morphologies to registered components from whole-brain imaging experiments. While these predictions are a useful starting point for future experiments, they have not convincingly shown that their method can identify individual cell types in genetic reagents with more restricted expression patterns. Adding further validation to show that genetically subtracting the candidate neurons from the overall expression pattern of the calcium indicator abolishes that component from the response would strengthen this claim. Furthermore, imaging the matched candidate neuronal cell type to show that it recapitulates the activity dynamics of the proposed component would add additional evidence.

In addition, increases in neural activity prior to walk onset in specific brain regions are intriguing but insufficient to demonstrate the neurons in these regions trigger walking. This claim should await further studies that employ targeted and acute manipulation of neural activity, as noted by the authors. Furthermore, that activity in these brain regions is significantly increased prior to walk onset awaits more rigorous statistical testing, as do the authors' claims that spontaneous versus forced walking alters these dynamics. The suggestion that walking increases brain-wide activity via feedback from the ventral nerve cord is an interesting possibility and would also benefit from additional experimental validation. Activating and silencing neurons that provide proprioceptive feedback from the legs and determining the effect of this manipulation on brain-wide neural activity would be a good starting point.

Reviewer #1 (Public Review):

This paper uses light field microscopy to measure calcium signals across the fly brain while it is walking and turning, and also while the fly is externally driven to walk and turn, using a treadmill. The authors drive calcium indicator expression using pan-neuronal drivers, as well as drivers specific to individual neurotransmitters and neuromodulators. From their experiments, the authors show that inhibitory and excitatory neurons in the brain are activated in similar patterns by walking and that neurons expressing machinery for different neuromodulatory amines tend to show differentially strong calcium signals during walking. By examining spontaneous and forced walking and turning, the authors identify brain regions that activate before spontaneous turning and that activate asymmetrically in concert with spontaneous or forced turning.

Strengths: Overall, the strength of this paper is in its careful descriptions and analyses of whole brain activation patterns that correlate with spontaneous and forced behaviors. Showing how the pattern of activity relates to broad classes of cells is also useful for understanding brain activation. Especially in brain regions identified as preceding spontaneous walking and in being asymmetrically involved in spontaneous and forced turning, it provides a wealth of potential hypotheses for new experiments. Overall, it contributes to a coarse-grained understanding of broad changes in brain activity during behavior.

Weaknesses: The primary weakness of this paper is that it presents some speculative interpretations and conclusions too strongly. Most importantly, average activity in a neuropil can represent the calcium activity of hundreds or thousands of neurons, and it is hard to know what fraction is active, for instance, or how expression pattern differences might play into calcium signals. Calcium signals also do not reliably indicate hyperpolarization, so a net increase in the average Ca++ indicator signal does not necessarily reflect that the average neuron is becoming more active, just that some labeled neurons are becoming more active, while others may be inactive or hyperpolarized. The conclusions about regions triggering walk (rather than just preceding it) are too strong for the manipulations in this paper, as are some of the links with individual neuron types. Thus, more presenting substantial caveats is required for the conclusions being drawn from the data presented here.

Reviewer #3 (Public Review):

Aimon and colleagues investigated brain activity in flies during spontaneous and forced walking. They used light-field microscopy to image calcium activity in the brain at high temporal resolution as the animal walked on a ball and they used the statistical inference methods PCA and ICA to tease out subregions of the brain that had distinct patterns of activity. They then sought to relate those patterns to walking. Most interesting are the experiments they performed comparing forced walking to spontaneous walking because this provides a framework to generate hypotheses about which aspects of neural activity are reporting the animal's movements versus generating those movements. The authors identify subregions and neuron types that may be involved in generating vs reporting walking. Their analysis is reasonable but could be further strengthened with a more powerful statistical framework that explicitly considered the multiple hypotheses being tested. More broadly, the work serves as a starting point to investigate the role of different regions in the brain and should spur follow-up investigations that involve more perturbative approaches in addition to the correlative approaches presented here.

Reviewer #1 (Public Review):

Tomasi et al. performed a combination of bioinformatic, next-generation tRNA sequencing experiments to predict the set of tRNA modifications and their corresponding genes in the tRNAs of the pathogenic bacteria Mycobacterium tuberculosis. Long known to be important for translation accuracy and efficiency, tRNA modifications are now emerging as having regulatory roles. However, the basic knowledge of the position and nature of the modifications present in a given organism is very sparse beyond a handful of model organisms. Studies that can generate the tRNA modification maps in different organisms along the tree of life are good starting points for further studies. The focus here on a major human pathogen that is studied by a large community raises the general interest of the study. Finally, deletion of the gene mnmA responsible for the insertion of s2U at position 34 revealed defects in in growth in macrophage but in test tubes suggesting regulatory roles that will warrant further studies. The conclusions of the paper are mostly supported by the data but the partial nature of the bioinformatic analysis and absence of Mass-Spectrometry data make it incomplete. The authors do not take advantage of the Mass spec data that is published for Mycobacterium bovis (PMID: 27834374) to discuss what they find.

Important points to be considered:

1) The authors say they took a list of proteins involved in tRNA modifications from Modomics and added manually a few but we do not know the exact set of proteins that were used to search the M. mycobacterium genome.

2) The absence of mnmGE genes in TB suggested that the xcm5U derivatives are absent. These are present in M. bovis (PMID: 27834374). Are the MnmEG gene found in M. bovis? If yes, then the authors should perform a phylogenetic distribution analysis in the Mycobacterial clade to see when they disappeared. If they are not present in M. bovis then maybe a non-orthologous set of enzymes do the same reaction and then the authors really do not know what modification is present or not at U34 without LC-MS. The exact same argument can be given for the xmo5U derivatives that are also found in M.bovis but not predicted by the authors in M. tuberculosis.

3) Why is the Psi32 predicted by the authors because of the presence of the Rv3300c/Psu9 gene not detected by CMC-treated tRNA seq while the other Psi residues are? Members of this family can modify both rRNA and tRNA. So the presence of the gene does not guarantee the presence of the modification in tRNAs

4) What are tsaBED not essential but tsaC (called sua5 by the authors) essential?

Reviewer #2 (Public Review):

In this study, Tomasi et al identify a series of tRNA modifying enzymes from Mtb, show their function in the relevant tRNA modifications and by using at least one deleted strain for MnmA, they show the relevance of tRNA modification in intra-host survival and postulate their potential role in pathogenesis.

Conceptually it is a wonderful study, given that tRNA modifications are so fundamental to all life forms, showing their role in Mtb growth in the host is significant. However, the authors have not thoroughly analyzed the phenotype. The growth defect aspect or impact on pathogenesis needs to be adequately addressed.

- The authors show that ΔmnmA grows equally well in the in vitro cultures as the WT. However, they show attenuated growth in the macrophages. Is it because Glu1_TTC and Gln1-TTG tRNAs are not the preferred tRNAs for incorporation of Glu and Gln, respectively? And for some reason, they get preferred over the alternate tRNAs during infection? What dictates this selectivity?

- As such the growth defect shown in macrophages would be more convincing if the authors also show the phenotype of complementation with WT mnmA.

An important consideration here is the universal nature of these modifications across the life forms. Any strategy to utilize these enzymes as the potential therapeutic candidate would have to factor in this important aspect.

Reviewer #3 (Public Review):

The work presented in the manuscript tries to identify tRNA modifications present in Mycobacterium tuberculosis (Mtb) using reverse transcription-derived error signatures with tRNA-seq. The study identified enzyme homologs and correlates them with presence of respective tRNA modifications in Mtb. The study used several chemical treatments (IAA and alkali treatment) to further enhance the reverse transcription signals and confirms the presence of modifications in the bases. tRNA modifications by two enzymes TruB and MnmA were established by doing tRNA-seq of respective deletion mutants. Ultimately, authors show that MnmA-dependent tRNA modification is important for intracellular growth of Mtb. Overall, this report identifies multiple tRNA modifications and discuss their implication in Mtb infection.

Important points to be considered:

- The presence of tRNA-based modifications is well characterised across life forms including genus Mycobacterium (Mycobacterium tuberculosis: Varshney et al, NAR, 2004; Mycobacterium bovis: Chionh et al, Nat Commun, 2016; Mycobacterium abscessus: Thomas et al, NAR, 2020). These modifications are shown to be essential for pathogenesis of multiple organisms. A comparison of tRNA modification and their respective enzymes with host organism as well as other mycobacterium strains is required. This can be discussed in detail to understand the role of common as well as specific tRNA modifications implicated in pathogenesis.

- Authors state in line 293 "Several strong signatures were detected in Mtb tRNAs but not in E. coli". Authors can elaborate more on the unique features identified and their relevance in Mtb infection in the discussion or result section.

- Deletion of MnmA is shown to be essential for E. coli growth under oxidative stress (Zhao et al, NAR, 2021). In similar lines, MnmA deleted Mtb suffers to grow in macrophage. Is oxidative stress in macrophage responsible for slow Mtb growth?

- Authors state in line 311-312 "Mtb does not contain apparent homologs of the tRNA modifying enzymes that introduce the additional modifications to s2U". This can be characterised further to rule out the possibility of other enzyme specifically employed by Mtb to introduce additional modification.

Reviewer #1 (Public Review):

Muller glia function as retinal stem cells in the adult zebrafish retina. Following retinal injury, Muller glia are reprogramned (reactive Muller glia), and then divide to produce a progenitor that amplifies and differentiates into retinal neurons. Previous scRNAseq analysis used total retinal RNA from uninjured and injured retinas isolated at time points when Muller glia are quiescent, being reprogrammed, and proliferating to reveal genes and gene regulatory networks underlying these events (Hoang et al., 2020). The manuscript by Celotto et al., used double transgenic zebrafish that allow them to purify by FACS quiescent and reactive Muller glia, Muller glia-derived progenitors, and their differentiating progeny at different times post retinal damage. RNA from these cell populations was used in scRNAseq studies to identify the transcriptomes associated with these cell populations. Importantly, they report two quiescent and two reactive Muller glia populations. These results raise the interesting possibility that Muller glia are a heterogenous population whose members may exhibit different regenerative responses to retinal injury. However, without further experimentation, the validity and significance of this result remain unclear. In addition to putative Muller cell heterogeneity, Celotto et al., identified multiple progenitor classes, some of which are specified to regenerate specific retinal neuron types. Because of its focus on Muller glia and Muller glia-derived progenitors at mid to late stages of retina regeneration, this new scRNAseq data will be a useful resource to the research community for further interrogation of gene expression changes underlying retina regeneration.

Major concerns:

1) The identification of multiple populations of Muller glia, reactive Muller glia, and progenitors is interesting, but beyond a few in situ hybridization studies to validate injury-dependent gene inductions, there are no experiments that confirm that multiple cell populations exist in vivo, and no experiments examining the significance of these different populations in the regenerative process. It would be helpful to discuss how the peripheral to the central gradient of Muller cell maturation influences the scRNAseq-based cell clustering results.

2) While the reliance on transient GFP and mCherry expression may be sufficient, the final population used for the scRNAseq analysis is only partial in nature. Permanently marking the MG through a Cre-Lox system is more ideal. The authors mention the possibility of missing highly proliferative populations of MG/RPC through the dilution of fluorescent proteins; a transgenic system that allows for true lineage tracing may then capture more appropriate MG/RPC populations. The lack of gating for a pure GFP population also confounds this problem which the authors do mention in the discussions; this oversight was not explained.

3) Much time was taken to identify each cell cluster and to list the differentially expressed genes, but no functional significance for these genes was probed. While a lot of work has gone into the analysis shown, altering some of the MG/RPC trajectories through differentially expressed genes would go a long way to making this study more impactful.

4) The data presented in this paper has significant overlap with scRNAseq data presented by Hoang et al., 2020 in Science where Muller glia, reactive Muller glia, and Muller glia-derived progenitors were carefully analyzed. How does their data fit with the data presented here? The authors could have used that paper as a jumping-off point and offered more time points for comparison, especially as progenitors differentiate.

5) A major conclusion of the paper is that neurogenic progenitors in the injured retina differentiate into neurons with a similar order as that taking place during development. This analysis is based on two time points, and while the trends stay true to the authors' model, two time points are too few to make such a conclusion. In addition, because of the time points chosen for this analysis, many mature neuronal markers are lacking. Including additional time points so mature neuronal markers are detected in the dataset would enhance the trajectory proposed.

Reviewer #2 (Public Review):

In this publication, the authors provide a comprehensive trajectory of transcriptional changes in Müller glia cells (MG) in the regenerating retina of zebrafish. These resident glia cells of the retina can differentiate into all neural cell classes following injury, providing full regenerative capabilities of the zebrafish retina. The authors achieved this by using single-cell RNA sequencing of Müller glia, progenitors, and regenerated progeny, comparing uninjured and light-lesioned retinae.

The isolation strategy involves using two transgenic strains, one labelling dividing cells and their immediate progeny, and the other Müller glia cells. This allowed them to separate injury-induced proliferating and non-reactive Müller glia cells. Subsequent single-cell transcriptomics showed that MG could be non-reactive under both uninjured and lesioned conditions and reactive MG give rise to a cell population that both replenishes the pool of MG and replenish neurogenic retinal precursor cells. These precursor cells produce regenerated neurons in a developmental time series with ganglion cells being born first and bipolar cells being born last. Interestingly hybrid populations have been detected that co-share characteristics of photoreceptor precursors and reactive glia.

This is the first study of its kind following the dynamic changes of transcriptional changes during retinal regeneration, providing a rich data source of genes involved in regeneration. Their finding of transcriptionally separable MG populations is intriguing.

This study focuses on the light-lesioned retina and leaves open the question if the observed transcriptional trajectories of regenerating neurons are generalizable to other lesion models (e.g. chemical or mutational lesions) or are specific to the light-damaged retina.

Reviewer #1 (Public Review):

Ciampa et al. investigated the role of the hypoxia-inducible factor 1 (HIF-1) pathway in placental aging. They performed transcriptomic analysis of prior data of placental gene expression over serial timepoints throughout gestation in a mouse model and identified increased expression of senescence and HIF-1 pathways and decreased expression of cell cycle and mitochondrial transcripts with advancing gestational age. These findings were confirmed by RT-PCR, Western blot, and mitochondrial assessment from mouse placental tissues from late gestation time points. Studies of human placental samples at similar late gestational ages showed similar trends in increased HIF-1 targets and decreased mitochondrial abundance with increasing gestation, but were not significantly significant due to the limited availability of uncomplicated preterm placenta samples. The authors demonstrated that stabilization of HIF-1 in vitro using primary trophoblasts and choriocarcinoma cell lines recapitulated the gene and mitochondrial dysfunction seen in the placental tissues and were consistent with senescence. Interestingly, cell-conditioned media from HIF-1 stabilized placenta cell lines induced myometrial cell contractions in vitro and correspondingly, induction of HIF-1 in pregnant mice was associated with preterm labor in vivo. These data support the role of the HIF-1 pathway in the process of placental senescence with increasing gestational age and highlight this pathway as a potentially important contributor to gestational length and a potential target for therapeutics to reduce preterm birth.

Overall, the conclusions of this study are mostly well supported by the data. The concept of placental aging has been controversial, with several prior studies with conflicting viewpoints on whether placental aging occurs at all, is a normal process during gestation, or rather only a pathologic phenomenon in abnormal pregnancies. This has been rather difficult to study given the difficulty of obtaining serial placental samples in late gestation. The authors used both a mouse model of serial placental sampling and human placental samples obtained at preterm, but non-pathologic deliveries, which is an impressive accomplishment as it provides insight into a previously poorly understood timepoint of pregnancy. The data clearly demonstrate changes in the HIF-1 pathway and cellular senescence at increasing gestational ages in the third trimester, which is consistent with the process of aging in other tissues.

Weaknesses of this study are that although the authors attribute alterations in HIF-1 pathways in advanced gestation to hypoxia, there are no experiments directly assessing whether the changes in HIF-1 pathways are due to hypoxia in either in vitro or in vivo experiments. HIF-1 has both oxygen-dependent and oxygen-independent regulation, so it is unclear which pathways contribute to placental HIF-1 activity during late gestation, especially since the third-trimester placenta is exposed to significantly higher oxygen levels compared to the early pregnancy environment. Additionally, the placenta is in close proximity to the maternal decidua, which consists of immune and stromal cells, which are also significantly affected by HIF-1. Although the in vitro experimental data in this study demonstrate that HIF-1 induction leads to a placenta senescence phenotype, it is unclear whether the in vivo treatment with HIF-1 induction acts directly on the placenta or rather on uterine myometrium or decidua, which could also contribute to the initiation of preterm labor.

Reviewer #2 (Public Review):

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

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

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

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

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

Reviewer #3 (Public Review):

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

Major concerns:

1) The hypothesis states that placental aging promotes parturition via HIF-1a activation, the study does not provide any evidence of an aged placenta. Aging is considered a progressive and irreversible loss of functional capacity, inability to maintain homeostasis, and decreased ability to repair the damage. The placenta retains all these abilities throughout pregnancy [PMID: 9462184], and there's no evidence that the placenta functionally declines between 35-39 weeks, otherwise, it wouldn't be able to support fetal development. However, there is evidence of a functional decline in post-term placentas (i.e. >40 weeks in humans) but the authors compare preterm placentas with E17.5 mice placentas or 39-week human placentas, both these gestational periods are prior to the onset of parturition in most pregnancies (human = 40wkGA, mice=E18.5).

2) While the authors provide evidence that HIF-1α activity increases in both the human and mice placenta as gestation progresses, the mechanistic link between placental HIF-1α and parturition is not strongly supported. For example, most of the evidence is based on in vitro studies showing that conditioned media from trophoblasts treated with CoCl2 increased the contraction of myometrial cells. The specific factor responsible was not identified but the authors allude to pro-inflammatory factors such as cytokines. It was therefore interesting to note that the conditioned media had undergone a filtration step that removes all substances >10kDa, which includes the majority of cytokines and hormones.

3) An alternative explanation is that CoCl2 treatment-induced trophoblast differentiation and the effects on myometrial contraction may be related to differences in secreted factors produced by cytotrophoblasts versus syncytiotrophoblast. Although JAR cells do not spontaneously differentiate, they can be induced to syncytialise upon cAMP stimulation. Ref 39 the authors cite shows this. Indeed, the morphology of the cells in Fig5F that were exposed to CoCl2 indicates that they may be syncytialised. Syncytialised trophoblasts also express markers of senescence including increased SA-β-gal activity and reductions in mitochondrial activity.

4) The in vivo experiment showing reduced gestation length in pregnant mice receiving DMOG injection is interesting. However, we cannot exclude the effects of DMOG on non-placental tissues (both maternal and fetal) or the non-specific effects of DMOG (i.e. HIF-1α independent). Furthermore, previous studies using a more direct approach to alter HIF-1α activity in the placenta using trophoblast-specific overexpression of HIF-1α in mice do not lead to changes in gestation length [PMID: 30808910].

5) Lack of appropriate experimental models. E.g. JAR choriocarcinomas are not an ideal model of the human trophoblast as they are malignant. Much better models are available e.g. primary human trophoblasts from term placentas or human trophoblast stem cells from first-trimester placentas. Similarly, the mouse model is also not specific as discussed above.

6) Lack of cohesion between the different experimental models. E.g. CoCl2 was used to induce hypoxia/HIF1α in mouse TBs, but DMOG was used in vivo in mice. SA-β Gal staining was carried out in cells but not in mouse or human tissues.

7) Evidence of senescence and mitochondrial abundance could be strengthened by providing additional markers. E.g. only GLB1 mRNA expression is provided as evidence of senescence, and COX IV protein for mitochondrial abundance in mouse and human placentas.

8) Given that the main goal of this study was to investigate the role of hypoxia, hypoxia (i.e. low oxygen) was never directly induced and the results were based on chemical inducers of HIF-1α which have multiple off-target effects.

Peer review report

Title: If it’s there, could it be a bear?

version: 2

Referee: Rahul Raveendran

Institution: Biodiversity Institute, University of Kansas

email: rahulravi777@gmail.com

General assessment

The manuscript needs to be revised thoroughly.

Essential revisions that are required to verify the manuscript

I feel that the introduction can be a little more elaborative. My suggestions are as follows:

• In the first paragraph, the author can give more details about ‘hominology’ by citing the works of Dmitry Bayanov. This is to give a historical account of ‘hominid research’ to the readers who are unfamiliar to this topic.

• Second paragraph has information related to the ‘misdeeds’ of the ‘proponents of hominology’. According to me, there must be continuous flow of information from paragraph to paragraph. Currently, I do not see a proper chronological flow of details in 1st and 2nd paragraph. I request the learned author to check this in such a way that 1st para must provide details about ‘hominids’, ‘hominology’, and the 2nd para must give the scientific explanation about these ‘controversial findings’.

• Line numbers 43-44: This paragraph must be expanded, and possibly include more information about ‘American black bear’ being misrecognized as ‘bigfoot sightings’ with references. If available, provide details regarding the molecular/clinical test results (i.e., references).

• A separate paragraph has to be incorporated to detail the methods adopted by scientists/researchers to link the population density of American black bear and bigfoot sightings.

• Line numbers 49-51: The sentence “No positive correlation between……a small proportion of all sightings” has to be re-written as I think that it does not convey its meaning properly.

• Provide the fundamentals of ecological niche modeling. How such a concept can be adopted in this sort of a study with a strong emphasis on the results of Lozier et al. (2009) would be helpful for the readers.

• In the last paragraph of the introduction, although not in detail, the author should state clearly the approach that was taken to execute the study. For example, details related to the chosen statistical methods with references. And state your hypothesis clearly.

Materials and Methods

• Line numbers 67-77: Please make these sentences more lucid. I feel that this paragraph lacks coherence.

• Line numbers 90-94: Please make these sentences more understandable.

• Line numbers 113-116: Please re-write these sentences to make them more understandable. Results

• Line numbers 121-123: The article states that both the sasquatch sighting and black bear population maps are strongly coloured in the Pacific Northwest area……”. BUT, in PNW, I do not think that bigfoot sightings in British Columbia are proportional to the black bear population.

• Presentation of results is a bit confusing for me. I would suggest to rewrite the results with a view to make everyone who reads this article understands the results properly.

Discussion

• Discussion must be vastly improved

a) It is difficult to understand the very first sentence of the discussion that starts with “The present study regressed ………………..”. Please re-write it.

b) Results of the present study should be discussed in detail, linking previous published reports.

c) The models employed must be discussed in detail with the support of previous reports to substantiate the conceptual correctness of the methodological framework.

Decision

Requires revisions: Major revisions are suggested.

Peer review report

Title: If it’s there, could it be a bear?

version: 2

Referee: Julie Sheldon

Institution: University of Tennessee

email: jsheldo3@tennessee.edu

ORCID iD: https://orcid.org/0000-0003-2813-3027

General assessment

This manuscript is a collection of statistical analyses attempting to show that sasquatch sightings correlate with black bear populations, and humans may be mistaking black bears for sasquatch.

The author effectively introduces the topic, provides adequate background on sasquatch, but does not provide much on black bear populations, natural history, or human-bear interactions.

The author performs several statistical tests to support the findings. I am not a statistician, but the tests seem valid. The data used for the statistical analyses, however, are not ideal. The resource (Hristienko and McDonald) provided for obtaining black bear populations was published in 2007 and the data was from 2001 via “subjective extrapolations” and “expert opinions”. Thus, this resource is outdated and suboptimal as black bear populations have changed over time. A more updated resource with more scientific methods in data collection would improve this manuscript since having as accurate as possible bear population estimates is very important for the goal of this study. The author notes this briefly in the limitations. If the human population and sasquatch sighting data matched up with the dates of bear population estimates, it would be more valid (just outdated), but there are no date ranges of human or sasquatch data provided in the manuscript.

In the results, the maps of bigfoot sightings and black bear population do not appear to correlate visually, which downplays the value of the statistical analysis. The stats should support the visual data and vice versa if the study is sound. Perhaps more updated bear population data will improve this.

The discussion is short and briefly brings up important points that can invalidate the study without much discussion or argument supporting the findings of this study.

Essential revisions that are required to verify the manuscript

I recommend the following to improve the manuscript enough to consider it valid:

Date-match the bear population, human population, and bigfoot sightings to improve the validity of the data analysis. One way to do this is to use data from the same 10-year period only.

Improve the sources of bear population information.

Expand the discussion to include reasons and ideas the maps don’t line up like the statistical analyses do – ie bears in Florida and the southeast.

Other suggestions to improve the manuscript

I recommend provide some information on black bear population/natural history in the introduction – ie what sort of habitats do black bears live in. Consider the possibility that sasquatch sightings may correlate with a type of habitat (ie forest), which happen to also correlate with black bear habitat. This may support the idea that sasquatch sightings are bears, or that sasquatch also likes to live in similar habitats as bears.

The author reports that black bears are not prominent in Florida; however, there are > 4,000 black bears bears in Florida, that are reportedly large, and it may be worth considering this as a reason for the concentration of sasquatch sightings in Florida as seen on the map. More accurate black bear data as discussed above may help improve this aspect. Experientially, there is also a high concentration of black bears in the southeastern US, where there is also a high concentration of humans and human-bear encounters. The author does not discuss this along with the number of sasquatch sightings in this region as seen on the map.

Decision

Verified with reservations: The content is academically sound but has shortcomings that could be improved by further studies and/or minor revisions.

Reviewer #1 (Public Review):

Summary

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

Strengths

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

Weaknesses

Showing that A-2 and especially A-3 are outliers in the PCA analysis is useful, but it may be hiding other interesting signals in the data. The other strains are remarkably colinear on these plots, hinting that if the outliers were removed, one main component would emerge along which they are situated. It also seems possible that this additional analysis step would allow the second dimension to better differentiate them in a way that is interesting with respect to their mutator status or mutations in key metabolic or regulatory genes.

There is a missed opportunity to connect some key results to what is known about LTEE mutations that reduce the activity of pykF (pyruvate kinase I). This gene is mutated in all 12 LTEE populations, and often these mutations are frameshifts or transposon insertions that should completely knock out its activity. At first glance, inactivating an enzyme for a step in glycolysis does not make sense when the nutrient source in the growth medium is glucose, even though PykF is only one of two isozymes E. coli encodes for this reaction. There has been speculation that inactivating pykF increases the concentration of phosphoenolpyruvate (PEP) in cells and that this can lead to increased rates of glucose import because PEP is used by the phosphotransferase system of E. coli to import glucose (see https://doi.org/10.1002/bies.20629). The current study has confirmed the higher PEP levels, which is consistent with this model.

In the introduction, the papers cited to show the importance of changes in metabolism for adaptation do not seem to fit the focus of this study very well. They stress production of toxins and secondary metabolites, which do not seem to be mechanisms that are at work in the LTEE. I can think of two areas of background that would be more relevant: (1) studies of how bacterial metabolism evolves in adaptive laboratory evolution (ALE) experiments to optimize metabolic fluxes toward biomass production (for example, https://doi.org/10.1038/nature01149 ), and (2) discussions of how cross-feeding, metabolic niche specialization, and metabolic interdependence evolve in microbial communities, including in other evolution experiments (for example, https://doi.org/10.1073/pnas.0708504105 and https://doi.org/10.1128/mBio.00036-12).

Impact and Significance

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

Reviewer #2 (Public Review):

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

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

However, the paper's overall clarity is lacking. It is spread too thin and covers many topics without a clear focus. I strongly recommend a substantial rewrite of the manuscript, emphasizing structure and readability. The science is well executed, but the current writing does not do it justice.

Reviewer #1 (Public Review):

The study examines how hemocytes control whole-body responses to oxidative stress. Using single cell sequencing they identify several transcriptionally distinct populations of hemocytes, including one subset that show altered immune and stress gene expression. They also find that knockdown of DNA Damage Response (DDR) genes in hemocytes increases expression of the immune cytokine, upd3, and that both upd3 overexpression in hemocytes and hemocyte knockdown of DDR genes leads to increased lethality upon oxidative stress.

Strengths

1, The single cell analyses provide a clear description of how oxidative stress can cause distinct transcriptional changes in different populations of hemocytes. These results add to the emerging them in the field that there functionally different subpopulations of hemocytes that can control organismal responses to stress.<br /> 2, The discovery that DDR genes are required upon oxidative stress to limit cytokine production and lethality provides interesting new insight into the DDR may play non-canonical roles in controlling organismal responses to stress.

Weaknesses

1, In some ways the authors interpretation of the data - as indicated, for example, in the title, summary and model figure - don't quite match their data. From the title and model figure, it seems that the authors suggest that the DDR pathway induces JNK and Upd3 and that the upd3 leads to tissue wasting. However, the data suggest that the DDR actually limits upd3 production and susceptibility to death as suggested by several results:<br /> a) PQ normally doesn't induce upd3 but does lead to glycogen and TAG loss, suggesting that upd3 isn't connected to the PQ-induced wasting.<br /> b) knockdown of DDR upregulates upd3 and leads to increased PQ-induced death. This would suggest that activation of DDR is normally required to limit, rather than serve as the trigger for upd3 production and death.<br /> c) hemocyte knockdown of either JNK activity or upd3 doesn't affect PQ-induced death, suggesting that they don't contribute to oxidative stress-induced death. Its only when DDR is impaired (with DDR gene knockdown) that an increase in upd3 is seen (although no experiments addressed whether JNK was activated or involved in this induction of upd3), suggesting that DDR activation prevents upd3 induction upon oxidative stress.

2, The connections between DDR, JNK and upd3 aren't fully developed. The experiments show that susceptibility to oxidative stress-induced death can be caused by a) knockdown of DDR genes, b) genetic overexpression of upd3, c) genetic activation of JNK. But whether these effects are all related and reflect a linear pathway requires a little more work. For example, one prediction of the proposed model is that the increased susceptibility to oxidative stress-induced death in the hemocyte DDR gene knockdowns would be suppressed (perhaps partially) by simultaneous knockdown of upd3 and/or JNK. These types of epistasis experiments would strengthen the model and the paper.

3, The (potential) connections between DDR/JNK/UPD3 and the oxidative stress effects on depletion of nutrient (lipids and glycogen) stores was also not fully developed. However, it may be the case that, in this paper, the authors just want to speculate that the effects of hemocyte DDR/upd3 manipulation on viability upon oxidative stress involve changes in nutrient stores.

Reviewer #2 (Public Review):

Hersperger et al. investigated the importance of Drosophila immune cells, called hemocytes, in the response to oxidative stress in adult flies. They found that hemocytes are essential in this response, and using state-of-the-art single-cell transcriptomics, they identified expression changes at the level of individual hemocytes. This allowed them to cluster hemocytes into subgroups with different responses, which certainly represents very valuable work. One of the clusters appears to respond directly to oxidative stress and shows a very specific expression response that could be related to the observed systemic metabolic changes and energy mobilization. However, the association of these transcriptional changes in hemocytes with metabolic changes is not well established in this work. Using hemocyte-specific genetic manipulation, the authors convincingly show that the DNA damage response in hemocytes regulates JNK activity and subsequent expression of the JAK/STAT ligand Upd3. Silencing of the DNA damage response or excessive activation of JNK and Upd3 leads to increased susceptibility to oxidative stress. This nicely demonstrates the importance of tight control of JNK-Upd3 signaling in hemocytes during oxidative stress. However, it would have been nice to show here a link to systemic metabolic changes, as the authors conclude that it is tissue wasting caused by excessive Upd3 activation that leads to increased susceptibility, but metabolic changes were not analyzed in the manipulated flies. The overall conclusion of this work, as presented by the authors, is that Upd3 expression in hemocytes under oxidative stress leads to tissue wasting, whereas in fact it has been shown that excessive hemocyte-specific Upd3 activation leads to increased susceptibility to oxidative stress (whether due to increased tissue wasting remains a question). The DNA damage response ensures tight control of JNK-Upd3, which is important. However, what role naturally occurring Upd3 expression plays in a single hemocyte cluster during oxidative stress has not been tested. What if the energy mobilization induced by this naturally occurring Upd3 expression during oxidative stress is actually beneficial, as the authors themselves state in the abstract - for potential tissue repair? It would have been useful to clarify in the manuscript that the observed pathological effects are due to overactivation of Upd3 (an important finding), but this does not necessarily mean that the observed expression of Upd3 in one cluster of hemocytes causes the pathology.

Reviewer #3 (Public Review):

In this study, Kierdorf and colleagues investigated the function of hemocytes in oxidative stress response and found that non-canonical DNA damage response (DDR) is critical for controlling JNK activity and the expression of cytokine unpaired3. Hemocyte-mediated expression of upd3 and JNK determines the susceptibility to oxidative stress and systemic energy metabolism required for animal survival, suggesting a new role for hemocytes in the direct mediation of stress response and animal survival.

Strength of the study:<br /> 1. This study demonstrates the role of hemocytes in oxidative stress response in adults and provides novel insights into hemocytes in systemic stress response and animal homeostasis.<br /> 2. The single-cell transcriptome profiling of adult hemocytes during paraquat treatment, compared to controls, would be of broad interest to scientists in the field.

Weakness of the study:<br /> 1. The authors claim that the non-canonical DNA damage response mechanism in hemocytes controls the susceptibility of animals through JNK and upd3 expression. However, the link between DDR-JNK/upd3 in oxidative stress response is incomplete and some of the descriptions do not match their data.<br /> 2. The schematic diagram does not accurately represent the authors' findings and requires further modifications.

Reviewer #1 (Public Review):

In this study, Muronova et al., demonstrate the physiological importance of a centriole and microtubule-associated protein, CCDC146, in sperm flagellar formation and male reproduction. In a previous study, the authors identified two loss-of-function mutations in CCDC146 from the sterile males with multiple morphological abnormalities in flagellar (MMAF) phenotype. To further test physiological significance of the CCDC146, the authors generate its knockout mouse model. The knockout males share the MMAF phenotypes with severely impaired flagellar morphology due to the defective sperm generation in testes. Using CCDC146 knock-in mouse model and expansion microscopy techniques, the authors observed CCDC146 localizes at human and mouse sperm flagella, which is different from the somatic cells. The authors also observed impaired manchette and head-tail coupling apparatus in developing spermatid lacking CCDC146 and address CCDC146 loss-of-function induces molecular and structural defects at axoneme in developing male germ cells, which finally causes MMAF phenotype and male infertility.

This reviewer agrees that identifying and analyzing new pathogenic molecules and variants is hugely valuable to establish male infertility in genetic level. As the authors have done, this study also enlarges the genetic causality underlying MMAF and male infertility. In addition, this study applies new techniques, expansion microscopy, which is also an innovative approach. Although many approaches are used, unfortunately, this study misses the molecular mechanisms to explain pathogenicity to cause MMAF by the CCDC146. Only intracellular localization of the molecule is heavily examined. Although the authors show defective intracellular localization of the centriole and manchette, how CCDC146 loss-of-function and the developmental defects are linked is not examined. These limits provide the impression that this study could be simply another identification of the MMAF-causing gene, which were heavily performed by the authors. Also, in many parts, the results do not clearly support the authors claim. Therefore, this reviewer thinks the current manuscript requires additional results to clearly explain molecular mechanisms underlying the pathogenicity by CCDC146 loss-of-function.

Reviewer #2 (Public Review):

In whole exome sequencing of two patients suffering from MMAF syndrome, mutations of CCDC146 gene that result in premature stop codons were identified. The position of mutations could result in a truncated form of protein, thus whether these patients do indeed lack CCDC146 protein or if present, whether the truncated protein is functional, is unanswered by showing the CCDC146 protein localization only in the sperm from healthy donors. The main claim that CCDC146 protein is microtubule associated protein in the axoneme is well supported imaging expanded sperm flagellum to increase spatial resolution. However, the author's claim that the signal in the mid-piece is not specific is less supported by experimental evidence. The detection of CCDC146 in the sperm head is not further explored while TEM images show spermatogenesis defects in the manchette and acrosome formation. Increased detection of the CCDC146 protein in mouse sperm with sarkosyl supports its association with microtubules but does not exclude its potential role in the formation of sperm head. Overall, this study provides valuable information on CCDC146 function in male germ cells during spermatogenesis.

Reviewer #3 (Public Review):

Male infertility is an important health problem. Among pathologies with multiple morphological abnormalities of the flagellum (MMAF), only 50% of the patients have no identified genetic causes. It is thus primordial to find novel genes that cause the MMAF syndrome. In the current work, the authors follow up the identification of two patients with MMAF carrying a mutation in the CCDC146 gene. To understand how mutations in CCDC146 lead to male infertility, the authors generated two mouse models: a CCDC146-knockout mouse, and a knockin mouse in which the CCDC146 locus is tagged with an HA tag. Male CCDC146-knockout mice are infertile, which proves the causative role of this gene in the observed MMAF cases. Strikingly, animals develop no other obvious pathologies, thus underpinning the specific role of CCDC146 in male fertility.

The authors have carefully characterised the subcellular roles of CCDC146 by using a combination of expansion and electron microscopy. They demonstrate that all microtubule-based organelles, such as the sperm manchette, the centrioles, as well as the sperm axonemes are defective when CCDC146 is absent. Their data show that CCDC146 is a microtubule-associated protein, and indicate, but do not prove beyond any doubt, that it could be a microtubule-inner protein (MIP).<br /> This is a solid work that defines CCDC146 as a novel cause of male infertility. The authors have performed comprehensive phenotypic analysis to define the defects in CCDC146 knockout mice. Surprisingly, the authors provide virtually no information on the penetrance of those defects - in most cases they simply show descriptive micrographs. The message of this manuscript would have been more convincing if the key phenotypes of the CCDC146 knockout mice were quantified, in particular those shown in Fig. 2E, 7A, 11B, 13.

The manuscript text is well written and easy to follow also for non-specialists. The introduction and discussion chapters contain important background information that allow putting the current work into the greater context of fertility research. The figures could have been designed more carefully, with additional information on the genotype and other details such as the antibodies used etc. directly added to the figure panels, which would improve their readability. The author might also consider pooling small figures with complementary content into one bigger figure in order to group related information together, and again facilitate the reading of the manuscript.

Overall, this manuscript provides convincing evidence for CCDC146 being essential for male fertility, and illustrates this with a large panel of phenotypic observations, which however mostly lack quantification in order to judge their penetrance. Together, the work provides important first insights into the role of a so-far unexplored proteins, CCDC146, in spermatogenesis, thereby broadening the spectrum of genes involved in male infertility.

Reviewer #1 (Public Review):

This research article by Watabe T and colleagues characterizes PKA waves triggered by prostaglandin E2 (PGE2). What the author discovered is that waves of PKA occur both in vitro, in MDCK epithelial monolayers, and in vivo, in the ear epidermis in mice. The PKA waves are the consequence PGE2 discharge, that in turn is triggered by Calcium bursts. Calcium level and ERK activity intensity control that mechanism by acting at different levels.

This article is a technological tour de force using different biosensors and optogenetic actuators. What makes this article interesting is the combination of these tools together to dissect a complex, highly dynamic signaling pathway at the single-cell level. For this reason, this paper represents the essence of modern cell biology and paves the way for the cell biology of the future. However, we think that the paper in this stage is still partly descriptive in its nature, and more measurements are needed to increase the strength of the mechanistic insights. Also, the work is not conclusive, some results are over-interpreted, and more work has to be done if the authors want to support all their claims.

Reviewer #2 (Public Review):

This study visualizes a specific localized form of cell-to-cell communication and conveys very well with what dynamics and sensitivity this biological phenomenon occurs.

Using a FRET-based PKA biosensor, the authors observed that radial localized kinase activity changes spontaneously occur in adjacent cells of certain cell density. This phenomenon of radial propagation of PKA activity changes in groups of cells was further mechanistically elucidated and characterized. Interestingly, the authors found that individual cells in the cell groups form spontaneous Ca2+ transients, which at a certain strength can trigger the biosynthesis and release of prostaglandin E2 (PGE2). PGE2 then acts on the neighboring cells and triggers the increase of cAMP levels and the associated activation of the PKA via G-protein-coupled receptors (EP2 and EP4). In systematic, well-structured experiments, it was then found that the frequency of occurrence of such radial activations depends not only on the cell density but also on the activation state of the ERK MAP kinase pathway. The authors skillfully used various modern genetically encoded biosensors and other tools such as optogenetic tools to visualize and characterize an interesting biological phenomenon of cell-to-cell communication. The insights gained with these investigations produce a better understanding of the dynamics, sensitivity, and spatial extent with which such communications can occur in a cell network. It is also worth noting that the authors have not limited the studies to 2D cell culture in vitro, but were also able to confirm the findings in an animal model.

Reviewer #3 (Public Review):

The manuscript entitled "Calcium transients trigger switch-like discharge of prostaglandin E2 (PGE2) in an ERK-dependent manner" by Watabe et al. investigates the interaction between PGE2, PKA, calcium and ERK signaling in MCDK cells and in mouse epidermis. By expressing PKA, calcium and ERK activity reporters, the authors conclude that calcium transients trigger release of PGE2 that signals through GPCR receptors EP2 and EP4 to recruit PKA in neighboring cells. Determining the dynamics of signaling molecules and their interrelationships is important to fully identify the spatiotemporal aspects of signaling mechanisms. This study addresses some aspects of the calcium-PGE2-GPCR-Erk-PKA signaling pathway in a cell line and in mouse skin ex vivo.

However, the sequential recruitment of the different signaling molecules has been described in previous studies. Hence, the novelty of the findings is limited.<br /> Additionally, the interpretation of some of the data is too speculative, more likely explanations are not considered, or not well supported by the data presented. The main conclusions the authors present are potentially artifactual (ie, cell density-dependent phenomena) and the authors need to either do further experiments to better support their conclusions or re-interpret the physiological significance of their findings.

Reviewer #1 (Public Review):

The manuscript by Huang et al. examines the potential "self-policing" of Bacillus cells within a biofilm. The authors first discover the co-regulation of lethal extracellular toxins (BAs) and the self-immunity mechanisms; the global regulator spoA controls both. The authors further show that a subpopulation of cells co-express these genes and speculate that these cells engage in preferential cooperation for biofilm formation (over cells that produce neither). Based on previous literature, the authors then evaluate the relative fitness of the wild-type strain compared to mutants locked into either constantly exporting the toxins or permanently immune to these poisons. The wild-type exhibited increased fitness (compared to the mutants) for the tested biofilm conditions. The manuscript raises interesting ideas and provides a potential model to probe questions of cooperatively in Bacillus biofilms.

Strengths:<br /> - The authors use fluorescence-producing reporter strains to discern the spatial expression patterns within biofilms. This real-time imaging provides striking confirmation of their conclusions about shared co-regulation.<br /> - The authors also nicely deploy genetic constructs in microbiological assays to show how toxin production and immunity can influence biofilm phenotypes, including resilience to stress.

Concerns:<br /> - My biggest concern is that the claim of policing on a single-cell level needs more quantitive microscopy, particularly of the xylose-induced strain. The data support a more tempered consideration of self-policing via BAs and self-resistance in this Bacillus species. It seems sufficient that this manuscript opens the door for a novel and readily examinable system for examining potential cooperation and its molecular controls (without making broader claims).<br /> - The discussion is more speculative than the presented data warrants. For example, the speculation in lines 289 - 310 is not anchored in the results. It is hard for this reviewer to imagine how one would use the genetic framework and tools developed in this manuscript to address the ideas proposed in lines 289 - 310.<br /> - Some conclusions (in the results section) are more decisive than the data supports. For example, the microscopy of the PI staining (as presented in Figure 2 and the supplemental movies) does not prove that only non-expressing cells die. Yet the conclusion in line 143 states that "ECM and BAs producers selectively punish the nonproducing siblings." Also, the presented data shows many non-labeled cells without PI; why do some nearby non-gfp-expressing cells remain alive?

Reviewer #2 (Public Review):

In this study, Huang et al. investigated Bacillus velezensis, a species that colonizes plant roots as part of the rhizosphere. They showed that clone of B. velezensis SQR9 retains a division of labor of motile, planktonic subpopulation that do not produce extracellular matrix (ECM) and biofilm-forming sessile subpopulation that do produce ECM. Specifically, the sessile subpopulation secret toxins named bacillunoic acids (BAs) to kill some, but not all, of the planktonic subpopulation. The killing mechanism is mediated by a global regulator Spo0A, which co-activates BAs production and immunity, as well as ECM production. A strain that has a disrupted policing system revealed reduced biofilm formation, lower resistance to environmental stresses and alleviated ability to colonize plant roots. Overall, the toxin-mediated policing system is important for B. velezensis to mediate division of labor for enhancing population stability and ecological fitness when required (e.g., cell transition from a planktonic style to a multicellular style).

Reviewer #3 (Public Review):

In this manuscript, Huang et al. use a variety of experimental approaches to investigate division of labor and cheater "policing" during biofilm formation in Bacillus velezensis SQR9. The authors show that SQR9 cells differentiate into two populations during biofilm development - one cell type produces extracellular matrix (ECM) and the other does not (referred to as "cheaters"). The authors go on to demonstrate that the ECM producing cells utilize a bacillunoic acid toxin system to selectively kill cheaters, keeping the cheater population in check which maintains the stability of the community. Further, the authors demonstrate that coordination of ECM production and synthesis of bacillunoic acid/immunity via acetyl-CoA carboxylase is mediated in part by Spo0A. I find the work as a whole to be compelling and thorough, and I expect it to be of broad interest to various fields of research.

Reviewer #1 (Public Review):

The authors show that TrafE, which is one of the five Dictyostelium discoideum TRAF proteins, is recruited to the Mycobacterium-containing vacuoles (MCVs) and is required for membrane damage repair and xenophagy. They propose that the TrafE-Ub-ALIX axis is important for the regulation of Vps4, and, thereby, for the normal function of ESCRT. They also suggest that TrafE is involved in phagophore sealing.

Overall, the parts of membrane damage repair and xenophagy induction are convincing. Although mammalian TRAF6 was already reported to be involved in the ubiquitination of Chlamydia and Toxoplasma-containing vacuoles (Haldar et al. PNAS, 2015, https://www.pnas.org/doi/epdf/10.1073/pnas.1515966112), how TRAF6 is recruited to pathogen-containing vacuoles remained unknown. This study reveals that the recruitment of TrafE to MCVs is dependent on membrane damage or reduced membrane tension. This is novel. However, the part of phagophore closure is too preliminary. The evidence that TrafE is involved in the phagophore closure is mostly indirect and weak.

Reviewer #2 (Public Review):

Raykov et al. reported that TrafE, a member of the E3 ubiquitin ligase family similar to the TRAF proteins in mammalian cells, is essential for Dictyostelium discoideum to effectively respond to endolysosomal damage and defend itself against Mycobacterium marinum infection. First, the authors demonstrate that TrafE is recruited to the site of Mycobacterium-Containing Vacuole (MCV) damage along with ubiquitin molecules. This recruitment is necessary for the effective suppression of M. marinum growth in the cells. They also found that this response was not limited to the damage caused by M. marinum, but was also triggered by sterile damage caused by chemical compounds. Furthermore, the authors revealed that TrafE plays a role in the recruitment of Vps4 to sites of membrane damage and regulates the disassembly of ESCRT subunits. While TRAF6 has been previously implicated in ubiquitination in response to invaded bacteria in mammalian cells, this study provides solid data that furthers our understanding of the mechanism behind xenophagy. The authors conducted a thorough analysis to contribute to this field of research.

Reviewer #1 (Public Review):

This manuscript reports on a rapid and precise CRISPR/Cas9-mediated knock-in approach in the African turquoise killifish, an emerging vertebrate animal and gerontology model. More specifically, it describes an easily adoptable method to efficiently insert fluorescent reporters of different sizes at various genomic loci and to drive cell-type- and tissue-specific expression. This methodology will allow the development of humanized disease models and of cell-type specific molecular probes to study complex vertebrate biology, including aging biology, in the killifish. While this knock-in methodology is already widely used in common vertebrate animal models, the efficient generation of stable lines with germline transmission has been missing in killifish. As killifish have the shortest generation time of vertebrate animal models in laboratory conditions, show a rapid sexual maturity, and a short lifespan, the established method enables the generation of stable lines of homozygous transgenic vertebrate animals in 2-3 months. Overall, we believe this first report on efficient long (1.8kb) construct knock-in using CRISPR/Cas9 in the killifish establishes the killifish as a system for precise genetic engineering at scale, which has been challenging so far in vertebrates.

The establishment of this methodology will have a major impact in the field and be of extreme use within the scientific community. It will allow the development of scalable human disease models and integrate both genetics and age as risk factors, thus having the potential to identify future therapeutic targets for age-related diseases. It also has a generic character as the generated protocol can serve as a template for knock-in approaches in other emerging model organisms.

Although the reported data are of major interest and relevance to the scientific field, they are, as yet not sufficiently shown in convincing figures. The methodology is state-of-the-art and entails an extensive set of molecular, biochemical, and morphological/imaging technologies. While most of the data are nicely presented and accompanied by illustrative figures, the manuscript would benefit from the inclusion of a more detailed material and methods section, and a little more elaboration on morphometrical expression data in the results section, e.g, expression shown for all the studied genes in the larval fish, and a more critical discussion, that also highlights a few of the limitations, e.g., those related to the fast generation of homozygous F1 fish.

Reviewer #2 (Public Review):

The manuscript "Rapid and precise genome engineering in a naturally short-lived vertebrate" describes the development of a CRISPR- based knock-in technology in Nothobranchius furzeri, or the African turquoise killifish, an innovative model species for studying aging and age-related disorders. While Tol2 systems had been demonstrated to be successful in generating reporter killifish lines, endogenous reporters via knock-in had not been reported so far. The major strength of the paper is that the authors show that they have been successful in developing 5 different knock-in fish lines with large inserts (up to 1.8kb) with high efficiency. They have inserted single or dual fluorescent reporters and demonstrated expression in line with the expected pattern. This is a breakthrough in the field and this method can be instrumental for many researchers working with unusual model species, and in particular, will expand the killifish community toolbox.

While this is very promising, the paper would benefit from a more rigorous validation of the KI lines that were generated. The authors did not show a co-localisation of the target gene expression with the reporter to prove bona fide reporting. In addition, it was not clear whether the KI affects the endogenous expression level of the target genes. The targeting efficiency of the method is high, but the quantifications are based on rather limited numbers of animals, which might not yet be very robust. A larger number of animals would have strengthened the efficiency conclusion.

The figures of the manuscript are well designed and support the conclusions, but several contain information that is not discussed in the main text, such as (un)expected bands on gels, reporter staining in WT animals, and unusual staining patterns. The body text seems to ignore these and only discusses findings that are in line with the story. A key point to the efficiency of the method seems to be a chemical modification of the repair template, which was not disclosed in the method section which at the moment hampers replication.

Finally, the discussion is brief and does not benchmark the method to other CRISPR-based KI methods in Xenopus or more typical model species such as mouse.

In conclusion, this paper describes a breakthrough method for a rising animal model that would benefit from a more thorough validation. Full disclosure of the methodology will boost the generation of genetically edited killifish lines and aid in the establishment of this promising animal model.

Reviewer #3 (Public Review):

In this manuscript, the authors detail an exciting protocol to knock-in c-terminal tags at the endogenous locus of a gene of interest in the short-lived vertebrate, the African Turquoise Killifish. The technique is clearly explained and will be a significant advancement for the field. The method relies on the injection of a cocktail containing cas9 protein, proprietary-modified gRNA and dsDNA ordered from IDT, and a chemical enhancer of HDR.

I believe the authors demonstrate that killifish is a tractable emerging system to integrate stable fluorescent tags at desired loci. The method should be easy to reproduce since the components are all commercially available, but the proprietary nature of the modifications could make it a pricey technique for smaller labs. A protospacer adjacent motif (PAM) sequence near the desired insertion site is still a restriction using this method. That being said, I think this represents a significant advancement in knock-in methods that could be adopted in other systems. This manuscript is rather simple and straightforward, and I do not have additional criticisms or critiques.

As a side note, I think the brain sections look very professional, but since I am not a neurobiologist I will defer to the other reviewers about the accuracy and claims about the regions labeled.

For additional context, I suggest reading Wierson et al. 2020 and Seleit et al. 2022, which can both be found in the reference section.

Reviewer #1 (Public Review):

The work in this study builds on previous studies by some of the same authors and aims to test whether the heartbeat evoked response was modulated by the local/global auditory regularities and whether this differed in post-comatose patients with different contagiousness diagnosis. The authors report that during the global effect there were differences between the MCS and UWS patients.

The study is well constructed and analysed and has data from 148 participants (although the maximum in anyone group was 59). The reporting of the results is excellent and the conclusions are supported by the results presented. This study and the results presented are discussed as evidence that EEG based techniques maybe a low cost diagnostic tool for consciousness in post-comatose patients, although it should be stressed that here no classification of diagnostics was performed on the EEG data.

One potential weakness was the relationship between the design of the experiment and the analysis pathway for the results. If I have understood correctly the experimental design the auditory regularity changed on whether the local/global regularity was standard/deviant. In the analysis the differences between all conditions in which the local or global regularity were compared between the standard and deviant trials. This difference was then compared between MCS and UWS patient groups. For these analyses the results for the health and emerging MCS were not included. If this is correct it would be interesting to understand the motivation for this. Relatedly, it would be good to clarify if the effects reported were corrected for the multiple planned contrasts and if not why they should not be corrected.

Reviewer #2 (Public Review):

The goal of this study was to determine whether heartbeat-evoked responses measured at the scalp level with EEG, which followed regularity violations, could potencial help inform the diagnosis of patients with altered states of consciousness.

The authors use high density EEG and an oddball paradigm that probes violations of both local and global regularities. Four groups were considered including unresponsive wakefulness syndrome patents, minimally consciousness patients, emerging minimally consciousness patients and healthy controls. A difference was found between unresponsive and minimally conscious patients in the amplitude of the heartbeat evoked responses measure with EEG following a sound that violated a global regularity. Similarly, differences were found between the variance of these responses between the two above mentioned groups (N=58 and N=59), but no differences were found in relation to the healthy control group, which appear to be "in between" the two other groups (at least for global effect of HER). I thought this was a little counterintuitive and raises some questions about what this neural signature can tell us about the state of consciousness. Having said that, the healthy control sample was very small, more than 5 times smaller (only N=11).

In general, I thought the Discussion section was a little light on the implications of the findings, what they tell us about the brain mechanisms of consciousness and their different levels/states. A question is raised about whether it is necessary to lock EEG to heartbeats to find differences between patients. The data appeared to say that this is not the case but the discussion does not appear to reflect that very clearly.

Reviewer #3 (Public Review):

I found the results very interesting but wondered why the ERP results for the global vs. local effects are not reported. This analysis is mentioned in the methods section, but I do not find it in the results. Is this what is shown in the mid row in panel D? If yes, it should be made clearer. Is there a significant local and global deviant response in each patient group?

Additionally, eyeballing Figure 1, there are a few potential issues that may be affecting the conclusion re HER:

(1) Panel D top: it seems that the orange trace (MCS) is largely the same in both the "Local" and "global" condition. But the blue trace (UWS) shows a larger negative going deflection in the "global" case. Put differently, the UWS, but not MCS patients appear to generate a different response to the Global effect relative to the local effect. Is this the case?<br /> (2) There are some MCS subjects that appear to show a global effect that is larger than that observed in EMCS and healthy controls. How do you interpret these data?<br /> (3) How do you interpret the negative average HER data shown by many UWS patients?

Reviewer #1 (Public Review):

Kazrin appears to be implicated in many diverse cellular functions, and accordingly, localizes to many subcellular sites. Exactly what it does is unclear. The authors perform a fairly detailed analysis of Kazrin in-cell function, and find that it is important for the perinuclear localization of TfN, and that it binds to members of the AP-1 complex (e.g., gamma-adaptin). The authors note that the C-terminus of Kazrin (which is predicted to be intrinsically disordered) forms punctate structures in the cytoplasm that colocalize with components of the endosomal machinery. Finally, the authors employ co-immunoprecipitation assays to show that both N and C-termini of Kazrin interacts with dynactin, and the dynein light-intermediate chain.

Much of the data presented in the manuscript are of fairly high quality and describe a potentially novel function for Kazrin C. However, I had a few issues with some of the language used throughout, the manner of data presentation, and some of their interpretations. Most notably, I think in its current form, the manuscript does not strongly support the authors' main conclusion: that Kazrin is a dynein-dynactin adaptor, as stated in their title. Without more direct support for this function, the authors need to soften their language. Specific points are listed below.

Major comments:<br /> 1) I agree with the authors that the data provided in the manuscript suggest that Kazrin may indeed be an endosomal adaptor for dynein-dynactin. However, without more direct evidence to support this notion, the authors need to soften their language stating as much. For example, the title as stated would need to be changed, as would much of the language in the first paragraph of the discussion. Alternatively, the manuscript could be significantly strengthened if the authors performed a more direct assay to test this idea. For example, the authors could use methods employed previously (e.g., McKenney et al., Science 2014) to this end. In brief, the authors can simply use their recombinant Kazrin C (with a GFP) to pull out dynein-dynactin from cell extracts and perform single molecule assays as previously described.<br /> 2) I'm not sure I agree with the use of the term 'condensates' used throughout the manuscript to describe the cytoplasmic Kazrin foci. 'Condensates' is a very specific term that is used to describe membraneless organelles. Given the presumed association of Kazrin with membrane-bound compartments, I think it's more reasonable to assume these foci are quite distinct from condensates.<br /> 3) The authors note the localization of Tfn as perinuclear. Although I agree the localization pattern in the kazKO cells is indeed distinct, it does not appear perinuclear to me. It might be useful to stain for a centrosomal marker (such as pericentrin, used in Figure 5B) to assess Tfn/EEA1 with respect to MT minus ends.<br /> 4) "Treatment with the microtubule depolymerizing drug nocodazole disrupted the perinuclear localization of GFP-kazrin C, as well as the concomitant perinuclear accumulation of EE (Fig. 5C & D), indicating that EEs and GFP-kazrin C localization at the pericentrosomal region required minus end-directed microtubule-dependent transport, mostly affected by the dynactin/dynein complex (Flores-Rodriguez et al., 2011)."<br /> - I don't agree that the nocodazole experiment indicates that minus end-directed motility is required for this perinuclear localization. In the absence of other experiments, it simply indicates that microtubules are required. It might, however, "suggest" the involvement of dynein. The same is true for the subsequent sentence ("Our observations indicated that kazrin C can be transported in and out of the pericentriolar region along microtubule tracks...").<br /> 5) Although I see a few examples of directed motion of Tfn foci in the supplemental movies, it would be more useful to see the kymographs used for quantitation (and noted by the authors on line 272). Also related to this analysis, by "centripetal trajectories", I assume the authors are referring to those moving in a retrograde manner. If so, it would be more consistent with common vernacular (and thus more clear to readers) to use 'retrograde' transport.<br /> 6) The error bars on most of the plots appear to be extremely small, especially in light of the accompanying data used for quantitation. The authors state that they used SEM instead of SD, but their reasoning is not stated. All the former does is lead to an artificial reduction in the real deviation (by dividing SD by the square root of whatever they define as 'n', which isn't clear to me) of the data which I find to be misleading and very non-representative of biological data. For example, the error bars for cell migration speed in Figure 2B suggest that the speeds for WT cells ranged from ~1.7-1.9 µm/sec, which I'm assuming is largely underrepresenting the range of values. Although I'm not a statistician, as someone that studies biochemical and biological processes, I strongly urge the authors to use plots and error bars that more accurately describe the data to your readers (e.g., scatter plots with standard deviation are the most transparent way to display data).

Reviewer #2 (Public Review):

A distinguishing feature of live cells is that intracellular organelles move powered by molecular motors. However, the arsenal of molecular motors is limited relative to the vast variety of cargoes and processes involving long-distance movement. Cells cope with this mismatch by using adaptors that "bridge" a given molecular motor with a specific cargo, whose identity is dictated by peripheral membrane proteins, such RABs, or identity-determining lipids, such as PtdIns3P. Cytoplasmic dynein walks towards the minus end of the microtubules. A score of cellular processes is dependent on dynein, such that deficient regulation of the motor has deep consequences in cellular homeostasis, and the identification of new adapters is of broad interest, both basic and, potentially, clinical.

Dynein adaptors usually stabilize the binding of dynactin to dynein using coiled-coil regions to longitudinally embrace dynactin, holding it to the elongated dynein cap of the super-complex. Not only do they adapt cargo but additionally increase the processivity and speed of the motor. In this manuscript, Julie and collaborators present evidence that a protein denoted kazrin, which is involved in a variety of processes, is actually an adaptor connecting endosome domains specialized in recycling cargo back to the surface of the cell by way of the RAB11 perinuclear recycling endosome. The topic is important, experiments have been carefully conducted and well controlled and display items faithfully guide readers through the main findings. However, I feel that the evidence that kazrin is a dynein adaptor is somewhat thin and that it could be improved with relatively little additional work. The manuscript would also benefit from better integration of the conclusions in the current state of the art in the dynein field.

Reviewer #3 (Public Review):

The authors sought to define a role for the Kazrin protein in the endosomal pathway. This effort is built on past observations of the impact of Kazrin over-expression on clathrin-mediated endocytosis. However, new Kazrin depletion experiments revealed no impact on endocytosis but a defect in the movement of early endosomes towards the nucleus. This observation that Kazrin depletion results in the dispersion of early endosomes is supported by shRNA knockdowns, CRISPR KO experiments, and the rescue of the phenotype by restoring Kazrin expression. The generalizability of the findings is supported by experiments in 2 different cell types (COS7 and MEFs). A direct role for Kazrin in linking early endosomes to dynein-dynactin is supported by observations that Kazrin is early present on endosomes and interacts with proteins of endosomes as well as with dynein-dynactin. A possible interaction with PI3P (a lipid enriched on early endosomes) is supported by a lipid binding assay. However, definitive results on this interaction would require validation by additional methods. With respect to the dynein-dynactin interactions, the authors strengthen confidence in this interaction and its putative functional relevance by identifying sequence homology between Kazrin and BICDR1 and hook3, 2 proteins with well-characterized functionally relevant roles in linking dynein-dynactin to cargos. The methods that were used to establish these functions for Kazrin were well aligned with the goals of this research and with the conclusions that were drawn. Efforts were made to quantify key observations and to provide statistical tests to establish the significance of differences that were observed. While these quantitative efforts are generally sufficient to support the major claims of the study, the data presentation would be stronger if the authors could better define the experimental sample size and the number of replicates that were performed for each experiment. Furthermore, the idea that the C-terminal region of Kazrin helps to promote the formation of "condensates" was not thoroughly supported by experimental data even if the presence of an intrinsically disordered region is supportive of this interpretation of the formation of Kazrin puncta on or near endosomes.

Reviewer #1 (Public Review):

Nicotine preference is highly variable between individuals. The paper by Mondoloni et al. provided some insight into the potential link between IPN nAchR heterogeneity with male nicotine preference behavior. They scored mice using the amount of nicotine consumption, as well as the rats' preference of the drug using a two-bottle choice experiment. An interesting heterogeneity in nicotine-drinking profiles was observed in adult male mice, with about half of the mice ceasing nicotine consumption at high concentrations. They observed a negative association of nicotine intake with nicotine-evoked currents in the antiparticle nucleus (IPN). They also identified beta4-containing nicotine acetylcholine receptors, which exhibit an association with nicotine aversion. The behavioral differentiation of av vs. n-avs and identification of IPN variability, both in behavioral and electrophysiological aspects, add an important candidate for analyzing individual behavior in addiction.

The native existence of beta4-nAchR heterogeneity is an important premise that supports the molecules to be the candidate substrate of variabilities. However, only knockout and re-expression models were used, which is insufficient to mimic the physiological state that leads to variability in nicotine preference.

Reviewer #2 (Public Review):

In the current study, Mondoloni and colleagues investigate the neural correlates contributing to nicotine aversion and its alteration following chronic nicotine exposure. The question asked is important to the field of individual vulnerability to drug addiction and has translational significance. First, the authors identify individual nicotine consumption profiles across isogenic mice. Further, they employed in vivo and ex vivo physiological approaches to defining how antiparticle nuclei (IPn) neuronal response to nicotine is associated with nicotine avoidance. Additionally, the authors determine that chronic nicotine exposure impairs IPn neuronal normal response to nicotine, thus contributing to higher amounts of nicotine consumption. Finally, they used transgenic and viral-mediated gene expression approaches to establish a causal link between b4 nicotine receptor function and nicotine avoidance processes.

The manuscript and experimental strategy are well designed and executed; the current dataset requires supplemental analyses and details to exclude possible alternatives. Overall, the results are exciting and provide helpful information to the field of drug addiction research, individual vulnerability to drug addiction, and neuronal physiology. Below are some comments aiming to help the authors improve this interesting study.

1. The authors used a two-bottle choice behavioral paradigm to investigate the neurophysiological substrate contributing to nicotine avoidance behaviors. While the data set supporting the author's interpretation is compelling and the experiments are well-conducted, a few supplemental control analyses will strengthen the current manuscript.<br /> a. The bitter taste of nicotine might generate confounds in the data interpretation: are the mice avoiding the bitterness or the nicotine-induced physiological effect? To address this question, the authors mixed nicotine with saccharine, thus covering the bitterness of nicotine. Additionally, the authors show that all the mice exposed to quinine avoid it, and in comparison, the N-Av don't avoid the bitterness of the nicotine-saccharine solution. Yet it is unclear if Av and N-Av have different taste discrimination capacities and if such taste discrimination capacities drive the N-Av to consume less nicotine. Would Av and N-Av mice avoid quinine differently after the 20-day nicotine paradigm? Would the authors observe individual nicotine drinking behaviors if nicotine/quinine vs. quinine were offered to the mice?<br /> b. Metabolic variabilities amongst isogenic mice have been observed. Thus, while the mice consume different amounts of nicotine, changes in metabolic processes, thus blood nicotine concentrations, could explain differences in nicotine consumption and neurophysiology across individuals. The authors should control if the blood concentration of nicotine metabolites between N-Av and Av are similar when consuming identical amounts of nicotine (50ug/ml), different amounts (200ug/ml), and in response to an acute injection of a fixed nicotine quantity.

2. Av mice exposed to nicotine_200ug/ml display minimal nicotine_50ug/ml consumption, yet would Av mice restore a percent nicotine consumption >20 when exposed to a more extended session at 50ug/kg? Such a data set will help identify and isolate learned avoidance processes from dose-dependent avoidance behaviors.

3. The author should further investigate the basal properties of IPn neuron in vivo firing rate activity recorded and establish if their spontaneous activity determines their nicotine responses in vivo, such as firing rate, ISI, tonic, or phasic patterns. These analyses will provide helpful information to the neurophysiologist investigating the function of IPn neurons and will also inform how chronic nicotine exposure shapes the IPn neurophysiological properties.

Reviewer #3 (Public Review):

The manuscript by Mondoloni et al characterizes two-bottle choice oral nicotine consumption and associated neurobiological phenotypes in the antiparticle nucleus (IPN) using mice. The paper shows that mice exhibit differential oral nicotine consumption and correlate this difference with nicotine-evoked inward currents in neurons of the IPN. The beta4 nAChR subunit is likely involved in these responses. The paper suggests that prolonged exposure to nicotine results in reduced nAChR functional responses in IPN neurons. Many of these results or phenotypes are reversed or reduced in mice that are null for the beta4 subunit. These results are interesting and will add a contribution to the literature. However, there are several major concerns with the nicotine exposure model and a few other items that should be addressed.

Strengths:<br /> Technical approaches are well-done. Oral nicotine, electrophysiology, and viral re-expression methods were strong and executed well.<br /> The scholarship is strong and the paper is generally well-written. The figures are high-quality.

Weaknesses:<br /> Two bottle choice (2BC) model. 2BC does not examine nicotine reinforcement, which is best shown as a volitional preference for the drug over the vehicle. Mice in this 2BC assay (and all such assays) only ever show indifference to nicotine at best - not preference. This is seen in the maximal 50% preference for the nicotine-containing bottle. 2BC assays using tastants such as saccharin are confounded. Taste responses can very likely differ from primary reinforcement and can be related to peripheral biology in the mouth/tongue rather than in the brain reward pathway. Moreover, this assay does not test free choice, as nicotine is mixed with water which the mice require to survive. Since most concentrations of nicotine are aversive, this may create a generalized conditioned aversion to drinking water - detrimental to overall health and a confounding factor. What plasma concentrations of nicotine are achieved by 2BC? When nicotine is truly reinforcing, rodents and humans titrate their plasma concentrations up to 30-50 ng/mL. The Discussion states that oral self-administration in mice mimics administration in human smokers (lines 388-389). This is unjustified and should be removed. Similarly, the paragraph in lines 409-423 is quite speculative and difficult or impossible to test. This paragraph should be removed or substantially changed to avoid speculation. Overall, the 2BC model has substantial weaknesses, and/or it is limited in the conclusions it will support.

Statistical testing on subgroups. Mice are run through an assay and assigned to subgroups based on being classified as avoiders or non-avoiders. The authors then perform statistical testing to show differences between the avoiders and non-avoiders. It is circular to do so. When the authors divided the mice into avoiders and non-avoiders, this implies that the mice are different or from different distributions in terms of nicotine intake. Conducting a statistical test within the null hypothesis framework, however, implies that the null hypothesis is being tested. The null hypothesis, by definition, is that the groups do NOT differ. Obviously, the authors will find a difference between the groups in a statistical test when they pre-sorted the mice into two groups, to begin with. Comparing effect sizes or some other comparison that does not invoke the null hypothesis would be appropriate.

Decreased nicotine-evoked currents following passive exposure to nicotine in minipumps are inconsistent with published results showing that similar nicotine exposure enhances nAChR function via several measures (Arvin et al, J Neurosci, 2019). The paper does acknowledge this previous paper and suggests that the discrepancy is explained by the fact that they used a higher concentration of nicotine (30 uM) that was able to recruit the beta4-containing receptor (whereas Arvin et al used a caged nicotine that was unable to do so). This may be true, but the citation of 30 uM nicotine undercuts the argument a bit because 30 uM nicotine is unlikely to be achieved in the brain of a person using tobacco products; nicotine levels in smokers are 100-500 nM. It should be noted in the paper that it is unclear whether the down-regulated receptors would be active at concentrations of nicotine found in the brain of a smoker. The statement in lines 440-41 ("we show that concentrations of nicotine as low as 7.5 ug/kg can engage the IPN circuitry") is misleading, as the concentration in the water is not the same as the concentration in the CSF since the latter would be expected to build up over time. The paper did not provide measurements of nicotine in plasma or CSF, so concluding that the water concentration of nicotine is related to plasma concentrations of nicotine is only speculative.

The results in Figure 2E do not appear to be from a normal distribution. For example, results cluster at low (~100 pA) responses, and a fraction of larger responses drive the similarities or differences.

10 mg/kg/day in mice or rats is likely a non-physiological exposure to nicotine. Most rats take in 1.0 to 1.5 mg/kg over a 23-hour self-administration period (O'Dell, 2007). Mice achieve similar levels during SA (Fowler, Neuropharmacology 2011). Forced exposure to 10 mg/kg/day is therefore 5 to 10-fold higher than rodents would ever expose themselves to if given the choice. This should be acknowledged in a limitations section of the Discussion.

Are the in vivo recordings in IPN enriched or specific for cells that have a spontaneous firing at rest? If so, this may or may not be the same set/type of cells that are recorded in patch experiments. The results could be biased toward a subset of neurons with spontaneous firing. There are MANY different types of neurons in IPN that are largely intermingled (see Ables et al, 2017 PNAS), so this is a potential problem.

Related to the above issue, which of the many different IPN neuron types did the group re-express beta4? Could that be controlled or did beta4 get re-expressed in an unknown set of neurons in IPN? There is insufficient information given in the methods for verification of stereotaxic injections.

Data showing that alpha3 or beta4 disruption alters MHb/IPN nAChR function and nicotine 2BC intake is not novel. In fact, some of the same authors were involved in a paper in 2011 (Frahm et al., Neuron) showing that enhanced alpha3beta4 nAChR function was associated with reduced nicotine consumption. The present paper would therefore seem to somewhat contradict prior findings from members of the research group.

Sex differences. All studies were conducted in male mice, therefore nothing was reported regarding female nicotine intake or physiology responses. Nicotine-related biology often shows sex differences, and there should be a justification provided regarding the lack of data in females. A limitations section in the Discussion section is a good place for this.

Reviewer #1 (Public Review):

Cerebellar parallel fiber to Purkinje cell synapses display multiple forms of long-term plasticity, expressed in both presynaptic and postsynaptic compartments. At this synapse, a prominent form of presynaptic LTP was once thought to operate through cAMP-dependent activation of PKA, and subsequent phosphorylation of RIM1a. However, recent studies have questioned this hypothesis. LTP is not blocked by selective inhibitors of PKA, or by mutations in Rim1a designed to block PKA-dependent serine phosphorylation. In this study, Wang and colleagues use a wide array of pharmacology and genetics to elucidate a potential signaling cascade for presynaptic LTP in parallel fibers, where cAMP activates EPAC, leading to PKCε-dependent phosphorylation of RIM1α. Presynaptic ablation of either EPAC or PKCε leads to loss of presynaptic LTP and forskolin-induced potentiation. The experiments are generally well conceived and executed. The findings provide a new framework for understanding how presynaptic cAMP elevations can alter vesicle release machinery and drive synaptic plasticity, and open new avenues for exploration at synapses throughout the CNS. The manuscript could be improved by better a more transparent citation of previous studies and a more open discussion of the unknown steps in the newly-elucidated signaling cascade.

Reviewer #2 (Public Review):

The authors successfully show that how EPAC and PKCε work together to recruit presynaptic proteins for neurotransmitter release instead of synaptic vesicle formation since the absence of EPAC and PKCε does not affect the number of synaptic vesicles. In addition, the data clearly demonstrate that EPAC and PKCε function specifically at the presynaptic terminals and thus is required for induction of presynaptic LTP. Their suggested EPAC- PKCε module is also essential for proper cerebellar motor performance and motor learning.

Furthermore, the order of data analysis perfectly matches the logical explanation of the entire story. The authors first prove that EPAC and PKCε, together with RIM1a, are necessary for neurotransmitter release at the presynaptic terminal. Then, by using specific knockdown mice of presynaptic granule cells, both proteins contribute to the release of synaptic vesicles in that only the frequencies of EPSC have changed. In addition, presynaptic LTP is only induced with the presence of EPAC and PKCε, highlighting the important role of the EPAC- PKCε module. Ultimately, the impact of EPAC and PKCε is shown by conducting the behavior tasks including OKR, VOR, and VVOR.

The authors suggest the missing link between EPAC and RIM1 is PKCε. Phosphorylation of RIM1 by PKCε is a novel signaling cascade found in this paper. The authors' data from the heterologous expression system and cerebellar granule cell-specific PKCε KO mice indicate that PKCε can regulate RIM1Threonine phosphorylation.<br /> The EPAC-PKCε unit is essential to both presynaptic neurotransmitter release and presynaptic LTP in parallel fiber-Purkinje cell synapse. Future work is necessary to dissect which is responsible for cerebellar motor performance and motor learning.

The study provides the necessity of exploring the new part of the motor learning circuit since the significant focus of cerebellar motor learning has been only confined to postsynaptic plasticity. Generally, postsynaptic plasticity is affected by the presynaptic properties, such as presynaptic vesicle release and recycling of neurotransmitters at the synapse. Also, the presynaptic terminal, which can be referred to as an inducing force of the postsynaptic plasticity, does not merely release the neurotransmitters at a constant rate; they also change as a result of incoming stimuli. Such change is called presynaptic plasticity. Therefore, it should be further scrutinized how presynaptic plasticity is conducted and determined.

Reviewer #3 (Public Review):

The manuscript by Wang et al. investigates the mechanisms and physiological consequences of presynaptic plasticity at parallel fiber synapses of the cerebellum. Using a wide range of molecular, cellular, and genetic approaches, they show that a signaling pathway involving cAMP, EPAC, and PKCε leads to phosphorylation of RIM1α in parallel fiber terminals. Using EM and electrophysiology, they show that RIM1α (by forming a protein complex with Rab3A and Munc13) promotes docking of synaptic vesicles and increased vesicle release probability. The authors demonstrated that EPAC/PKCε are necessary for the induction of presynaptic LTP at parallel fiber synapses. The authors then extend this work to the behavioral level by showing the mice lacking EPAC or PKCε expression in cerebellar granule cells lack presynaptic LTP at parallel fiber synapses and display motor learning deficits during adaptation of the vestibular ocular reflex, a common test of cerebellum-dependent learning. The mechanisms of synaptic plasticity at parallel fiber synapses have been long investigated, but still remain unclear. This work makes a significant and convincing contribution to understanding presynaptic plasticity mechanisms. Likewise, the relative contribution of various pre- and postsynaptic forms of plasticity to cerebellar learning has long been debated but remains unsettled. This work provides novel evidence that presynaptic plasticity contributes to motor learning, possibly complimenting postsynaptic forms of plasticity. However, given the experimental conditions, it is difficult to extrapolate the slice electrophysiology findings to mechanisms of motor learning in vivo (see detailed comments below).

This manuscript provides compelling evidence for the role of EPAC and PKCε in regulating RIM1α and vesicle release. The authors use an impressive range of cellular, molecular, and genetic approaches to establish each link in the chain of the cAMP/EPAC/PKC signaling. In general, the conclusions are well supported by the data, often with multiple approaches used to address each question. In a few cases, the conclusions are overstated or not well supported by the data.

Specific comments:

1. While the data are generally very convincing, the authors overstated the conclusions in several instances. For example, the authors state that EPAC and PKCε are "required" or "essential" for vesicle docking and release. However, the author's own data show that both vesicle docking and release are clearly present (though reduced) in the absence of EPAC and PKCε, demonstrating they are not absolutely required. The language could be toned down without diminishing the impact of the excellent work.

2. The authors used analysis of cumulative EPSCs to estimate release probability (Pr) and the readily releasable pool (RRP) size. Unfortunately, this approach is likely not suited for low release probability synapses such as parallel fibers (the authors estimate Pr to be 0.04-0.06). Thanawala and Regehr (2016) extensively investigated the validity of cumulative EPSC analysis under a variety of conditions. They found that this analysis produces large errors in Pr and RRP at synapses with a Pr below ~0.2. In addition, 20 Hz EPSC stimulation (as was used here) produces much larger errors compared to the more commonly used 100 Hz stimulation. Between the low Pr at parallel fiber synapses and the low stimulus frequency used, it is likely that the cumulative EPSC analysis provides a poor estimate of Pr and RRP in this case.

3. Using a combination of genetic knockouts and pharmacology, this paper convincingly shows that presynaptic EPAC/PCKε are necessary for presynaptic LTP, but do not alter postsynaptic LTP/ LTD. However, given the experimental conditions in the slice experiments, it is difficult to extrapolate from the slice data to in vivo plasticity during motor learning. Synaptic plasticity in the cerebellar cortex is quite complex and can depend significantly on age, temperature, location, and ionic conditions. Unfortunately, these were not well matched between slice and in vivo experiments. Slice experiments used P21 mice, while in vivo experiments were performed at P60. Slice experiments were performed in the vermis, while VOR expression/adaptation generally requires the vestibulo-cerebellum/flocculus. Slice experiments were performed at room temperature, not physiological temperature. Lastly, slice experiments used 2 mM Ca2+ in the ACSF, somewhat high compared to the physiological extracellular fluid. Each of these factors can significantly affect the induction and expression of plasticity. These differences leave one wondering how well the slice data translate into understanding plasticity in the in vivo context.

4. Many experiments use synaptosomal preparation. The authors identify excitatory synapses by VGLUT labelling, but it is unclear how, or if, the authors distinguish between parallel fiber, climbing fiber, and mossy fiber synaptosomes. These synapses likely have very different properties and molecular composition, some quantification or estimation of how many synaptosomes are derived from each type of synapse would be helpful.

5. The math1-cre mouse line is used to selectively knockout EPAC or PKCε expression in cerebellar granule cells. This line also expresses Cre in unipolar brush cells (UBCs) of the cerebellum (Wang et al., 2021). This is likely not a factor in the molecular/slice studies of EPAC/PKC signaling, but UBC dysfunction could play a role in motor/learning deficits observed in vivo. This possibility is not considered in the text.

Joint Public Review:

This paper presents two new tools for investigating GLP-1 signaling. The genetically encoded sensor GLPLight1 follows the plan for other GPCR-based fluorescent sensors, inserting a circularly permuted GFP into an intracellular loop of the GPCR. The light-uncaged agonist peptide, photo-GLP1, has no detectable agonist activity (as judged by the GLPLight1 sensor) until it is activated by light. However, based on the current characterization, it is unclear how useful either of these tools will be for investigating native GLP-1 signaling.

The GLPLight1 sensor has a strong fluorescent response to GLP-1 with an EC50 of ~10 nM, and its specificity is high, as shown by lack of response to ligands of related class B GPCRs. However, the native GLP1R enables biological responses to concentrations that are ~1000-fold lower than this (as shown, for instance, in a supplemental figure of this paper). This makes it difficult to see how the sensor will be useful for in vivo detection of GLP-1 release, as claimed; although there may be biological situations where the concentration is adequate to stimulate the sensor, this is not established. Data using a GLP-1 secreting cell line suggest that the sensor has bound some of the released GLP-1, but it is difficult to have confidence without seeing an actual fluorescence response to stimulated release.

Alternatively, the sensor might be used for drug screening, but it is unclear that this would be an improvement over existing high-throughput methods using the cAMP response to GLP1R activation (since those are much more sensitive and also allow detection of signaling through different downstream pathways).

The utility of the caged agonist PhotoGLP1 is similarly unclear. The data demonstrate a substantial antagonism of GLP-1 binding by the still-caged compound, and it is therefore unclear whether the kinetics of the response to PhotoGLP1 itself would mimic the normal activation by GLP-1 in the absence of the caged compound. A further concern is that the light-dependence of the agonist effect of PhotoGLP1 was evaluated only with the GLPLight1 sensor and not with GLP1R signaling itself, which is 1000x more sensitive and which would be the presumed target of the tool. In addition, PhotoGLP1 is based upon native GLP-1, which is rapidly truncated and inactivated by the peptidase DPPIV, expressed in most cell types, and expressed at very high levels in the plasma. The utility of PhotoGLP1 is therefore limited to acute (minutes) in vitro experiments.

Reviewer #1 (Public Review):

Using a combination of structural biology methods, this report aims at describing the auto-inhibited architecture of kinesin 1 either as homodimers or hetero-tetramers. Hence, the multiple contacts between the protein domains and their folding pattern is addressed using cross-linking mass spectrometry (XL-MS), negative stain electron microscopy and Alpha Fold based structure prediction. Based on the existing literature, the key domains and amino acids responsible for kinesin 1 inhibited state were not clearly deciphered. The synergetic use of different methods now seems to describe in detail the molecular cues which could induce kinesin-1 refolding and opening. Multiple interactions between the different domains seem to induce the folded conformation.

The combination of methodologies is an efficient way to unravel details that could not be addressed previously. The paper is well written. However, the methodology is sometimes not sufficiently detailed and the paper would benefit from additional explanations and demonstrations. The methods for generating the electron microscopy data and its relevance and quality, for instance, are barely described. In addition, the conclusions drawn would be more convincing if similar investigations would be carried out similarly for all isoforms (KIF5B and FIF5C) in parallel.

This article raises the potential strength and power of deep learning structure prediction methods combined simultaneously with other structural biology methods to answer specific questions. In the present context, this study will certainly be helpful to reveal and understand the activation mechanism of kinesin motor proteins.

Reviewer #2 (Public Review):

The authors sought to define the molecular structure of autoinhibited Kinesin-1, which is the major kinesin providing plus-end directed transport on microtubules. The paper reports a structural model of full-length kinesin-1 which builds on the known folded conformation of kinesin-1 and describes its autoinhibitory mechanism using cryo-EM, alphafold structural predictions, cross-linking and mass spectrometry. The authors study the conformation of dimeric Kinesin Heavy Chain (KHC) and tetrameric KHC bound to the Kinesin Light Chains (KLCs), where KLC stabilize the autoinhibited conformation. The combination of these various approaches leads to an integrated molecular model of autoinhibited Kinesin-1. Until now, there was some debate over the role of the small coiled coil 3 (a and b) and where the hinge region of Kinesin-1. The authors resolve this question and present data indicating the hinge is between cc3a and cc3b.

In some places the absence of crosslinks is reported as a lack of interaction, however it could also be that there are no residues that can be crosslinked in this region. The distance is also not reported in the figures so we do not know how valid these model are. For example for TRAP binding to KHC, there are not many crosslinks but it is not clear if there was an issue with the complex assembly or crosslinking reaction-as there is no EM data of this complex. There is also a structural model of KHC and KLC (Fig 4) where the domains are too far apart for the crosslinks to be allowed, raising a question about whether that model is correct or not. The structural data are supported by single molecule motility assays with various mutants of Kinesin-1, which greatly help characterising the domains functionally.

Overall there are some interesting novel data on the autoinhibitory mechanism of Kinesin-1, with well performed and analyzed data with KLC and TRAP. The topic and paper will be of interest to many.

Reviewer #2 (Public Review):

To date, only a handful of studies have addressed the importance of AGS3, a paralog of the relatively well-characterized spindle orientation factor LGN. The authors now show that AGS3 acts as a negative regulator of LGN and propose that this activity could work through competition for binding partner(s). Remarkably, regulation is temporally restricted in such a way that the conserved role played by LGN in metaphase spindle orientation is unaffected. Instead, AGS3 regulates a post-metaphase function for LGN, namely Telophase Correction.

The article is well-written, the experiments are performed at a high level, and the claims are generally supported by the data. Two main points of confusion are raised in the current version. 1) The authors show that AGS3 regulates cortical localization of LGN, but would need to clarify how LGN is being affected. 2) The authors propose in the discussion that AGS3 might exert its regulatory effect through competition for NuMA, an important binding partner for LGN, but would need to clarify how and why NuMA would be involved in Telophase Correction.

Reviewer #1 (Public Review):

The model put forward by the authors in this manuscript is a simple and exciting one, explaining the function of AGS3 as a negative regulator of LGN, acting as a 'dominant-negative' version of LGN. Overall, the results support the model very well, and the results shown in Fig 6, which clearly reveal the functional relevance of AGS3, add strength to the paper.

In Figures 3A and B, the authors claim that AGS3 overexpression leads to depolarization of LGN in epidermal stem cells. However, in the example provided in Figure 3A, the LGN signal appears to be stronger than the control, with more LGN still on the apical side (many would categorize this as 'apically polarized'). In the scoring shown in Figure 3B, I am not sure if 'eyeballing' is the right way to decide whether it is polarized/depolarized/absent. The authors should come up with a bit more quantitative method to quantify the localization/amount of LGN and explain the method well in the manuscript. A similar concern regarding the determination of the LGN localization pattern applies to the rest of figure 3 as well.

Reviewer #3 (Public Review):

This paper examines the mechanisms that control division orientation in the basal layers of the epidermis. Previous work established LGN as a key promoter of divisions where one of the siblings populates the differentiated layers (perpendicular). This work addresses two important, related issues - the mechanisms that determine whether a particular division is planar vs perpendicular, and the function of AGS3, and LGN paralog that has been enigmatic. A central finding is that AGS3 is required for the normal distribution of planar and perpendicular divisions (roughly equal) such that in its absence the distribution is skewed towards the perpendicular. Interestingly, however, the authors find that AGS3 has no detectable effect on orientation if the orientation is measured at anaphase. This timing aspect builds upon previous work from this group demonstrating a phenomenon they term "telophase correction" in which the orientation changes at the latest phases of division (and possibly post division?). Thus AGS3 seems to exert its effect using these later mechanisms and this is supported by further analysis by the authors. Importantly, the authors show that AGS3 acts through LGN, based on localization data and an epistasis analysis. The function of AGS3 has been highly enigmatic so resolving this issue while providing a useful step towards understanding how the division orientation decision is made, makes for exciting progress towards an important problem. I found the overall narrative and presentation to be quite good and especially appreciated the thoughtful discussion section that did an excellent job of putting the results in context and speculating how unknown aspects of the mechanism might work based on current clues. With that said, I think there are some important issues that should be resolved.

Regarding the orientation measurements, the authors should specify how the midbody marker was used to mark sibling cells, especially given the midbody can move following division. For example, how can the authors be confident that the siblings in the middle panel of 1A are correct and not an adjacent cell?

Regarding quantification, it would be useful for the authors to comment on how the following would influence their measurements: 1) movements along the z-axis, and 2) movement of the nucleus within the cell.

A similar question is how much telophase correction really happens in telophase. How confident are the authors that the process actually occurs during division and not subsequent to it? What is drawn in their previous paper and in Figure 7A implies that post-division movements may be important. It would be useful for the authors to comment on whether they can make the distinction and whether or not it might be important.

Does the division angle in the AGS3 OE experiment (Figure 1D) correlate with AGS3 levels within the cell?

I found the localization data to be the weakest part of the paper and feel that some reconsideration and reanalysis are warranted.

First, the quantifications in Figures 2C, 3B, and 3F are unnecessarily vague scoring-based metrics. In 2C, "Localization pattern" should be replaced with membrane/cytoplasm ratio or an equivalent quantification. In 3B "LGN localization" should be replaced with apical/cytoplasmic and apical/basal ratios or equivalents. In 3F, "Polarized LGN frequency" should be replaced with apical/basal ratio or equivalent. It seems to me that non-AI processed data would be most appropriate for these quantifications unless such processing can be justified.

Second, it is important to note that the cytoplasmic localization of AGS3 does not allow one to conclude that AGS3 is not on the membrane. Unfortunately, high cytoplasmic signal can preclude the determination of membrane-bound signal.

Finally, I had difficulty reconciling the images of LGN shown in Figure 3 with the conclusions made by the authors.

The challenge of the localization data is troubling because an important conclusion of the paper is that AGS3 acts via LGS. The localization data provided one leg of support for this conclusion and the other is provided by an epistasis analysis. Unfortunately, this data seems to be right on the edge because it is based on the difference between the solid and dashed blue lines in Figure 5B not being significant. However, we can see how close this is by comparing the solid and dashed red lines in the adjacent 5C, which are significantly different. Between the localization data, which doesn't seem clear cut, and the epistasis experiment, which is on the razor's edge, I'm concerned that the conclusion that AGS3 acts through LGN may be going beyond what the data allows.

Reviewer #1 (Public Review):

This work is a follow-up of the work from the same group where the authors showed that Lactiplantibacillus plantarum can enhance juvenile growth by activating the expression of an intestinal protease. They previously showed that this process was mediated by the dlt operon which is involved in the D-Alanylation of teichoic acid.

In the present study, the authors characterized the structure and enzymatic activity of the first protein encoded by this operon and show that the first gene of this operon encodes for an esterase releasing D-Ala from D-Ala lipoteichoic acids (LTA) and renamed it here DltE. The gene encoding this protein was previously uncharacterized and annotated as a peptidoglycan-binding protein putatively involved in peptidoglycan maturation. With the structure and enzymatic characterization of this protein, this study revealed that this protein does not act as peptidoglycan, but instead releases D-Ala from D-alanylated-LTA.

The authors use a Drosophila mutant impaired in response to mDAP-Peptidoglycan fragments (affected in the IMD pathway) to show that this mutant still responds to D-Ala-LTAs. This result is important to show that D-Ala-LTAs act as additional cues sensed by Drosophila independent of m-DAP-peptidoglycan by a still unknown sensory pathway. The study convincingly shows that D-Ala-LTA from the gut microbe L. plantarum leads to increase intestinal peptidase expression (intestinal activity) and enhance juvenile larva growth.

Reviewer #2 (Public Review):

The authors conduct a structure-function analysis of an uncharacterized gene, DltE, which was found by a genetic screen to be involved in the growth promotion of Drosophila larvae by Lactiplantibacillus plantarum, a bacterium that is consistently associated with Drosophila. They find that DltE is a D-Ala carboxylesterase that removes D-Ala from lipoteichoic acids in the cell envelope and that D-alanylated lipoteichoic acids stimulate Drosophila larval growth. The result that D-Ala LTA stimulates larval growth is compelling, although some minor experimental details to do with biological replicates are not shown and the tracking of bacterial abundances should be addressed to make the conclusions more solid. Additionally, I think the use of the terms "direct" and "symbiotic" is inappropriate in the manuscript, but this can be resolved by removing them or performing additional experiments.

The authors make these claims:<br /> - DltE is not a carboxypeptidase modifying Lp peptidoglycan;<br /> - DltE is a D-Ala esterase acting upon D-Ala-LTA;<br /> - only LTAs but not WTAs are D-alanylated in LpNC8 cell envelopes;<br /> - D-Ala-LTAs, in addition to PG, are direct symbiotic cues supporting<br /> (1) intestinal peptidase expression and<br /> (2) juvenile growth in Drosophila.<br /> I find all of the claims to be well supported by data except the suggestion that these are "direct symbiotic" cues. I think the authors provide the support that D-Ala LTAs are nutritional cues, not symbiotic ones.

Overall, I find the work compelling.

Reviewer #3 (Public Review):

This work by Nikolopoulos et al. expands on prior studies demonstrating the ability of a member of the Drosophila melanogaster gut microbiome, Lactiplantibacillus plantarum, to support juvenile development in nutrient-limiting conditions. Previously, the authors identified the pbpX2-dltXABCD operon of L. plantarum that when mutated eliminated the growth-promoting ability of the bacterium to flies experiencing malnutrition (protein starvation). To better understand the bacterial components that support this larval development, the authors used a combination of structural, biochemical, and mutational analysis to describe the physiological role of the DltE, a previously uncharacterized gene within the pbpX2-dltXABCD operon. Although annotated as a serine-type D-Ala-D-Ala-carboxypeptidase, this work supports its role instead as a D-ala esterase that acts upon D-alanylated lipoteichoic acids, which are directly sensed by the host to induce peptidase expression and support juvenile growth in flies.

Overall, the data is compelling, and the conclusions are well-supported. The multiple methods used to examine and support their findings - the combination of structural and biochemical analyses, and the use of both bacterial and fly mutants to substantiate and demonstrate physiological relevance was elegant in execution.

The identification of a role for this bacterial cell component is exciting as it has not previously been appreciated as a bacterial-derived signal in fly immunity and/or metabolism. This work adds to the growing evidence for the breadth and diversity of bacterial metabolites and products that underlie fly-microbiome interactions and may have implications in other animal-microbe interactions, especially L. plantarum-mediated host growth promotion in other models including mammals.

An intriguing aspect of the work is the evidence of a bifurcation of this bacterial signal on immunity and metabolism, with the pathway regulating the latter yet unknown. Likewise, determining how these cell components are sensed by the host will also be of future interest. Another unknown that may limit the implications of this study is the ubiquity of D-ala LTA production among D. melanogaster-associated L. plantarum strains and whether this is a common or rare signal/role.

Reviewer #1 (Public Review):

This manuscript by Walker et. al. explores the interplay between the global regulators HapR (the QS master high cell density (HDC) regulator) and CRP. Using ChIP-Seq, the authors find that at several sites, the HapR and CRP binding sites overlap. A detailed exploration of the murPQ promoter finds that CRP binding promotes HapR binding, which leads to repression of murPQ. The authors have a comprehensive set of experiments that paints a nice story providing a mechanistic explanation for converging global regulation. I did feel there are some weak points though, in particular the lack of integration of previously identified transcription start sites, the lack of replication (at least replication presented in the manuscript) for many figures, some oddities in the growth curve, and not reexamining their HapR/CRP cooperative binding model in vivo using ChIP-Seq.

Reviewer #2 (Public Review):

This manuscript by Walker et al describes an elegant study that synergizes our knowledge of virulence gene regulation of Vibrio cholerae. The work brings a new element of regulation for CRP, notably that CRP and the high density regulator HapR co-occupy the same site on the DNA but modeling predicts they occupy different faces of the DNA. The DNA binding and structural modeling work is nicely conducted and data of co-occupation are convincing. The work could benefit from doing a better job in the manuscript preparation to integrate the findings into our current state of knowledge of HapR and CRP regulated genes and to elevate the impact of the work to address how bacteria are responding to the nutritional environment. Importantly, the focus of the work is heavily based on the impact of use of GlcNAc as a carbon source when bacteria bind to chitin in the environment, but absent the impact during infection when CRP and HapR have known roles. Further, the impact on biological events controlled by HapR integration with the utilization of carbon sources (including biofilm formation) is not explored. The rigor and reproducibility of the work needs to be better conveyed.

Specific comments to address:

1) Abstract. A comment on the impact of this work should be included in the last sentence. Specifically, how the integration of CRP with QS for gene expression under specific environments impacts the lifestyle of Vc is needed. The discussion includes comments regarding the impact of CRP regulation as a sensor of carbon source and nutrition and these could be quickly summarized as part of the abstract.<br /> 2) Line 74. This paper examines the overlap of HapR with CRP, but ignores entirely AphA. HapR is repressed by Qrrs (downstream of LuxO-P) while AphA is activated by Qrrs. WithLuxO activating AphA, it has a significant sized "regulon" of genes turned on at low density. It seems reasonable that there is a possibility of overlap also between CRP and AphA. While doing an AphA CHIP-seq is likely outside the scope of this work, some bioinformatic or simply a visual analysis of the promoters known AphA regulated genes would be interest to comment on with speculation in the discussion and/or supplement.<br /> 3) Line 100. Accordingly with the above statement, the focus here on HapR indicates that the focus is on gene expression via LuxO and HapR, at high density. Thus the sentence should read "we sought to map the binding of LuxO and HapR of V. cholerae genome at high density".<br /> 4) Line 109. The identification of minor LuxO binding site in the intergenic region between VC1142 and VC1143 raises whether there may be a previously unrecognized sRNA here. As another panel in figure S1, can you provide a map of the intergenic region showing the start codons and putative -10 to -35 sites. Is there room here for an sRNA? Is there one known from the many sRNA predictions / identifications previously done? Some additional analysis would be helpful.<br /> 5) Line 117. This sentence states that the CHIP seq analysis in this study includes previously identified HapR regulated genes, but does not reveal that many known HapR regulated genes are absent from Table 1 and thus were missed in this study. Of 24 HapR regulated investigated by Tsou et al, only 1 is found in Table 1 of this study. A few are commented in the discussion and Figure S7. It might be useful to add a Venn Diagram to Figure 1 (and list table in supplement) for results of Tsou et al, Waters et al, Lin et al, and Nielson et al and any others). A major question is whether the trend found here for genes identified by CHIP-seq in this study hold up across the entire HapR regulon. There should also be comments in the discussion on perhaps how different methods (including growth state and carbon sources of media) may have impacted the complexity of the regulon identified by the different authors and different methods.<br /> 6) The transcription data are generally well performed. In all figures, add comments to the figure legends that the experiments are representative gels from n=# (the number of replicate experiments for the gel based assays). Statements to the rigor of the work are currently missing.<br /> 7) Line 357-360. The demonstration of lack of growth on MurNAc is a nice for the impact of the work. However, more detailed comments are needed for M9 plus glucose for the uninformed reader to be reminded that growth in glucose is also impaired due to lack of cAMP in glucose replete conditions and thus minimal CRP is active. But why is this now dependent of hapR? A reminder also that in LB oligopeptides from tryptone are the main carbon source and thus CRP would be active.<br /> 8) A great final experiment to demonstrate the model would have been to show co-localization of the promoter by CRP and HapR from bacteria grown in LB media but not in LB+glucose or in M9+glycerol and M9+MurNAc but not M9+glucose. This would enhance the model by linking more directly to the carbon sources (currently only indirect via growth curves)<br /> 9) Discussion. Comments and model focus heavily on GlcNAc-6P but HapR has a regulator role also during late infection (high density). How does CRP co-operativity impact during the in vivo conditions? Does the Biphasic role of CRP play a role here (PMID: 20862321)?

Reviewer #3 (Public Review):

Bacteria sense and respond to multiple signals and cues to regulate gene expression. To define the complex network of signaling that ultimately controls transcription of many genes in cells requires an understanding of how multiple signaling systems can converge to effect gene expression and ensuing bacterial behaviors. The global transcription factor CRP has been studied for decades as a regulator of genes in response to glucose availability. It's direct and indirect effects on gene expression have been documented in E. coli and other bacteria including pathogens including Vibrio cholerae. Likewise, the master regulator of quorum sensing (QS), HapR), is a well-studied transcription factor that directly controls many genes in Vibrio cholerae and other Vibrios in response to autoinducer molecules that accumulate at high cell density. By contrast, low cell density gene expression is governed by another regulator AphA. It has not yet been described how HapR and CRP may together work to directly control transcription and what genes are under such direct dual control.

Using both in vivo methods with gene fusions to lacZ and in vitro transcription assays, the authors proceed to identify the smaller subset of genes whose transcription is directly repressed (7) and activated (2) by HapR. Prior work from this group identified the direct CRP binding sites in the V. cholerae genome as well as promoters with overlapping binding sites for AphA and CRP, thus it appears a logical extension of these prior studies is to explore here promoters for potential integration of HapR and CRP. Inclusion of this rationale was not included in the introduction of CRP protein to the in vitro experiments.

Seven genes are found to be repressed by HapR in vivo, the promoter regions of only six are repressed in vitro with purified HapR protein alone. The authors propose and then present evidence that the seventh promoter, which controls murPQ, requires CRP to be repressed by HapR both using in vivo and vitro methods. This is a critical insight that drives the rest of the manuscripts focus.

The DNase protection assay conducted supports the emerging model that both CRP and HapR bind at the same region of the murPQ promoter, but interpret is difficult due to the poor quality of the blot. There are areas of apparent protection at positions +1 to +15 that are not discussed, and the areas highlighted are difficult to observe with the blot provided.

The model proposed at the end of the manuscript proposes physiological changes in cells that occur at transitions from the low to high cell density. Experiments in the paper that could strengthen this argument are incomplete. For example, in Fig. 4e it is unclear at what cell density the experiment is conducted. The results with the wild type strain are intermediate relative to the other strains tested. Cell density should affect the result here since HapR is produced at high density but not low density. This experiment would provide important additional insights supporting their model, by measuring activity at both cell densities and also in a luxO mutant locked at the high cell density. Conducting this experiment in conditions lacking and containing glucose would also reveal whether high glucose conditions mimicking the crp results.

Throughout the paper it was challenging to account for the number of genes selected, the rationale for their selection, and how they were prioritized. For example, the authors acknowledged toward the end of the Results section that in their prior work, CRP and HapR binding sites were identified (line 321-22). It is unclear whether the loci indicated in Table 1 all from this prior study. It would be useful to denote in this table the seven genes characterized in Figure 2 and to provide the locus tag for murPQ. Of the 32 loci shown in Table 1, five were selected for further study using EMSA (line 322), but no rationale is given for studying these five and not others in the table.

Since prior work identified a consensus CRP binding motif, the authors identify the DNA sequence to which HapR binds overlaps with a sequence also predicted to bind CRP. Genome analysis identified a total of seven sites where the CRP and HapR binding sites were offset by one nucleotide as see with murPQ. Lines 327-8 describe EMSA results with several of these DNA sequences but provides no data to support this statement. Are these loci in Table 1?

Using structural models, the authors predict that HapR repression requires protein-protein interactions with CRP. Electromobility shift assays (EMSA) with purified promoter DNA, CRP and HapR (Fig 5d) and in vitro transcription using purified RNAP with these factors (Figure 5e) support this hypothesis. However, the model proports that HapR "bound tightly" and that it also had a "lower affinity" when CRP protein was used that had mutations in a putative interaction interface. These claims can be bolstered if the authors calculate the dissociation constant (Kd) value of each protein to the DNA. This provides a quantitative assessment of the binding properties of the proteins. The concentrations of each protein are not indicated in panels of the in vitro analysis, but only the geometric shapes denoting increasing protein levels. Panel 5e appears to indicate that an intermediate level of CRP was used in the presence of HapR, which presumably coincides with levels used in lane 4, but rationale is not provided. How well the levels of protein used in vitro compare to levels observed in vivo is not mentioned.

The authors are commended for seeking to connect the in vitro and vivo results obtained under lab conditions with conditions experienced by V. cholerae in niches it may occupy, such as aquatic systems. The authors briefly review the role of MurPQ in recycling of the cell wall of V. cholerae by degrading MurNAc into GlcNAc, although no references are provided (lines 146-50). Based on this physiology and results reported, the authors propose that murPQ gene expression by these two signal transduction pathways has relevance in the environment, where Vibrios, including V. cholerae, forms biofilms on exoskeleton composed of GlcNAc.

The conclusions of that work are supported by the Results presented but additional details in the text regarding the characteristics of the proteins used (Kd, concentrations) would strengthen the conclusions drawn. This work provides a roadmap for the methods and analysis required to develop the regulatory networks that converge to control gene expression in microbes. The study has the potential to inform beyond the sub-filed of Vibrios, QS and CRP regulation.

Reviewer #1 (Public Review):

Germe and colleagues have investigated the mode of action of bacterial DNA gyrase, a tetrameric GyrA2GyrB2 complex that catalyses ATP-dependent DNA supercoiling. The accepted mechanism is that the enzyme passes a DNA segment through a reversible double-stranded DNA break formed by two catalytic Tyr residues-one from each GyrA subunit. The present study sought to understand an intriguing earlier observation that gyrase with a single catalytic tyrosine that cleaves a single strand of DNA, nonetheless has DNA supercoiling activity, a finding that led to the suggestion that gyrase acts via a nicking closing mechanism. Germe et al used bacterial co-expression to make the wild-type and mutant heterodimeric BA(fused). A complexes with only one catalytic tyrosine. Whether the Tyr mutation was on the A side or BA fusion side, both complexes plus GyrB reconstituted fluoroquinolone-stabilised double-stranded DNA cleavage and DNA supercoiling. This indicates that the preparations of these complexes sustain double strand DNA passage. Of possible explanations, contamination of heterodimeric complexes or GyrB with GyrA dimers was ruled out by the meticulous prior analysis of the proteins on native Page gels, by analytical gel filtration and by mass photometry. Involvement of an alternative nucleophile on the Tyr-mutated protein was ruled unlikely by mutagenesis studies focused on the catalytic ArgTyrThr triad of residues. Instead, results of the present study favour a third explanation wherein double-strand DNA breakage arises as a consequence of subunit (or interface/domain) exchange. The authors showed that although subunits in the GyrA dimer were thought to be tightly associated, addition of GyrB to heterodimers with one catalytic tyrosine stimulates rapid DNA-dependent subunit or interface exchange to generate complexes with two catalytic tyrosines capable of double-stranded DNA breakage. Subunit exchange between complexes is facilitated by DNA bending and wrapping by gyrase, by the ability of both GyrA and GyrB to form higher order aggregates and by dense packing of gyrase complexes on DNA. By addressing a puzzling paradox, this study provides support for the accepted double strand break (strand passage) mechanism of gyrase and opens new insights on subunit exchange that may have biological significance in promoting DNA recombination and genome evolution.

The conclusions of the work are mostly well supported by the experimental data.

Strengths:

The study examines a fundamental biological question, namely the mechanism of DNA gyrase, an essential and ubiquitous enzyme in bacteria, and the target of fluoroquinolone antimicrobial agents.

The experiments have been carefully done and the analysis of their outcomes is comprehensive, thoughtful and considered.

The work uses an array of complementary techniques to characterize preparations of GyrA, GyrB and various gyrase complexes. In this regard, mass photometry seems particularly useful. Analysis reveals that purified GyrA and GyrB can each form multimeric complexes and highlights the complexities involved in investigating the gyrase system.

The various possible explanations for the double-strand DNA breakage by gyrase heterodimers with a single catalytic tyrosine are considered and addressed by appropriate experiments.

The study highlights the potential biological importance of interactions between gyrase complexes through domain-or subunit-exchange

Weaknesses:

The mutagenesis experiments described do not fully eliminate the perhaps unlikely participation of an alternative nucleophile.

Reviewer #2 (Public Review):

DNA gyrase is an essential enzyme in bacteria that regulates DNA topology and has the unique property to introduce negative supercoils into DNA. This enzyme contains 2 subunits GyrA and GyrB, which forms an A2B2 heterotetramer that associates with DNA and hydrolyzes ATP. The molecular structure of the A2B2 assembly is composed of 3 dimeric interfaces, called gates, which allow the cleavage and transport of DNA double stranded molecules through the gates, in order to perform DNA topology simplification.<br /> The article by Germe et al. questions the existence and possible mechanism for subunit exchange in the bacterial DNA gyrase complex.

The complexes are purified as a dimer of GyrA and a fusion of GyrB and GyrA (GyrBA), encoded by different plasmids, to allow the introduction of targeted mutations on one side only of the complex. The conclusion drawn by the authors is that subunit exchange does happen, favored by DNA binding and wrapping. They propose that the accumulation of gyrase in higher-order oligomers can favor rapid subunit exchange between two active gyrase complexes brought into proximity.<br /> The authors are also debating the conclusions of a previous article by Gubaev, Weidlich et al 2016 (https://doi.org/10.1093/nar/gkw740). Gubaev et al. originally used this strategy of complex reconstitution to propose a nicking-closing mechanism for the introduction of negative supercoils by DNA gyrase, an alternative mechanism that precludes DNA strand passage, previously established in the field. Germe et al. incriminate in this earlier study the potential subunit swapping of the recombinant protein with the endogenous enzyme, that would be responsible for the detected negative supercoiling activity.

Accordingly, the authors also conclude that they cannot completely exclude the presence of endogenous subunits in their samples as well.

Strengths

The mix of gyrase subunits is plausible, this mechanism has been suggested by Ideka et al, 2004 and also for the human Top2 isoforms with the formation of Top2a/Top2b hybrids being identified in HeLa cells (doi: 10.1073/pnas.93.16.8288).<br /> Germe et al have used extensive and solid biochemical experiments, together with thorough experimental controls, involving :<br /> - the purification of gyrase subunits including mutants with domain deletion, subunit fusion or point mutations.<br /> - DNA relaxation, cleavage and supercoiling assays<br /> - biophysical characterization in solution (size exclusion chromatography, mass photometry, mass spectrometry)

Together the combination of experimental approaches provides solid evidence for subunit swapping in gyrase in vitro, despite the technical limitations of standard biochemistry applied to such a complex macromolecule.

Weaknesses

The conclusions of this study could be strengthened by in vivo data to identify subunit swapping in the bacteria, as proposed by Ideka et al, 2004. Indeed, if shown in vivo, together with this biochemical evidence, this mechanism could have a substantial impact on our understanding of bacterial physiology and resistance to drugs.

Joint Public Review

The molecular composition of synaptic vesicles (SVs) has been defined in substantial detail, but the function of many SV-resident proteins are still unknown. The present study focused on one such protein, the 'orphan' SV-resident transporter SLC6A17. By utilizing sophisticated and extensive mouse genetics and behavioral experiments, the authors provide convincing support for the notion that certain SLC6A17 variants cause intellectual disability (ID) in humans carrying such genetic variations. This is an important and novel finding. Furthermore, the authors propose, based on LC-MS analyses of isolated SVs, that SLC6A17 is responsible for glutamine (Gln) transport into SVs, leading to the provocative idea that Gln functions as a neurotransmitter and that deficits in Gln transport into SVs by SLC6A17 represents a key pathogenetic mechanism in human ID patients carrying variants of the SLC6A17 gene.

This latter aspect of the present paper is not adequately supported by the experimental evidence so that the main conceptual claims of the study appear insufficiently justified at this juncture. Key weaknesses are as follows:

A. Detection of Gln, along with classical neurotransmitters such as glutamate, GABA, or ACh, in isolated SV fractions does not prove that Gln is transported into SVs by active transport. Gln is quite abundant in extracellular compartments. Its appearance in SV samples can therefore also be explained by trapping in SVs during endocytosis, presence in other - contaminating - organelles, binding to membrane surfaces, and other processes. Direct assays of Gln uptake into SVs, which have the potential to stringently test key postulates of the authors, are lacking.

B. The authors generated multiple potentially very useful genetic tools and models. However, the validation of these models is incomplete. Most importantly, it remains unclear whether the different mutations affect SLC6A17 expression levels, subcellular localization, or the expression and trafficking of other SV and synapse components.

C. Apart from the caveats mentioned above regarding Gln uptake into SVs, the data interpretation provided by the authors lacks stringency with respect to the biophysics of plasma membrane and SV transporters.

Reviewer #1 (Public Review):

Abdellahi et al. used targeted memory reactivation (TMR) and machine learning tools to look for evidence that waking neural activity is reinstated during subsequent REM sleep. Prior work has demonstrated that learning content is successfully decoded following TMR cues during NREM sleep, but a direct link between patterns of brain activity recorded during wakefulness and subsequent REM sleep in humans has never been reported. In this paper, the authors report that an LDA classifier detects wake-like neural activity (specifically, neural activity recorded while imaging performing a trained serial reaction time task) approximately one second after TMR cues are presented during REM sleep. Decoding performance is better when the classifier is trained on sleep trials with high theta compared to low theta power, and classifier performance was correlated with overnight improvement on the task.

Finding evidence of reinstated waking neural activity during REM sleep is an exciting result, and the authors present a promising method that holds implications for advancing our understanding of how memories are reprocessed during REM sleep. I think it is a particular strength of the paper that the authors trained on sleep data and tested in wake data, which is analogous to prior rodent studies that found evidence of replay during REM. I also thought playing sounds during the adaptation night, prior to SRTT training, provided a nice control.

The conclusions of this paper are mostly supported by the results presented, but it is not always clear how those results were obtained. Some aspects of the experimental and data analytic methods need to be clarified and expanded, both for a better understanding of how the results of this study were obtained, as well as for future reproducibility.

Reviewer #2 (Public Review):

I believe the authors succeeded in finding neural evidence of reactivation during REM sleep. This is their main claim, and I applaud them for that. I also applaud their efforts to explore their data beyond this claim, and I think they included appropriate controls in their experimental design. However, I found other aspects of the paper to be unclear or lacking in support. I include major and medium-level comments:

Major comments, grouped by theme with specifics below:<br /> Theta.<br /> Overall assessment: the theta effects are either over-emphasized or unclear. Please either remove the high/low theta effects or provide a better justification for why they are insightful.

Lines ~ 115-121: Please include the statistics for low-theta power trials. Also, without a significant difference between high- and low-theta power trials, it is unclear why this analysis is being featured. Does theta actually matter for classification accuracy?

Lines 123-128: What ARE the important bands for classification? I understand the point about it overlapping in time with the classification window without being discriminative between the conditions, but it still is not clear why theta is being featured given the non-significant differences between high/low theta and the lack of its involvement in classification. REM sleep is high in theta, but other than that, I do not understand the focus given this lack of empirical support for its relevance.

Line 232-233: "8). In our data, trials with higher theta power show greater evidence of memory reactivation." Please do not use this language without a difference between high and low theta trials. You can say there was significance using high theta power and not with low theta power, but without the contrast, you cannot say this.

Physiology / Figure 2.<br /> Overall assessment: It would be helpful to include more physiological data.

It would be nice, either in Figure 2 or in the supplement, to see the raw EEG traces in these conditions. These would be especially instructive because, with NREM TMR, the ERPs seem to take a stereotypical pattern that begins with a clear influence of slow oscillations (e.g., in Cairney et al., 2018), and it would be helpful to show the contrast here in REM. Also, please expand the classification window beyond 1 s for wake and 1.4 s for sleep. It seems the wake axis stops at 1 s and it would be instructive to know how long that lasts beyond 1 s. The sleep signal should also go longer. I suggest plotting it for at least 5 seconds, considering prior investigations (Cairney et al., 2018; Schreiner et al., 2018; Wang et al., 2019) found evidence of reactivation lasting beyond 1.4 s.

Temporal compression/dilation.<br /> Overall assessment: This could be cut from the paper. If the authors disagree, I am curious how they think it adds novel insight.

Line 179 section: In my opinion, this does not show evidence for compression or dilation. If anything, it argues that reactivation unfolds on a similar scale, as the numbers are clustered around 1. I suggest the authors scrap this analysis, as I do not believe it supports any main point of their paper. If they do decide to keep it, they should expand the window of dilation beyond 1.4 in Figure 3B (why cut off the graph at a data point that is still significant?). And they should later emphasize that the main conclusion, if any, is that the scales are similar.

Line 207 section on the temporal structure of reactivation, 1st paragraph: Once again, in my opinion, this whole concept is not worth mentioning here, as there is not really any relevant data in the paper that speaks to this concept.

Behavioral effects.<br /> Overall assessment: Please provide additional analyses and discussion.

Lines 171-178: Nice correlation! Was there any correlation between reactivation evidence and pre-sleep performance? If so, could the authors show those data, and also test whether this relationship holds while covarying our pre-sleep performance? The logic is that intact reactivation may rely on intact pre-sleep performance; conversely, there could be an inverse relationship if sleep reactivation is greater for initially weaker traces, as some have argued (e.g., Schapiro et al., 2018). This analysis will either strengthen their conclusion or change it -- either outcome is good.

Unlike Schönauer et al. (2017), they found a strong correspondence between REM reactivation and memory improvement across sleep; however, there was no benefit of TMR cues overall. These two results in tandem are puzzling. Could the authors discuss this more? What does it mean to have the correlation without the overall effect? Or else, is there anything else that may drive the individual differences they allude to in the Discussion?

Medium-level comments<br /> Lines 63-65: "We used two sequences and replayed only one of them in sleep. For control, we also included an adaptation night in which participants slept in the lab, and the same tones that would later be played during the experimental night were played."

I believe the authors could make a stronger point here: their design allowed them to show that they are not simply decoding SOUNDS but actual memories. The null finding on the adaptation night is definitely helpful in ruling this possibility out.

Lines 129-141: Does reactivation evidence go down (like in their prior study, Belal et al., 2018)? All they report is theta activity rather than classification evidence. Also, I am unclear why the Wilcoxon comparison was performed rather than a simple correlation in theta activity across TMR cues (though again, it makes more sense to me to investigate reactivation evidence across TMR cues instead).

Line 201: It seems unclear whether they should call this "wake-like activity" when the classifier involved training on sleep first and then showing it could decode wake rather than vice versa. I agree with the author's logic that wake signals that are specific to wake will be unhelpful during sleep, but I am not sure "wake-like" fits here. I'm not going to belabor this point, but I do encourage the authors to think deeply about whether this is truly the term that fits.

Reviewer #3 (Public Review):

The authors investigated whether reactivation of wake EEG patterns associated with left- and right-hand motor responses occurs in response to sound cues presented during REM sleep.

The question of whether reactivation occurs during REM is of substantial practical and theoretical importance. While some rodent studies have found reactivation during REM, it has generally been more difficult to observe reactivation during REM than during NREM sleep in humans (with a few notable exceptions, e.g., Schonauer et al., 2017), and the nature and function of memory reactivation in REM sleep is much less well understood than the nature and function of reactivation in NREM sleep. Finding a procedure that yields clear reactivation in REM in response to sound cues would give researchers a new tool to explore these crucial questions.

The main strength of the paper is that the core reactivation finding appears to be sound. This is an important contribution to the literature, for the reasons noted above.

The main weakness of the paper is that the ancillary claims (about the nature of reactivation) may not be supported by the data.

The claim that reactivation was mediated by high theta activity requires a significant difference in reactivation between trials with high theta power and trials with low theta, but this is not what the authors found (rather, they have a "difference of significances", where results were significant for high theta but not low theta). So, at present, the claim that theta activity is relevant is not adequately supported by the data.

The authors claim that sleep replay was sometimes temporally compressed and sometimes dilated compared to wakeful experience, but I am not sure that the data show compression and dilation. Part of the issue is that the methods are not clear. For the compression/dilation analysis, what are the features that are going into the analysis? Are the feature vectors patterns of power coefficients across electrodes (or within single electrodes?) at a single time point? or raw data from multiple electrodes at a single time point? If the feature vectors are patterns of activity at a single time point, then I don't think it's possible to conclude anything about compression/dilation in time (in this case, the observed results could simply reflect autocorrelation in the time-point-specific feature vectors - if you have a pattern that is relatively stationary in time, then compressing or dilating it in the time dimension won't change it much). If the feature vectors are spatiotemporal patterns (i.e., the patterns being fed into the classifier reflect samples from multiple frequencies/electrodes / AND time points) then it might in principle be possible to look at compression, but here I just could not figure out what is going on.

For the analyses relating to classification performance and behavior, the authors presently show that there is a significant correlation for the cued sequence but not for the other sequence. This is a "difference of significances" but not a significant difference. To justify the claim that the correlation is sequence-specific, the authors would have to run an analysis that directly compares the two sequences.

Reviewer #1 (Public Review):

Most previous studies investigating the phenomenon of crowding in depth use small stereoscopic differences in depth. Taken together their results suggest that a depth difference between target and flankers reduces crowding. A potential problem is that stereo displays can reduce depth perception. The studies that have used a real-depth display have provided some inconsistent findings. The present study investigated larger differences, representative of those among many objects in the real world. These larger differences increased crowding, even in the absence of diplopia (double vision).

This study is likely to be impactful in the field as it shows that crowding occurs in-depth and strengthens the importance of crowding in natural 3D environments. All existing models of crowding would need to be modified to explain this experimental finding.

The novel multi-depth plane display that the authors used enables measurements of depth differences that are more likely to correspond to differences in the real world, and could be used by others to further investigate crowding in-depth or other perceptual processes (e.g., visual search).

In general, there are some interactions that were reported and others that were not reported, but it would be important to know if they are significant. (pages 15-16) For example, when the target is at fixation and the target is at a variable flanker depth: In Experiment 1, was there a significant interaction between (a) target-fixation depth and flanker depth (in front versus behind) and (b) target-fixation depth and target-flanker spacing? In Experiment 3, it is reported that perceptual error was higher when the target was in from or behind the flanker ring and fixation and that the greatest perceptual error occurred when the target was behind, but it is not reported if this interaction was significant. Its presence is important to know whether the data should be independently analyzed for 'in front' and 'behind'. In Experiment 5, was the interaction between target-flanker spacing and depth significant?

The findings are clear but the explanation(s) for the findings is not. The authors state that large interocular disparity differences likely induce diplopia, which could increase perceptual error by increasing the number of features. The authors should explain what they mean by features and how an increased perceived number of features would increase crowding. Moreover, the authors acknowledge that only a few observers reported experiencing diplopia; however, they speculate that observers may have experienced diplopia but not noticed it consciously given the short stimulus presentation time.

Reviewer #2 (Public Review):

The authors reexamine the effects of depth on crowding, using a clever display that presents at three depths at once, and find that placing the target or flanker at far depth greatly increases crowding, contrary to what might have been expected by prior work with small depth differences. These stimuli avoid creating conflicting cues to depth and are thus the most relevant to viewing in daily life, indicating more crowding than was expected.

Reviewer #3 (Public Review):

Smithers et al. examine the effects of large differences in target-flanker depth on peripheral visual crowding. To investigate this, they developed a novel real-depth display and measured the perceptual errors caused by the presence of flanker objects that were presented at different distances and at either the same or at different depths from a target object that the participants had to recognize.

Their primary result is that large depth differences between flanking and target objects increase the magnitude of crowding. Interestingly, it appears to be a two-faced finding: when the target is at fixation depth, crowding is more pronounced if the flankers are behind the target as opposed to in front of it. Yet, when the flankers are at fixation depth, crowding is more pronounced if the target is behind the flankers. They explain their finding in terms of increased clutter in areas outside the limits of binocular fusion. This conclusion of the study is well supported by the data and experiments. The work provides compelling evidence that real depth may affect peripheral crowding under the specific circumstances of their experiment. Whether this finding would also apply to more natural viewing conditions, in which there is much more clutter, to begin with, remains to be determined.

Strengths:<br /> By introducing a novel multi-depth plane display authors contribute to future research on the effect of real depth differences on several visual functions and increase the potential ecological validity of their results.<br /> By using perceptual error as their dependent variable and linear mixed models to analyze their data, authors improve their ability to represent the variability in the data.<br /> The authors explain the discrepancies between their results and previous research with sufficient additional experiments and data.<br /> The inclusion of a large number of participants, which is fairly uncommon in this type of experiment.

Weaknesses:<br /> 1. At several points in the paper authors refer to the 'natural three dimensional scenes'. Indeed, the authors increase the ecological validity of their experiment by introducing actual depth differences, therefore allowing for depth cues such as accommodation, vergence and defocus blur. This is indeed a significant improvement over previous studies. However, they still use relatively impoverished visual stimuli in a tightly controlled psychophysical experiment requiring head stabilization by means of a chin rest. So, their experiment is still far removed from deploying actual, ecologically valid, conditions. Consequently, their stimuli mostly lack the complexity and associated clutter of natural stimuli as well as other potential depth cues that an observer might gain from parallax, aerial perspective, lighting, or shading. Therefore, their suggestion "that crowding has a more significant impact on our perception of natural three-dimensional environments than previously estimated with 2D displays." is stretching what can be concluded from their present work.<br /> 2. The inclusion of a large number of participants, in which none of the participants seemed to have performed all the conditions, is both a strength and a potential weakness. Their current approach of including (presumably) naive participants and having each do a portion of the experiments in itself is valid. But it also adds to the complexity of their study and presumably adds variability to their data.

Reviewer #1 (Public Review):

Pelentritou and colleagues investigated the brain's ability to infer temporal regularities in sleep. To do so, they measured the effect on brain and cardiac activity to the omission of an expected sound. Participants were presented with three different categories of sounds: fixed sound-to-sound intervals (isochronous), fixed heartbeat-to-sound intervals (synchronous), and a control condition without any regularity (asynchronous). When omitting a sound, they observed a difference in the isochronous and synchronous conditions compared to the control condition, in both wakefulness and sleep (NREM stage 2). Furthermore, in the synchronous condition, sounds were temporally associated with sleep slow waves suggesting that temporal predictions could influence ongoing brain dynamics in sleep. Finally, at the level of cardiac activity, the synchronous condition was associated with a deceleration of cardiac frequency across vigilance states. Overall, this work suggests that the sleeping brain can learn temporal expectations and responds to their violation.

Major strengths and weaknesses:<br /> The paradigm is elegant and robust. It represents a clever way to investigate an important question: whether the sleeping brain can form and maintain predictions during sleep. Previous studies have so far highlighted the lack of evidence for predictive processes during sleep (e.g. (Makov et al., 2017; Strauss et al., 2015; Wilf et al., 2016)). This work shows that at least a certain type of prediction still takes place during sleep.

However, there are some important aspects of the methodology and interpretations that appear problematic.<br /> (1) The methodology and how it compares to previous articles would need to be clarified. For example, the Methods section indicates that the authors used a right earlobe electrode as a reference. This is quite different from the nose reference used by SanMiguel et al. (2013) or in Dercksen et al. (2022). This could affect the polarity and topographies of the OEP or AEP and thus represents a very significant difference. Likewise, SOs are typically detected in a montage reference to the mastoids. Perhaps the left/right asymmetries present in many plots (e.g. Figure 3) could be due to the right earlobe reference used. Also, the authors did not use the same filters in wakefulness and sleep, which could introduce an important bias when comparing sleep and wake results or sleep results with previous wake papers.<br /> (2) The ERP to sound omission shows significant differences between the isochronous and asynchronous conditions in wakefulness (Figure 3A and Supp. Fig.) but this difference is very different from previous reports in wakefulness. Topographies are also markedly different, which questions whether the same phenomenon is observed. For example, SanMiguel and colleagues observed an N1 in response to omitted but expected sounds. The authors argue that they observe a similar phenomenon in the iso vs baseline contrast, but the timing and topography of their effect are very different from the typical N1. The authors also mention that, within their study, wake and N2 OEPs were "largely similar" but they differ in terms of latencies and topographies (Figure 3A-B). It would be better to have a more objective way to explore differences and similarities across the different analyses of the paper or with the literature.<br /> (3) The authors applied a cluster permutation to identify clusters of significant time points. However, some aspects of this analysis are puzzling. Indeed, the authors restricted the cluster permutation to a temporal window of 0 to 350ms in wake (vs. -100 to 500ms in sleep). This can be misleading since the graphs show a larger temporal window (-100 to 500ms). Consequently, portions of this time window could show no cluster because the analysis revealed an absence of significant clusters but because the cluster permutation was not applied there. Besides, some of the reported clusters are extremely brief (e.g. l. 195, cluster's duration: 62ms), which could question their physiological relevance or raise the possibility that some of these clusters could be false positives (there was no correction for multiple comparisons across the many cluster permutations performed). Finally, there seems to be a duplication of the bar graphs showing the number of significant electrodes in the positive and first negative cluster for Figure 2 Supp. Fig. 1.<br /> (4) More generally, regarding statistics, the absence of exact p-values can render the interpretation of statistical outputs difficult. For example, the authors report a significant modulation of the sound-to-SO latency across conditions (p<0.05) but no significant effect of heartbeat peak-to-SO latency (p>0.05). They interpret this pattern of results rather strongly as evidence that the "readjustment of SOs was specific to auditory regularities and not to cardiac input". Yet, examining the reported chi-square values show very close values between the two analyses (7.9 vs. 7.4). It seems thus difficult to argue for a real dissociation between the two effects. Providing exact p-values for all statistical tests could help avoid this pitfall.

Reviewer #2 (Public Review):

This study was designed to study the cortical response to violations in auditory temporal sequences during wakefulness and sleep. To this end, the study had three levels of temporal sequence, a regular temporal sequence, an auditory tone that was yoked to the cardiac signal, and an irregular tone. The authors show significant EEG differences to an omitted tone when the auditory tone was predictable both during wakefulness and sleep.

The authors analyze the ERP to the omitted tone as well as when aligned to the R-peak of the HEP. The analysis was comprehensive and the effects reported align with the interpretation given. Of particular interest was the fact that a deceleration of the heart rate was present for omissions when the auditory tone was yoked to the R-peak (synch) in all stages of wakefulness and sleep.

However, one weakness was the rationale for the current study and how the results link to current theoretical frameworks for the role of interoception in perception and cognition. This was in contrast to the clear background and explanation to study the response to omissions for a predictable auditory sequence in wakefulness and sleep. It was unclear why the authors selected the cardiac signal to yoke their auditory stimuli. What is the specific motivation for the cardiac signal rather than the respiratory signal? This was not clear.

Reviewer #1 (Public Review):

Kozol et al adapt an important tool, in the form of the atlas, to the Astyanax research community. While broadly the atlas appears to correctly identify large brain regions, it is unclear what is the significance of the finer divisions. The external confirmations are restricted to just a few large brain regions (by independent human observer: e.g., optic tectum, hypothalamus. By molecular marker: hypothalamus only.). As such, interpretations of results from as many as 180 small subregions should be interpreted sceptically.<br /> The authors also suggest that some brain regions have increased in size during cavefish evolution (e.g., hypothalamus, subpallium). The analysis of progeny from a genetic cross of cave and surface morphs suggest a complex genetic program has evolved to control this variant set of brain structures. With the development of genetic manipulation tools in this species, an exciting series of experiments may link causal variants with brain development differences.

MAJOR ISSUES<br /> Line 85+. Segmentation accuracy is not well established by the authors.<br /> For example, Figure S2 states that the pixel correlation is high between Astyanax populations. But the details of how this cross-correlation was done are sparse. Is the Y-axis here showing the fraction of pixels that are shared in the morphs? While the annotation appears to function similarly across morphs, the 80% machine:human correlation is difficult to put into context. On the one hand, this seems low. For what values should one strive? Are there common "mistakes" or differences in human & machine annotations that lead to certain regions being excluded? A discussion of these is warranted and will be useful to others who wish to use this approach.

Line 87. "such as" is misleading since these were the only two antibodies used to confirm molecular definitions of regions.<br /> But more to the point, additional markers should be used to confirm more than just the ISL+ hypothalamic divisions.<br /> This is particularly warranted, as Fig 1d is not convincing. I believe that the yellow label is ISL; this is difficult to see in the figures. ISL is not ideal since this is widespread in the hypothalamus. There are no ISL-negative regions depicted, which would be necessary to demonstrate that the resolution of this subregion labeling tool is high. A complementary approach would be to find molecular markers that are more restricted than ISL which label only subsets of hypothalamic regions.<br /> Finally, do the mid/hindbrain ISL labeled regions correspond to known ISL+ subregions?

The molecular and human-observed confirmations of brain regions suggests that the annotated borders of gross anatomical regions are correctly identified by the algorithm. However, data is not presented that indicates whether the smaller regions correspond to biologically meaningful compartments.

Parameters used in CobraZ to perform the segmentation are not defined. More transparency is required here for others to replicate.

Reviewer #2 (Public Review):

The authors tackled a longstanding question for brain evolution: if the brain regions change based on functional constraints or developmental constraints.

The strength of this study is that the authors introduced an automated method for brain segmentation based on the zebrafish tool, which is a highly advanced technology. They also performed the volume and landmark-based shape analyses in a surface, cave and their F1 and F2 hybrid, highlighting genetic regulations, and revealed 3 genetically correlating clusters of brain regions, which are brand new as far as I know. This study needs intense effort, fine skills to conduct, and intellectual efforts to summarize the vast dataset. I simply admire how the authors achieve their study at this level.

The weakness of this study is that the method/approach used in this study is difficult to test the functional constraint hypothesis although the authors nicely tested the developmental constraint hypothesis, which was highlighted in their correlation studies (volumetric and shape: Fig 4 and 5). I am also a little concerned with the accuracy of the automated segmentation algorithm shown in Figure 1-figure supplement 2. The original zebrafish paper (CobraZ) showed a similar accuracy (cross-correlation as 80%). If this level of accuracy is accepted in the field, I am OK with it.<br /> Their data support the conclusion 'brain-wide evolution occurs in distinct developmental modules' because of their correlation study. However, I am not so positive at the point that one of two central hypotheses were directly tested in this study: the functional constraint hypothesis - to test it, for example, the authors need to address the functional connectivities (calcium imaging, etc) and then test if the correlation between calcium-transients and the size/shape of each pair of brain regions.

Reviewer #3 (Public Review):

In this manuscript the authors use novel techniques and analytical methods on an up and coming animal model for brain evolution. The manuscript utilizes the cavefish Astyanax mexicanus, which can provide future important insights into the field of neurobiology and in evolution in general.<br /> The authors however, only argue that Astyanax is a powerful system for functionally determining basic principles of brain evolution (which clearly it will be), but fail to actually describe what brain evolution insights Astyanax gives. The data is in the paper, but the interpretation needs refinement. This would be a much more valuable paper with a thorough evolutionary context based on the already existing, extensive literature. I believe this manuscript has the potential to be extremely impactful.

Reviewer #1 (Public Review):

The authors of this manuscript aimed to systematically evaluate the pleiotropic effects of MCR-1-mediated colistin resistance. They evaluated the effect of MCR-1 and MCR-3 carried on different plasmids on antimicrobial peptides (AMPs) and assessed their ultimate effect on virulence. The authors find that MCR-1-mediated colistin resistance correlates with increased resistance against some host AMPs, but also increased sensitivity to others. The authors also find that MCR-1 alone is associated with resistance to human serum and to elements of the complement system. This highlights a potential selective advantage for MCR-1-mediated resistance to host immune factors and a potential for enhanced virulence.

The methods have been well established before and adequately support their main findings. While determining the role of MCR-1 in a single genetic background is important to better understand its potential pleiotropic effects against a diversity of AMPs and in a variety of scenarios, the impact and significance of the results are partially ameliorated because different genetic backgrounds, particularly those most relevant to a clinical (or agricultural) context were not considered. The results depicted here are still a necessary and important step towards a more comprehensive understanding of the pleiotropic effects of MCR-1. But, interactions between plasmids and host genomes and their co-evolution can have important effects more generally. The authors do mention this in the discussion and suggest it to be an important avenue for future work. However, given the objective of the study and the clinical and agricultural context in which the authors have framed their work, it seems more relevant to include those distinct genetic backgrounds already here.

The conclusions stemming from the results found in Figure 3, and Figures 4c and d seem too overreaching to me. The associated resistance to AMPs from pigs seems to be only strong enough against one of the five tested AMPs and hence concluding that these impose a strong selective pressure in the pig's gut seems unsubstantiated. Similarly, the difference in survival probability within their in vivo system, though statistically significant, seems to be very ild between their MCR-1 and empty vector control.

Reviewer #2 (Public Review):

Jangir et al test the hypothesis that resistance to the antimicrobial peptide (AMP) colistin can simultaneously increase resistance to other AMPS with related modes of action. Because AMPS comprise part of innate immunity, their central concern is that colistin resistance may compromise host defenses and thereby increase bacterial virulence. Their results show that MCR-1, whether expressed from naturally circulating or synthetic plasmids, can increase the MIC to AMPS from humans, pigs, and chickens, and impart fitness benefits at sub-MIC concentrations. In addition, they find that MCR-1-containing strains have increased survival in human plasma and are more lethal in an insect infection model.

The conclusions of the paper are generally well supported by the results, but some aspects could be clearer and better defended with a few small additional experiments.

Strengths:<br /> Using both synthetic and natural plasmids makes it possible to cleanly separate the effects of MCR-1 from the effects of other plasmid-borne genes or plasmid copy numbers. This helps confirm the causal role of MCR-1 on altered AMP susceptibility.

Testing the survival of transformed isolates in human serum and in insects points to relevance in the more immunologically complex host environment where cells are exposed to a suite of factors that reduce bacterial survival.

Weaknesses/suggestions:<br /> Although increases in MIC are evident for different AMPS, the effects are generally modest. To address this, it might be helpful to use pairwise competition assays, as in Figure 1, to establish that even small changes to MIC are associated with clear selective benefits. This would be especially helpful in assays with human serum and in Galleria where the concentrations of AMPS or other immune components are unknown.

Assays using human serum are interesting but challenging to interpret given the diverse causes of bacterial killing, including complement. Although this was partly addressed in Supplementary Figure 6, I found the predictions of these experiments unclear. First, I think these experiments are too central to be relegated to the supplemental materials; they belong in the main text. Secondly, it is important to explicitly spell out the expectations of using heat-killed serum (which will degrade any heat-labile components) or complement-deficient serum. It should be clearer under which conditions MCR-1-containing strains are predicted to do better or worse than controls.

Galleria is a useful infection model for virulence, but it is unclear what drives differences between strains. First, bacterial numbers aren't measured in this assay, so it isn't known if increased virulence is due to increased bacterial growth or decreased bacterial clearance. As above, I think these assays would be stronger using the competition-based approach in Figure 1. This would indicate bacterial numbers through time and directly show the selective benefit associated with MCR-1. Second, it would be useful to elaborate on why MCR-1 increases virulence, especially any known similarities between Galleria AMPS and those tested in Figures 1 and 2. Overall, it would help if Galleria were less of a black box.

Reviewer #1 (Public Review):

The adhesion of Leishmania promastigotes to the stomodeal valve in the anterior region of the sandfly vector midgut is thought to be important to facilitate the transmission of the parasites by bite. The promastigote form found in attachment is termed a 'haptomonad', although its adhesion mechanism and role in facilitating transmission have not been well studied. Using 3D EM techniques, the paper provides detailed new information pertaining to the adhesion mechanism. Electron tomography was especially useful to reveal the ultrastructure of the attachment plaque and the extensive remodelling of the flagellum that occurs. A few of the attached haptomonads were found to be in division, which is a novel observation. The attachment of cultured promastigotes to plastic and glass surfaces in vitro was found to involve a similar remodeling of the flagellum and was exploited to image the sequential steps in attachment, flagellar remodeling, and haptomonad differentiation. The in vitro attachment was found to be calcium2+ dependent. Based mainly on the in vitro observations, a sound model of the haptomonad attachment plaque and differentiation process is provided.

Reviewer #2 (Public Review):

The study by Yanase et al. investigated the details of the 3D architecture of Leishmania haptomonad promastigote's adhesion to the midgut of the insect vector. The authors generated a dataset of images that reveal intricate details of the formed adhesion plaque and expanded the study with in vitro alternatives for the exploration of how Leishmania promastigotes strong adhesion by hemidesmosomes to surfaces can happen and be maintained. They show with unprecedented detail the ultrastructure of the attachment plaque. The in vitro dataset of the paper adds to the specific literature important details on how to explore micro/nanostructures involved in an important attachment step for this eukaryotic parasite. However, the in vitro data should be reconsidered in its discussion and conclusions as it does not support direct comparison with in vivo Leishmania forms as pictured by the authors. In general, the dataset presented in this manuscript adds valuable data and resources for the study of Leishmania promastigotes to surfaces, especially to the thoracic midgut parts of its insect vector.

The dataset of this paper is well-collected and robust, but some aspects of image analysis need to be clarified and extended. Also, the in vitro data from the manuscript will benefit from an extensive adjustment in its discussion. Points to focus on:

1) The haptomonad promastigote is indeed a possible critical form for transmission, but it lacks formal demonstration still in all literature available. This should not be claimed without proper formal demonstration.

2) Literature available and cited in this manuscript regarding in vitro adhesion of culture Leishmania promastigotes does not provide direct evidence for haptomonad differentiation. Haptomonads are still a largely unknown promastigote form with no defined ontogeny. With that, to propose an in vitro haptomonad differentiation protocol, more detailed direct evidence of in vivo haptomonads will be necessary. The in vitro experiments available show how cultured promastigotes attach to surfaces. Detailed studies in vivo will be needed still to attribute the findings in vitro to haptomonads.

3) This manuscript will benefit by having a detailed description of how to analyze and get to the 3D models presented. This has a strong potential for usage beyond the Leishmania/sand fly field. Statistics should be made available with ease across the manuscript and with a dedicated section on methods.

Reviewer #1 (Public Review):

In this manuscript, Sampaio et al. tackle the role of fluid flow during left-right axis symmetry breaking. The left-right axis is broken in the left-right organiser (LRO) where cilia motility generates a directional flow that permit to dictate the left from the right embryonic side. By manipulating the fluid moved by cilia in zebrafish, the authors conclude that key symmetry breaking event occurs within 1 hour through a mechanosensory process.

Overall, while the study undeniably represents a huge amount of work, the conclusions are not sufficiently backed up by the experiments. Furthermore, the results provided present a limited advance to the field: the transient activity of the LRO is well established, and narrowing down this activity to 1 hour (even though unclear from the presented data that it is a valid conclusion) does not help to understand better the mechanism of symmetry breaking. Importantly, the authors do not provide any convincing experiments to back up the mechanosensory hypothesis because the fluid extraction experiments affect both the chemical and physical features of the LRO, so it is impossible to disentangle the two with this approach.

Reviewer #2 (Public Review):

The manuscript by Sampaio and colleagues utilizes an elegant and delicate approach to manipulate fluid dynamics in zebrafish Kupffer's vesicle (KV) to answer a long-standing question in the field - is it fluid movement or something in the fluid that governs the break in symmetry?

The researchers extract fluid from KV at different times during somitogenesis and find this procedure results in left-right organ defects when fluid is removed from the 3 to 5 somite stage, peaking at 5 somites. The effect on left-right patterning by this manipulation is not significant from the 6 somite stage onward. This technique is non-trivial and the researchers have used it with great effect.

Fluid extraction in this sensitive time window (3-5 somites) did not affect cilia number, length, or distribution within KV suggesting the effect on left-right patterning is due to disruption of the fluid. There is a clear effect of the manipulation on dand5 RNA asymmetry as expected. Manipulated embryos that developed left-right defects also showed a decrease in angular velocity of particle movement in the anterior LRO. Increasing the viscosity of the fluid in KV with methylcellulose also results in left-right patterning defects. Taken together, these results are in strong support of fluid movement and detection being important in breaking symmetry in a ciliated left-right organizer. They also argue against the idea that there are signals in the fluid that are being moved asymmetrically to signal to the "left" to break the symmetry. Importantly, they help set a time window when fluid flow is critical for this process.

Reviewer #1 (Public Review):

In this manuscript, Lee and colleagues address the participation of NBR1 in chloroplast clearance after treatment with high light intensity. Authors use NBR1 fused to reporter proteins (GFP, mCherry), with the aid of nbr1, atg7, and nbr1-atg7 mutants, in combination with immunogold labelling to show localization of NBR1 to surface and interior of photodamaged chloroplasts, which follows with their engulfment in the vacuole, a process which is independent of ATG7. The combined use of ATG8 fused to GFP further shows that NBR1 and ATG8 are recruited independently to photodamaged chloroplasts. In addition, the use of mutant versions of NBR1 in combination with mutants lacking E3 ligases PUB4 and SP1 and mutant toc132-2 and tic40-4 lacking members of the TIC-TOC complex of protein translocation to the chloroplast, authors show that chloroplast localization of NBR1 requires the ubiquitin ligase domain (UBA2) of the protein, whereas, the PB1 domain exerts a negative effect on NBR1 chloroplast association, yet neither the PUB4 and SP1 E3 ligases nor the TOC-TIC are required for NBR1 association to photodamaged chloroplasts. All these approaches are well described and strongly support the authors' conclusions that the loss of chloroplast envelope integrity allows the entrance of cytosolic ubiquitin ligases and the participation of NBR1 in photodamaged chloroplast clearance by a process of microautophagy. All these findings add valuable information to our knowledge of chloroplast homeostasis in response to light stress.

To further support these conclusions, authors perform a chloroplast proteomic analysis of the WT, nbr1, atg7, and nbr1-atg7 mutants. However, in contrast with the above results, the description of the proteomic data is rather confusing. The paragraph on Page 17 (lines 393-406) is hard to follow. The term "over-representation of less abundant chloroplast protein" is also quite confusing, like the data in Fig. 6 and supplementary to this figure (what does show the PCA analysis in Fig. 6-suppl. 1?). I wonder whether it would be possible to show all these data as supplementary and try to present the data supporting the major conclusion of these analyses (if I understood correctly, that nbr1, atg7, and the double mutant have lower contents of chloroplast proteins), in a more simple and clear format.

Reviewer #2 (Public Review):

The authors conducted a wide-ranging series of experiments which lead to the conclusion that NBR1 is involved in the clearance of photodamaged chloroplasts. It is a novel finding because the role of NBR1 in this process was never documented. Notably, the NBR1-mediated clearance is only one of the several possible mechanisms responsible for chloroplast turnover. It is not surprising, considering that the nbr1 mutants are viable. The work is arranged very well. The rationale of the subsequent experiments is logically justified and the outcomes and followed by clear conclusions. In consequence, the authors managed not only to observe the association of NBR1 with the chloroplasts but they threw some light on the corresponding mechanisms. The manuscript contains numerous high-quality images from a confocal microscope and from a transmission electron microscope. All images are accompanied by statistical analysis of the respective microscopic observations, which greatly improves the credibility of the conclusions. Shortly, the authors demonstrated that NBR1 decorates not only the exterior but also the interior of damaged chloroplasts in an ATG7-independent way. Next, they establish that NBR1 and ATG8 are recruited to different populations of damaged chloroplasts, and they document differences in chloroplasts turnover, differences in chlorophyll abundance and chlorophyll photochemical properties, as well as differences in the total proteome of the nbr1 mutant in comparison to the wild type and atg7 mutant in two light regimes (low light and high light). Finally, they exclude the requirement for the known E3 ligases PUB4 and SP1 for NBR1-mediated degradation and show that the NBR1 internalization relies rather on the chloroplastic membrane rupture than on the TIC-TOC-dependent processes. In summary, the authors postulate that NBR1-mediated chloroplast clearance is a novel, not yet described mechanism and summarize it in a clear diagram.

The work is interesting, the figures are convincing and the conclusions are justified by the results. It provides novel data on the function of selective autophagy receptors NBR1 in plant cells, however, it also leaves the reader with some unanswered questions. The most important is the relative contribution of each of the chloroplast's degradation routes to the turnover of these organelles in different stresses, light regimes, plant growth stages, etc. This is a difficult problem because the mutations in relevant genes have pleiotropic effects and it is difficult to separate the functions of the individual turnover routes. For example, the defects in core autophagy genes (like the atg7 mutant used in this study) result in an increased level of NBR1. These issues are not sufficiently addressed in the discussion.

Reviewer #3 (Public Review):

The authors use an impressive array of techniques to determine the role of the NBR1 autophagy receptor protein specifically in the clearing of photodamaged chloroplasts. The authors describe the mechanism(s) by which this receptor operates in this context and demonstrate that this NBR1-mediated process occurs independently of SP1 and PUB4 (whose own roles in other aspects of chloroplast autophagy have previously been shown). The authors further dissect the functional domains of NBR1 to identify which are important in this process.

The major strength of this work is the myriad techniques used to approach the problem. The data are of high quality, and on the whole, well replicated and statistically analysed. In the main, these data substantiate the findings of the authors, although some findings are quite correlative/descriptive. However, the authors show good circumspection in their conclusions and discussion. One potential weakness is that the genetic data (use of mutants) rely on single mutant alleles, therefore whilst genetic linkage to the mutations is assumed, it cannot strictly be guaranteed. The authors performed effective genetic complementation to analyse the domain structure of NBR1 shown in Figure 7. It would have been good if complementation of nbr1 and atg1 mutants and/or alternative mutant alleles had been used for experiments described in Figures 1 to 6. Without this, I think even more circumspection regarding the data obtained from these single-allele mutants would be advised.

Reviewer #1 (Public Review):

The manuscript entitled "Pooled genome-wide CRISPRa screening for rapamycin resistance gene in Drosophila cells" by Xia et al. is a well-structured piece of work with clear objectives and experiments. The authors successfully demonstrated genome-wide gene activation using CRISPRa using a novel sgRNA design, which overcame previous failed attempts to replicate gene activation that worked well in mammalian systems. The study is detailed and highly relevant for the application of CRISPRa in understanding the molecular mechanism of gene candidates.

Reviewer #2 (Public Review):

In this work Xia et al have generated CRISPR resources for genome-wide gain-of-function genetic perturbation in the Drosophila genome and have used them to identify novel genes that cause Rapamycin resistance in Drosophila cells. To do so, they have used the SAM system, already established to work well in flies (Jia et al., PNAS 2018). 3 of these candidate genes they discovered in the screen, were further characterized to study how they affect the mTOR pathway leading to Rapamycin resistance. Since genome-wide libraries for GOF studies do not exist for Drosophila, these resources will be very useful for a wider Drosophila community.

Strengths

1. GOF CRISPR library does not exist currently to be used in Drosophila and hence this is going to be useful for the wider Drosophila community<br /> 2. Authors have used already established and currently the most effective SAM system for gene activation for a genome-wide genetic screen.<br /> 3. From this screen they have found candidate genes overexpression which leads to Rapamycin resistance. They have validated 3 of these genes by multiple methods and have also tried to elucidate the mechanism by which these genes might regulate mTOR signaling and confer resistance to Rapamycin. The authors have shown the strength and usefulness of the resource that they have generated and this resource will be complementary to loss-of-function screens of similar nature.

Weaknesses

1. Authors have taken a number of measures to maintain the integrity of the CRISPRa library, including multiple gRNA targets per gene, 1000 cells per gRNA, and deep sequencing. However, do the authors have an idea of what percentage of the gRNA vectors are functional? Looking at the data they show for the 3 candidate genes, at least half of them are not functional, which could be either because of gRNA location or efficiency. Considering this to be an average situation, there might be a large number of genes for which all gRNAs might not function at all. I understand this might be a caveat for all such studies, but an estimate of some kind in discussion might be useful for anyone who might want to use these resources.<br /> 2. As the authors mention that ~32% of genes in Drosophila have transcription start side <1kb apart, off-targeting (neighbouring genes getting activated in addition to the intended gene) will be an issue. To address this, the authors describe one example of genes where although the genes TSS are within one kb of each other, the sgRNA specifically activated only one gene and not the other. However, since following this, authors have generated genome-wide resources keeping 500bp upstream as their benchmark, a large percentage of these 32% genes might have off-targets. It would be useful to know the estimates of off-targeting for such a resource. In addition, have authors looked at the transcripts of genes close to the specific genes they have studied? CG9932 is in close proximity to (although not within the 1 kb range) a few genes including mTOR.

Reviewer #1 (Public Review):

Previously the authors showed that ERK3 plays a critical role in the production of IL-8, immune cell chemotaxis, and metastasis (Bogucka et al, eLife 2020). This is a follow-up study on these observations in which they uncover a critical role for ERK3 in the activation of RhoGTPases, formation of actin-rich protrusions, and actin polymerization. Previous publications have reported a critical role of ERK3 in regulating cell morphology and migration. However, the molecular mechanisms responsible for these phenotypes remain elusive. The polarized phenotype of motile cells involves complex actin cytoskeleton re-arrangements, and in this study, the authors demonstrate a direct role for MAPK6 kinase in regulating actin dynamics.

First, the authors confirm that loss of ERK3 negatively affects MDA-MB231 cell motility and migration, both in vitro and in vivo. Interestingly loss of ERK3 reduced F-actin content in primary breast mammary epithelial cells. The authors used a multi-disciplinary approach to elucidate the underlying mechanisms. Using biochemical methods, they elegantly show the direct link between ERK3 and RhoGTPases as well as the ARP2/3 complex. Furthermore, direct binding of ERK3 to Rac1, Cdc42, and Arp2/3 complex is shown by biochemical assays, and these observations are validated by monitoring the interaction between ERK3 and the Cdc42/ARP2/3 complex in cells at endogenous levels. The finding that ERK3 acts as a GEF for Cdc42 and not Rac1 is interesting and further links this kinase to PAKs. PAK kinases have been shown to phosphorylate ERK3 at Ser 189 in the SEG motif to activate ERK3 (Deleris et al JBC,2011). Overall, this study generated a lot of interesting data and the work has been well-executed and properly interpreted. The main findings are novel and important, and they are of particular interest to readers in the fields of cell migration and actin dynamics. This manuscript is also likely to stimulate additional investigations using biophysical and structural methods to further decipher GEF activity controls ERK3.

Reviewer #2 (Public Review):<br /> <br /> MAPKs are key fundamental enzymes and out of the 14 MAPKs, ERK3 and ERK4 remain less studied. The authors have made some interesting discoveries on ERK3, especially in the context of chemotaxis and tumourigenesis previously (Bogucka et al eLife 2020). Here they investigated the role of ERK3 in the control of cell architecture. Loss of ERK3 led to a reduction in the formation of actin-rich protrusions which led the authors logically to look for the activation of RhoGTPases. Intriguingly, they found that ERK3 functioned as a GEF for Cdc42 but not for Rac1. Further, they identified that Rac-WAVE and Arp2/3 were present at endogenous levels in a heteromeric complex in cells. As ERK3-deficient breast epithelial cells exhibit less F-actin content, this has led the authors to check for Arp2/3-dependent events here. By employing a variety of knockdown and complementation approaches, the authors convincingly demonstrate that the kinase activity of ERK3 is not required for the total F-actin content but for the formation of actin-rich protrusions. Finally, loss of ERK3 reduced random cell motility in vitro and in vivo, which was accomplished by intravital imaging of breast cancer cells in mice. Many protein kinases have catalysis-dependent and -independent functions (catalytic activity versus allosteric activity) and here is another example that deserves further investigation and opens new lines of investigation.

Reviewer #3 (Public Review):

Bogucka-Janczi et al. have carefully dissected a role for ERK3 in the regulation of actin cytoskeleton dynamics. They identify two "nodes" of operation for ERK3 in this process, firstly, the interaction and effect of ERK3 on the small GTPases Rac1 and Cdc42, and secondly, the interaction with and effect of ERK3 on ARP3. In addition, they show a robust phosphorylation of ERK3-S189 in response to EGF stimulation. They further show that ERK3 knockdown results in a decrease of chemotaxis in response to EGF, although they have been unable to identify an important role of S189 phosphorylation in this context.

The authors have clearly carried out a large number of experiments in order to understand these complex events in a highly dynamic process. They have largely succeeded, although some aspects are rather unclear.

Peer review report

Title: Types of Arrhythmias and the risk of sudden cardiac death in dialysis patients: A Systematic Review and Meta-analysis

version: 1

Referee: Milaras Nikias

Institution: National and Kapodistrian University of Athens- Ippokrateion Hospital

email: nikiasmil@med.uoa.gr

ORCID iD: 0000-0001-7312-0976

General assessment

It is now well known that high cardiovascular mortality in ESRD patients is only partly due to atherothrombotic events. Ventricular tachyarrhythmias and electromechanical dissociation account for a significant amount of those deaths as was reported in landmark trials such as the MADIT II. VT or VF might be the mode of death in only a minority of those patients and this is extrapolated from the fact that ICD implantation in this population does not extend survival, whether due to high competing comorbidities or due to electromechanical dissociation being the cause of death. It is true that ESRD patients are underrepresented in such studies due to the high competing factor for non-cardiac death and no safe conclusion can yet be drawn. It remains yet to be seen whether a better risk stratification algorithm through Holter monitoring or programmed ventricular stimulation can unveil those truly at high risk for SCD.

This meta-analysis tries to unveil the mode of death and the high cardiovascular mortality in renal failure through a thorough literature search that included 11 studies. This systematic review/meta-analysis follows current writing and reporting guidelines.

The English used is adequate although some parts of the manuscript could be refined (eg 3rd paragraph in Introduction)

Essential revisions that are required to verify the manuscript

ESRD and ESKD are both discussed in the manuscript. I would personally prefer that the authors devoted more effort in commenting on the meta-analysis results and its implications. The included studies are not adequately annotated in the text, making reading difficult for the statistically unschooled reader who must understand the plots provided.

Decision

Verified with reservations: The content is academically sound but has shortcomings that must be improved.

Reviewer #1 (Public Review):

This paper by Zhuang and colleagues seeks to answer an important clinical question by trying to come up with novel predictive biomarkers to predict high-risk T1 colorectal cancers that are at risk for nodal involvement. The current clinical features may both miss patients who underwent local therapy and who should have gone on to have surgery and patients for whom surgery was done based on risk features but perhaps unnecessarily. Using a training and validation set, they developed a protein-based classifier with an AUC of 0.825 based on mass spec analyses and proteomic analyses of patients with and without LN importantly linking biological rationale to the proteomic discoveries.

In the training cohort, they took 105 candidate proteins reduced to 55, and did a validation in the training cohort first and then in two validation cohorts (one of which was prospective). They also looked at a 9 protein classifier which also performed well and furthermore looked at IHC for clinical ease.

Reviewer #2 (Public Review):

De Filippo et al. investigated the spatiotemporal dynamics of the ripples propagation in the hippocampus of head-fixed mice. By leveraging the LFP and the isolated units of an open dataset of 49 animals with ~6 Neuropixels probes in the longitudinal axis of the hippocampus, they found: first, that stronger ripples (>ninth decile of power) originated in the most septal pole of the hippocampus (medially, anatomically) tend to travel more (M to L) than more lateral ripples (closer to the temporal pole). Second, while strong ripples were mainly local, the authors found that they are most likely to be generated in the temporal pole of the hippocampus, from where they can travel with relatively small attenuation. Finally, they found that strong/septal ripples elicit high spiking activity along the entire mediolateral axis of the hippocampus. Longer/stronger ripples have been proposed to be important in situations with high memory load, and these analyses increase our understanding of their physiology and mechanisms of generation.

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

1) High amplitude ripples preferentially occur in distal CA1, and ripples can propagate at a higher degree on the proximo-distal than in the septo-temporal axis of the hippocampus (Kumar and Deshmuckh, 2020). Therefore, a proximo-distal bias in the Neuropixel positioning could explain part of the variance the authors report. Authors should consider (or control for) the proximodistal positioning of the electrodes.

2) In my opinion, the dynamics of the ripple-induced spiking activity for the events generated in the medial or lateral section of the hippocampus are very striking, more even considering that only a minority of the detected ripples are strong/long events (less than 5% in a familiar environment, Fernandez-Ruiz et al, 2019), while, according to the authors, majority of the ripples (grouped as 'common' by the authors) travel on the opposite direction (from the lateral section towards the septal pole, figure 2). Moreover, in the 50-120ms window, the most lateral positions (>3500um) seem to be more influenced by the medial ripples than relatively more central electrodes (~3000um). How can the authors explain this? To understand a little bit more how ripple features relate to the spiking dynamics, authors could try to generate heatmaps of the differential spiking between medial and lateral ripples (as they did in Fig. 4D-E) for 'strong' and 'common' ripples, or for local and propagating ripples.

Reviewer #3 (Public Review):

Using a large Neuropixels dataset provided by the Allen Institute (https://allensdk.readthedocs.io/en/latest/visual_coding_neuropixels.html), Filippo & Schmitz examined propagation profiles of the hippocampal ripples along the longitudinal axis. In addition to the previously described correlation between the ripple strength and distance (Patel et al., 2013; Kumar et al., 2019), the authors revealed heterogeneous propagation patterns depending on the strength and the origin. Within the septal half of the hippocampus, 'strong' ripples (top 10% strength in a session) is more likely to propagate from the medial to the lateral while the other ripples move in the other direction. Interestingly, these strong ripples are unique in that they are generated locally and more in the medial part of the septal hippocampus. Finally, the authors found that more neurons, with higher firing rates, are engaged in the strong ripples generated in the medial part of the septal hippocampus.

The major strength of the present study is their finding of the unique propagation of the strong ripples across the longitudinal axis. Past studies examining ripple propagations did not have a particular focus on the strength of ripples and thus have not described this feature. On the other hand, however, I believe the manuscript would represent a higher significance if the authors provided more thoughts on physiological impacts and or particular roles of this unique propagation pattern. The authors propose 1) the integration of the different kinds of information and 2) the contribution of the septal hippocampus to higher memory demand (Lines 275-296). Although these views are interesting, the former only explains the longer propagation of the ripples but not the direction (i.e., the ripples could propagate from the lateral to the medial), and the latter idea is less convincing because the Neuropixels data is collected from the mice only passively receiving visual stimuli.

The propagation of the locally generated ripples across the septotemporal axis has been well described in past studies (Patel et al., 2013; Kumar & Deshmukh, 2019). The authors' findings about different directionalities of ripple propagation depending on the origin would provide a valuable view for the expert in the field of the hippocampal physiology.

Reviewer #1 (Public Review):

This paper presents a systematic and novel examination of how pupil size relates to BOLD fMRI signal in a set of subcortical nuclei. It provides some important novel findings that should help advance understanding of how pupil size relates to activity in subcortical nuclei as well as providing important advances in how to measure these relationships.

The authors first tried replicating prior findings of a relationship between pupil size and BOLD signal using the prior methods. They could not (despite replicating pupil-cortical region relationships), and so tested whether the delay in the hemodynamic response function might differ in subcortical and cortical regions. They found that BOLD signal in the subcortical nuclei showed associations with pupil size at short delays. This is a critical finding as typical fMRI analyses assume a longer delay and so likely obscure the ability to see effects in these subcortical regions. The authors provide a number of helpful 'control' analyses that help strengthen confidence in their findings. For instance, it buttresses their findings that the pons control region did not show any significant effect to time-to-peak on correlations with pupil size or derivative measures. It also is helpful to know that pupil size fluctuations were associated with cortical activity in the regions expected from prior studies. The rigor of the study is also supported by the fact that there was a preregistration and that data are publicly shared.

Reviewer #2 (Public Review):

Lloyd et al examine the relationship between pupil size and fMRI signals in six brain nuclei responsible for providing the four major neuromodulators in the brain: norepinephrine from the locus coeruleus (LC), dopamine from ventral tegmental area (VTA) and substantia nigra, serotonin from the dorsal and median raphe nuclei, and acetylcholine from the cholinergic basal forebrain. Importantly, the authors focus on the relationship between these nuclei in the ascending arousal system (AAS) and the pupil at rest, outside of the context of any task, to determine the extent that small changes in pupil size are predictive of AAS activity.

Very few previous studies have examined this relationship at rest, perhaps in part because of the increased sensitivity required in the absence of event-based averaging. These nuclei are small (especially the LC), and thus are difficult to measure with standard fMRI.

The authors use a number of data collection and processing techniques to increase the sensitivity and precision of their recordings targeted to small ROIs. They find robust correlations between multiple AAS nuclei and pupil size with a time course that is not well captured by a standard hemodynamic response function (HRF).

The latter methodological finding is likely to be useful to the field for future studies focused on extracting useful signals from these nuclei, and the observed relationship between multiple AAS nuclei and the pupil support an emerging consensus from animal research that pupil fluctuations are correlated with neuromodulators besides norepinephrine.

Reviewer #3 (Public Review):

The authors took a comprehensive set of analyses to examine the relationship between pupil diameter / derivative and BOLD-signal during rest in the ascending arousal system nuclei in 72 young participants. Focus is on the locus coeruleus, ventral tegmental area, substantia nigra, dorsal and median raphe nuclei and the basal forebrain. Analyses were performed using various processing pipelines: canonical versus custom hemodynamic response functions, with/without smoothing, time to peak analyses and cross spectral power density analyses to define the time lag between both measurements. The authors could not replicate previous correlations between locus coeruleus BOLD and pupil measurements using standard analytic approaches, and also found no relationship between locus coeruleus BOLD and pupil measurements when using custom hemodynamic response functions. When using time to peak and cross-correlation analyses, the authors found that coupling between pupil size and AAS BOLD patterns increases with decreasing time to peak, when the two signals were close in time. The authors conclude that these findings suggest that pupil size could be used as a noninvasive readout of AAS activity under passive conditions.

These authors did a thorough assessment, and described the methods and results well and in a balanced manner.<br /> Outstanding questions:<br /> - the reliability of these observations? would we see the same findings in a different cohort or using a different sequence/field strength?<br /> - What is the independent association of each assessed nucleus with pupil dilation? That could be informative to understand their shared or unique role.

Reviewer #1 (Public Review):

The manuscript by Mansur et al examines the roles of KLHL40, mutations which lead to the development of skeletal muscle disease (nemaline myopathy, NM). The authors use CRISPR-based gene editing in a model organism (zebrafish) to disrupt the two fish isoforms of KLHL40 (a and b) and examine the resulting phenotypes. The authors find that disease-like phenotypes develop in adulthood selectively with the deletion of the KLHL40a isoform. Phenotypes include reduced body size, reduced endurance, and reduced life span with cellular effects that include perturbations to sarcomere organization, perturbed morphology of secretory organelles and mitochondria, and defects in collagen secretion and ECM deposition. The system provided the advantage of following both development and pre-disease state (onset) allowing the authors to look at changes in translation but mainly in the proteome with a focus on ubiquitylation (followed by mass spectrometry). Selective changes to the proteomthe e in KLHL40a deletion mutant are evident in the pre-symptomatic stage. Pathway analysis suggests that mutant cells show selective increases in glycolytic and biosynthetic enzymes/pathways, perhaps, akin to a Warburg effect. Monitoring the correlation between loss of KLHL40a-dependent ubiquitylation and increased protein levels defined the small GTPase Sar1a as a direct target for KLHL40a-directed degradation. Sar1a interacts with KLHL40a and is ubiquitylated by Cul3-KLHL40 in cell-free and over-expression assays in mammalian cells. Overexpression of Sar1a in muscle leads to endoplasmic reticulum (ER) membrane tubulation and thickening of the Z-lines similar to ones showing in KHLH40a deletion and NM patients. Markedly elevated levels of Sar1a and defects in collagen secretion are also recorded in patients with KLHL40 mutations. These observations suggest that selective control of COPII coat protein Sar1a levels (and thus the activity of the COPII coat, which mediates biosynthetic secretion from the ER), perturbs collagen secretion and ECM deposition. Overall this comprehensive work delineates the roles of Cul3-KLHL40a in the development of NM and specifically in regulating secretion by controlling the levels of one component of the COPII coat. The work is very interesting yet requires additional experimental clarifications and analysis.

Strength

This is a very interesting study showing global developmental and disease onset-related changes to the proteome focusing on changes derived from KLHL40a deletion. The work demonstrates a key role of ubiquitylation and selective protein degradation in the development and muscle disease onset. The global proteome view identified changes to energy production modes and defined direct regulation of Sar1a levels by Cul3-KHLH40a ubiquitylation which regulates ECM secretion, providing a mechanistic explanation for the development of NM in patients with KLHL40 mutations. Furthermore, the study highlights an interesting mechanism in which the levels of an individual component of the COPII coat are controlled by degradation to regulate biosynthetic secretion from the ER.

Weaknesses

There are weaknesses in the analysis that would markedly benefit from added clarifications. The differential outcome with the deletion of klhl40 a and b requires explanation. Morphological observations, which are key to understanding the overall phenotypes of KLHL40a deletion should be developed to provide a better definition of effects on organelle morphology and in particular ones involved in secretion. Some of the transcriptome-proteome data are left unexplored, in particular a view of the unfolded protein response (UPR) within the data, which will complement the documented defects in protein secretion and provide intrinsic controls to the work. The findings on Sar1a and the role of controlled degradation in regulating COPII activities are highly interesting yet a more complete analysis of COPII components is missing. Information on Sar1b, previously implicated in selective effects on secretion, Sec23-Sec24 and ratio (where levels are regulated by ubiquitylation and de ubiquitylation), and outer layer COPII proteins Sec13 and in particular Sec31, which is by itself a target for Cul3-KLHL12 regulation during development and modifies selective biosynthetic secretion, is lacking. Added analysis can provide new perspectives on the potential broader implications and significance of this study.

Reviewer #2 (Public Review):

Mansur et al highlight interesting aspects of KLHL40-mediated proteostatic mechanisms in secretion and skeletal muscle development in zebrafish. They propose that KLHL40-mediated ubiquitylation of functional modules in the muscle proteome, particularly membrane traffic components, regulates protein abundance to control development. The authors present solid evidence for the role of KLHL40-mediated ubiquitylation and degradation of the cellular proteome but would benefit from further supporting evidence for their direct consequences on protein secretion.

Reviewer #3 (Public Review):

The manuscript is addressing the hypothesis that KLHL40, of which mutations lead to a nemaline myopathy, leads to aberrant processing/turnover via the UPS of specific proteins. The aberrant turnover of these specific proteins then leads to the disease phenotype.

The manuscript creates two fish models knocking out orthologs of KHL40 in fish and finds that KHLH40a is necessary for maintaining fish size.

A multi-omic approach identifies potential candidates that are KHLH40 targets, specifically, Sar1a. Overexpression of Sar1a leads to some phenotypic changes ultrastructurally that resemble khl40a knockout. In vitro studies suggest some co-regulation of KHL40a with sar1a but lack the methodologic rigor at this point to be convincing. In addition, whether Sar1a dysregulation leads to more global issues seen in patients and fish remains to be established.

Reviewer #1 (Public Review):

The authors aimed to study the contribution of bacterial factors to poor treatment outcomes in drug-susceptible TB, an important issue that has not been well studied. The authors performed GWAS on a very large population-based (3 sites in China) dataset of 3416 Mtb WGS data of pre-treatment isolates linked with clinical data to predict treatment outcomes. Logistic regression was used to assess the association between predictors and outcomes and ROC curves were generated to assess the value of the genomic signatures to predict poor TB treatment outcomes. The authors were successful in identifying 14 Mtb variants in 13 genes and reactive oxygen species that were more likely to occur in patients with poor treatment outcomes.

The investigators were very thorough, in investigating both fixed and unfixed mutations, and analyzing the changes in gene expression under stress (exposure to first-line drugs and hypoxic conditions) for the 13 genes identified, which further strengthened the evidence generated by GWAS. The authors attempted to perform an external validation of their findings but could not identify a suitable existing dataset.

These data can be used by others to guide their analyses, and confirm if these 13 genes are also found in other settings. If confirmed, then the results could open the possibility for individualised tailoring of treatment of drug-susceptible TB, especially to prevent the risk of relapse.

Reviewer #2 (Public Review):

The availability of large collections of Mycobacterium tuberculosis (Mtb) isolates has enabled many important studies looking to identify mycobacterial genetic polymorphisms associated with anti-tuberculosis (TB) drug resistance, including both classical "resistance-conferring" mutations and novel "resistance-enabling" mutations. Importantly, these studies have expanded our understanding of mycobacterial genetic adaptations undermining chemotherapy, in many cases allowing for improved diagnostic tests and predictions of treatment failure. In this submission, Gao and colleagues adopt a different approach to the problem: although also applying a GWAS-type analysis, they instead attempt to elucidate polymorphisms implicated in poor outcomes of TB patients undergoing treatment for the drug-susceptible disease. Starting with a large dataset comprising 3496 samples with corresponding clinical (host) metadata, the authors generate Mtb whole-genome sequence data for 91 samples obtained from patients with "poor" outcomes and 3105 patients with "good" outcomes. These are used to identify 14 fixed and >230 unfixed mutations that might be associated with "poor" treatment outcomes, a conclusion which they argue is plausible given transcriptional evidence implicating many of the identified genes in the mycobacterial response in vitro to first-line drug exposure and/or hypoxia, both of which are considered relevant to clinical disease. Notably, they also identify a tendency for a greater proportion of "ROS mutational signatures" in unfixed mutations from "poor" outcome samples. Finally, incorporating these observations in a prediction model, the authors observe that the mycobacterial factors aren't adequate on their own but, when combined with key host factors - including patient age, sex, and duration of diagnostic delay (which have stronger predictive value) - they enhance predictive capacity. In summary, this paper reports a novel approach yielding observations that offer tantalizing insight into the mycobacterial factors which might influence TB treatment outcomes independent of drug resistance, however, the following must be considered:

(i) The manuscript provides little to no detail about how the samples were obtained, other than the fact that they comprise "pre-treatment" samples: are they all sputum samples? Were they induced? Similarly, no information is provided about sample propagation: were the samples cultured to achieve sufficient biomass for whole-genome sequencing? If so, in what growth media, for how long, and how many passages? Were all samples treated identically? And were they plated to single colonies - or are the "isolates" referred to throughout the manuscript actually heterogenous populations of potentially different Mtb clones obtained - and propagated - as a mixed sample? This information is critical given the potential that the identified polymorphisms - both fixed and (perhaps even more so) unfixed - might have arisen as a consequence of in vitro (laboratory) manipulation under standard aerobic conditions.

(ii) A key question that arises from this study (and others like it) is whether causation has been adequately established. Ideally, the Mtb genotypes contained within samples obtained pre-treatment should be compared with samples obtained from the same patients following treatment - that is, when the "poor" outcome was manifest. The expectation is that the polymorphisms identified prior to initiation of therapy - especially the 14 fixed mutations - should be evident (even dominant) at the later stage when therapy failed (or at the subsequent presentation in cases of relapse). Recognizing that this is not easily accomplished, though, it seems fair to suggest that the perceived relevance of the identified mutations would be strengthened if the authors were able to provide any other evidence - perhaps from studies of drug-resistant Mtb isolates - supporting their inferred role in undermining frontline treatment.

(iii) Related to the above, the authors make the valid point that their intention here was different from other studies which have deliberately utilized drug-resistant Mtb isolates to identify resistance-conferring and resistance-enabling mutations (such as in the study they cite by Hicks et al). It would be interesting to know, however, if any of the mutations identified in those other studies were also picked up in this work - and, if not, why that might be the case.

(iv) Finally, the analyses presented in this study are heavily dependent on the use of appropriate statistical methods to identify potentially rare genetic polymorphisms. However, as noted for sample processing (see my earlier comment above), there is very little detail provided about the methodology applied. This omission detracts from the interpretation, especially given that the predominance of lineage 2 (which contributes >75% of the isolates, with sublineage 2.3 constituting >50%) risks a lineage-specific association, rather than a more generalizable pathogenicity phenotype. Similarly, the heavy skew in the numbers of "good" (3105 samples) versus "poor" (91 samples) collections (approximately 34x difference in sample size) raises the possibility that mutations identified in the "poor" category might be artificially over-represented. More clarity in detailing the statistical methods is required to allay any concerns about the identification of candidate polymorphisms.

Reviewer #1 (Public Review):

This study sought to establish a model of targeted lung endothelial ablation and subsequently study the regeneration process post-ablation using single-cell RNA-sequencing in order to identify key subpopulations and underlying mechanisms of regeneration.

Strengths of the study include:

1. The elegance of the DT endothelial ablation model which leverages local lung instillation of DT to locally ablate the endothelium and cause significant lung vascular leakiness while keeping the endothelium of other organs intact, as is convincingly demonstrated in Fig 1 and Fig 2.

2. The temporal analyses using scRNA-seq demonstrate key shifts in endothelial and non-endothelial cell populations following endothelial injury. These experiments identify a highly proliferative subpopulation of endothelial cells that expresses the transcription factor FoxM1 during the regeneration phase.

3. The authors discover that the traditionally designated "gCap" lung endothelial population contains additional subpopulations that have regenerative potential and that there is a transient expression of apelin in the regenerative population. Pharmacological inhibition of the apelin receptor increase mortality.

Potential weaknesses include:

1. The description of the "stem-like" nature of endothelial cells is not experimentally proven. "Stem-like" is a vague term and the usage of this term is primarily based on the expression of Procr. However, that itself does not justify the usage of "stem-like" unless there is more clear evidence of what "stem-like" properties these cells have, such as multipotency.

2. The intriguing finding of the proliferative EC population raises the question as to how these cells emerge. Do they have a specific subpopulation/cluster origin in the baseline lung endothelium, and was Apelin expression both necessary as well as sufficient to induce the switch to the proliferative state? Such mechanistic analyses would be very helpful in understanding the coordination of the lung endothelial regeneration program.

3. The authors mention that endothelial ablation also induces shifts in the numbers of other cell types such as epithelial cells, alveolar macrophages, and immune cells but there is no analysis beyond the quantification of the cells. Are these cells involved in the regeneration of the endothelium by providing ligands such as growth factors?

Reviewer #2 (Public Review):

Acute lung injury (ALI) and ARDS are major causes of morbidity and mortality in critically ill patients and patients infected with Sars-Cov-2. There are no effective therapies for ALI/ARDS, and the 28-day mortality rate is ~40%. One of the main pathological features of ALI/ARDS is a vascular injury characterized by endothelial dysfunction, inflammation, and in situ thrombosis. Using a murine model of ALI/ARDS triggered by diphtheria toxin (DT) mediated endothelial specific ablation, the authors apply sc-RNA-seq analysis to study how lung cell populations respond to injury and identify two main endothelial subpopulations responsible for regenerating lung vasculature over seven days. The study's implications are exciting as they provide evidence of intrinsic repair mechanisms that could be targeted for vascular regeneration and recovery of lung function in the context of ALI/ARDS. In particular, the apelin pathway rises as a prime therapeutic candidate given its role in coordinating the behavior of general and aerocyte capillary cells in lung vascular repair.

While the results of this study are exciting and novel, it must be recognized that several limitations need to be properly addressed to facilitate the translation of the findings toward medical care. For instance, the animal model used in this study (DT mediated EC ablation) does not fully recapitulate all the pathological hallmarks of ALI/ARDS, the most important of which is that repair proceeds at a very slow pace as a result of multiple factors that are not recapitulated in this made. Since the authors use only one model of ALI/ARDS, it is not entirely clear whether the current findings can be generalized to other models. Since no one model truly recapitulates the complexity of human ALI/ARDS, it is important to use at least two or more models that can narrow genetic and molecular mechanisms fundamental to lung injury and recovery. Another important aspect is the lack of validation in human samples and cells, which could strengthen the conclusions raised by the authors in the discussion. Finally, the authors appropriately emphasize how this study could help efforts to understand Sars-Cov2 mediated ALI/ARDS. Still, no studies explore any overlap with currently available Omics data from COVID lungs.

Despite these weaknesses, this study is the first to apply rigorous scRNA-seq analysis to this unique model of ALI/ARDS. It also provides data to support the importance of the two newly discovered endothelial cell subpopulations (gCap and aCap) in lung repair and regeneration, which hold the potential to offer unique mechanistic insights into the genetic and molecular mechanisms responsible for vascular repair and offers the opportunity to consider apelin based therapeutic approaches to treat ALI/ARDS. In conclusion, this study is expected to contribute to our lung biology understanding greatly. It provides the research community with novel resources and tools that greatly aid efforts to understand ALI/ARDS and identify therapeutics to treat this devastating disease.

Reviewer #3 (Public Review):

This highly innovative study makes elegant use of single-cell RNA sequencing in a transgenic murine model of selective lung endothelial depletion to study endothelial repair and regeneration. Within 3 days after ablation of 70% of lung endothelial cells, a new stem-like endothelial population expressing markers of general capillary endothelial cells (gCap), yet also apelin, Procr, Angpt2, and CD93, yet not the gCap-typical apelin receptor emerged. This was followed at day 5 by a population of highly proliferative gCap-like endothelial cells expressing the apelin receptor along with FoxM1, which replenished all depleted endothelial populations and allowed for rapid resolution of microvascular injury. These newly identified cell states are highly reminiscent of tip and stalk cells in sprouting angiogenesis and may guide the development of new regenerative strategies.

Strengths:<br /> The present work provides important novel insights into the mechanisms of endothelial repair and reconstitution. Importantly, the authors identify a subset of gCap cells that upon endothelial depletion develops into a stem cell-like population expressing (among others) apelin, which signals via the apelin receptor to another, progenitor-like cell population that arises subsequently from the former stem cell-like population. These findings shed new light on the process of microvascular "healing" in acute lung injury and ARDS, and open up intriguing parallels to processes well known from angiogenic sprouting that may be exploited for therapeutic purposes.

Weaknesses:<br /> As with every innovative study, the emerging answers give rise to a series of new questions. Notable among those is the identity of the signal that initially drives the transition of the stem cell-like gCap population from their basal state - the recognition of such a signal may allow replicating the proposed cycle in vitro, with the opportunity to harvest cells at specific time points for both research and therapeutic purposes. Similarly, one may wonder how a lung may survive with 70% of its endothelial cells gone - do the respective vascular segments simply get excluded from perfusion (and, possibly, ventilation, as AT-II cells also decline in parallel, resulting in an emphysematous phenotype) or does fluid simply leak into the interstitium (which seems hard to reconcile with survival)? From a methodological point of view, RNA velocity analyses may be considered in follow-up studies to further substantiate the notion of a gradual transition of a subset of gCap cells from a basal to a stem cell-like to a progenitor-like and back to a basal state.

Reviewer #2 (Public Review):

The authors utilized a label-free LC-MS/MS analysis in formalin-fixed paraffin-embedded (FFPE) tumors from 143 LNM-negative and 78 LNM-positive patients with T1 CRC to identify protein biomarkers to determine LNM in T1 CRC.

The authors used a fair number of clinical samples for the proteomics investigation. The experimental design is reasonable, and the statistical methods used in this manuscript are solid.

The authors largely achieved their aims and the results supported their conclusion. The method used in this proteomic study can also be used for the proteomics analysis of other cancer types to identify diagnostic and prognostic biomarkers. In addition, the 9 marker panel has a potential clinical diagnosis practice in determining LNM in T1 CRC.

Nevertheless, the authors need to justify their standards in selecting the biomarkers. For example, a p-value cut-off of 0.1 is not a usual criterion in similar proteomic studies. In addition, an identification frequency of 30% in patients seems not preferable for biomarker identification. The authors also need to justify the definition of fold change in the three subtypes with Kruskal-Walli's test. The authors need to describe more details on how they identified the 13 proteins from a 55-protein database. In addition, what is the connection between the final 9 proteins and the 19 proteins? What is the criterion to select 5 proteins for IHC validation from the 9 proteins?

Reviewer #3 (Public Review):

This work provides a proteomic analysis of 132 early-stage (pT1) colorectal cancers (CRC) to attempt to identify proteins (or a signature pattern thereof) that might be used to predict the patient risk of lymph node metastases (LNM) and potentially stratify patients for further treatment or surveillance. The generated dataset is extensive and the methods appear solid. The work identifies a 55-protein signature that is strongly predictive of LNM in the training cohort and two validation cohorts and then generates two simplified classifiers: a 9-protein proteomic and a 5-protein immunohistochemical classifier. These also perform very well in predicting LNM. Loss of the small GTPase RHOT2 is identified as a poor prognostic factor and validated in a migration assay. The findings could allow better prognostication in CRC and, if confirmed and better validated and contextualized, might impact patient care.

Strengths:<br /> A large training cohort of resected early-stage (pT1M0) CRCs was analyzed by rigorous methods including careful quantitative analysis. The data generated are unbiased and potentially useful. A number of proteins are found to be different between CRCs with and without lymph node metastases, which are used to train a machine learning model that performs flawlessly in predicting LNM in the training cohort and very well in predicting LNM in two validation cohorts. The authors then develop two simplified classifiers that might be more readily extended into clinical care: a 9-protein proteomic assay and a 5-protein immunohistochemical assay; both of these also perform well in predicting LNM. Because LNM is a key prognostic factor, and colectomy (which includes removal of lymph nodes needed to assess LNM) carries significant risk and morbidity, particularly in rectal cancer, classifiers like these are potentially interesting. Finally, the authors identify the loss of expression of RHOT2 as a novel prognostic factor.

Weaknesses:<br /> Major points:<br /> The data are limited by a number of assumptions about metastasis, minimal contextualization of the results, and claims that are too strong given the data. Critically, the authors use the presence or absence of LNM as the study's only outcome; while LNM is a key predictor in CRC, it is uncommon in T1 CRC (generally 3-10%, 12% in this study), stochastic, inefficient, and incompletely identified by histologic evaluation. Larger resection (here, colectomy) removes both identified and occult LNM, which is probably best studied in randomized trials of lymphadenectomy in Japanese gastric cancer cohorts and should be better discussed. Critically, patient survival or disease-free survival would be more relevant outcomes. Further, absent longer-term data, many patients without identified LNM might nonetheless be high-risk and skew the cohorts. It is also not clear whether these findings would be generalizable to other early-stage colon cancers.

The data are also not correlated with the genetics of the cases, which were not discussed. The results would benefit from the inclusion of standard-of-care MSI status. The classifiers would also be much more impactful if they were generalizable beyond T1 CRCs; this could be readily tested in public datasets.

The authors explain the data as mechanistic, but, aside from one experiment modulating RHOT2 levels, they are fundamentally correlative and should be described as such.

Although they focused on areas containing >80% tumor as judged by the reading pathologist, it is unclear whether the identified proteomic changes originate from the tumor or the microenvironment.

The authors fail to properly contextualize the results or overstate the novelty of their study. A number of examples - the study is claimed as "the first proteomic study of T1 CRC" and "the first comprehensive proteomics study to focus on LNM in patients with submucosal T1 CRCs"; neither of these appears to be true, for example, Steffen et al. (Journal of Proteome Research, 2021, reference 18) may satisfy both of these, although the numbers are smaller. Many other results are reported without context, for example, proteomic characterization of mucinous carcinomas has been performed previously, a modest correlation in mucinous carcinoma is ascribed a large mechanistic role, and PDPN is discussed but is not contextualized as a protein that has been well-studied in the context of metastasis.

The data on RHOT2 are promising but very preliminary. RHOT2 is described as ubiquitous in colorectal cancer cell lines; a brief search in Human Protein Atlas shows RHOT2 RNA and proteins are ubiquitously expressed throughout the body. While its loss appears potentially prognostic, it is unclear whether this is simply a surrogate for other features, such as loss of differentiation state, and whether this is unique to CRC; multivariate analysis would be important.

Reviewer #1 (Public Review):

Lammer et al. examined the effects of social loneliness, and longitudinal change in social loneliness, on cognitive and brain aging. In a large sample longitudinal dataset, the authors found that both baseline loneliness and an increase in loneliness at follow-up were significantly associated with smaller hippocampal volume, reduced cortical thickness, and worse cognition in healthy older adults. In addition, those older adults with high loneliness at baseline showed even smaller hippocampal volume at follow-up. These results are interesting in identifying the importance of social support to cognitive and brain health in old age. With a longitudinal design, they were able to show that increased loneliness was related to reduced brain structural measures. Such results could help guide clinicians and policymakers in designing social support systems that would benefit the growing aging population.

The strength of the current study lies in the large sample size and longitudinal follow-up design. The multilevel models used to separate within and between subject effects are well constructed. Combining neuroimaging data with behavioral changes provided further evidence that social loneliness may be related to accelerated brain aging. Stringent FDR correction, Bayes factor comparison, and the additional analyses for sensitivity showed the robustness and credibility of the results.

Weaknesses of the study were related to the interpretation and discussion of their findings.

Social loneliness is a relatively little-studied factor in cognitive ageing, and the authors should consider expanding the discussion, with some additional analyses, as to how their results could be used by clinicians and older adults to monitor social behaviors.

The authors examined the interaction between baseline and age change to see if higher baseline loneliness was associated with accelerated decline. The interaction was significant, but the authors did not further explore the interaction effect, which may have clinical significance. The authors should consider identifying a cut-off point in LSNS that suggests persons scoring less than this score on the LSNS may be at greater risk of accelerated brain decline than others. Such a cut-off point is important for clinicians, as well as for future researchers to compare their results.

Although it was not directly tested in the paper, LSNS scores did not seem to change with increasing age (Table 1). This general stability of LSNS scores in older adults should be discussed further. The authors should consider how their relatively healthy and high SES sample may be less vulnerable to loss of family or friends in old age, making this sample sub-optimal for the question they have. The significance of the subject effect suggests that some individuals still experience a loss of social connectedness. The authors may want to elaborate on this and give some explanations of such subject differences in the ageing effect on social loneliness. Although stress was not a significant mediating factor, is it related to baseline loneliness or changes in loneliness in the current sample?

The presentation of longitudinal data (Figure 1) lacks dimensionality. The scatter plots presented here are more suitable for cross-sectional studies and could cause confusion regarding the interpretation of the results. The authors should consider individual growth curves or spaghetti plots in visualizing change within subjects.

Reviewer #2 (Public Review):

The paper by Laurenz Lammer and colleagues used cohort data to investigate the cross-sectional and longitudinal association between loneliness and brain structure and cognitive function. The main finding was that baseline social isolation and change in social isolation were associated with smaller hippocampus volumes, reduced cortical thickness, and poorer cognitive function. Given that more and more people feel lonely nowadays (e.g., due to the pandemic), the study by Lammer and colleagues addresses a highly relevant health concern of our time.

Significant strengths of the study:

- large cohort;<br /> - the cross-sectional and longitudinal analyses confirmed the findings;<br /> - the study was preregistered;<br /> - the study included men and women;<br /> - analyses were sound and controlled for essential confounders.

The major weaknesses of the study:

- it is unclear whether loneliness causally contributes to brain structure and cognitive function;<br /> - the factors that may cause loneliness are unclear.

Reviewer #1 (Public Review):

Muscle is a major insulin-responsive tissue for the disposal of glucose, a process dependent on the translocation of GLUT4 glucose transporter from intracellular compartments to the plasma membrane. Knudsen and co-workers provide an analysis of the impact of microtubule-based movement on GLUT4 biology in muscle cell lines, and rodent and human muscle fibers ex vivo. A role for microtubules in the control of GLUT4 vesicle dynamics in both unstimulated and insulin-stimulated adipocytes (cultured and primary) has been previously reported by a number of groups. Less is known about the requirement for microtubules for GLUT4 translocation in muscle. A strength of this study is that key aspects of the work were performed in muscle fibers rather than muscle cell lines.

Conclusions that are strongly supported by the data presented include:

1. Demonstration of constitutive GLUT4 movement along microtubule tracks in both unstimulated and insulin-stimulated muscle fibers. GLUT4 dynamics in unstimulated fibers were captured by fluorescence recover after photobleaching (FRAP) and by quantifying vesicle movements by live cell microscopy, whereas in insulin-stimulated cells GLUT4 dynamics were captured by following the movements of GLUT4-containing vesicles. These data support a model in which intracellular GLUT4 is dynamic in both unstimulated and insulin-stimulated muscle fibers rather than being static in unstimulated conditions and only mobilized upon insulin-stimulation.

2. Similar microscopy analyses of GLUT4-containing vesicles demonstrate that depolymerization of microtubules reduced GLUT4 vesicle movement and impacted insulin-stimulated glucose uptake. Short term depolymerization of microtubules (5 min) did not affect insulin-stimulated glucose uptake, whereas insulin-stimulated glucose uptake was blocked after prolonged depolymerization (2 hrs). The use of a muscle on a chip method to monitor glucose uptake in real time was critical for these experiments.

The changes in glucose uptake were accompanied by changes in the morphologies of intracellular GLUT4-containing structures. The differences between short and long term depolymerization of microtubules support a model in which GLUT4 can be translocated to the plasma membrane by insulin stimulation in the absence of microtubules but an intact microtubule cytoskeleton is required to maintain GLUT4 in a "compartment" that can be recruited by insulin. Stated another way, the microtubule-dependent dynamics of GLUT4-containing vesicles in unstimulated cells is permissive for insulin-stimulated GLUT4 translocation.

3. Knockdown of the microtubule motor protein, Kif5b, blunts insulin-stimulated translocation of GLUT4 to the plasma membrane of cultured muscle cells. These findings agree with previously demonstrated role for Kif5b in adipocytes.

4. In an in vitro model of insulin resistance (incubation of muscle fibers with short chain C2 ceramide) unstimulated and insulin-stimulated GLUT4-containing vesicle movement was blunted and unstimulated and insulin-stimulated microtubule polymerization was reduced.

Weakness of the study include:

1. There are no data supporting a role for insulin regulation of microtubule-dependent GLUT4-containg vesicle movement. The data in Fig.2B do not support a differences in the number of "moving" GLUT4 vesicles between basal and insulin-stimulated fibers. The statement on line 103 that they "observed a ~16% but insignificant increase" to be confusing. These data do not support an effect of insulin on the number of moving GLUT4 vesicles that can be detected in an individual experiment. There is also effect of insulin on GLUT4 vesicles in the data reported in Fig.S2D, Fig.S5B, and Fig.S5F. However, the data in Fig. 2C suggest there was a consistent increase in "moving" vesicles in insulin-stimulated conditions in 4 independent experiments (how are these data normalized?). Because the basis of insulin-regulation of glucose uptake is the control of GLUT4 translocation to the plasma membrane, the authors need to clarify their thinking on why they do not detect insulin robust effects on GLUT4 dynamics in the individual experiments. Is it that they are not measuring the correct parameter? That the assay is not sensitive to the changes?

The small (or no effect) of insulin distracts a bit from the findings that there is microtubule-dependent GLUT4 movement in basal and stimulated muscle fibers, and that disruption of this movement by depolymerization of microtubules or Kif5b knockdown blunts GLUT4 translocation. As noted above, the data strongly support microtubule-dependent GLUT4 dynamics as permissive for insulin-stimulated GLUT4 translocation even if this dynamics might not be a target of insulin action.

2. The analyses of GLUT4-containing structures are not particularly informative. Co-localization with other markers (beyond syntaxin6) are needed to understand these structures. Defining structures as small, medium or large is incomplete. In particular, it is important to probe the microtubule nucleation site clusters for other membrane markers. Transferrin receptor? IRAP?

3. The Kinesore data do not support the authors hypothesis. The data show that Kinesore increases the amount of GLUT4 in the plasma membrane of basal cells and that insulin further increases plasma membrane GLUT4 to the same extent as it does in control cells. How does that provide insight into the role microtubules (or kif5b) in GLUT4 biology? Why does Kinesore increase plasma membrane GLUT4? Is it an effect of Kinesin 1 on GLUT4 vesicles? Kinesore is reported to remodel the microtubule cytoskeleton by a mechanism dependent on Kinesin 1. Is that the reason for the change in GLUT4?

4. The analysis of Kif5b is a bit cursory. Depolymerization of microtubules in muscle fibers essentially blocks all GLUT4 movement (only the insulin condition is shown in Fig.2B but I assume basal would be equally inhibited), and fully inhibits insulin-stimulated glucose uptake in muscle fibers. What are the effects of nocodazole in L6 cells (cell used for kif5b studies) and is it similar in magnitude to kif5b knockdown? Those data would identify there are non-Kif5b microtubule-dependent effects.

5. The authors need to show that the fibers isolated from the HFD mice remain insulin-resistant ex vivo by measuring glucose uptake. It is possible that once removed from the mice they "revert" to normal insulin-sensitivity, which might contribute to the differences reported in Fig5.

6. Although it is interesting that the authors have included the insulin-resistance models/experiments, they are not well developed and therefore the conclusions are not particularly strong.

7. The data do not support the title.

Reviewer #2 (Public Review):

Overall, this manuscript provides a thorough characterization of the role of microtubules in the movement of GLUT4 in muscle fibers, and demonstrates the need for an intact microtubule network for GLUT4 responsiveness but only after the initial round of response.<br /> The study poses a very interesting question, rooted in studies in the literature studying the effects of Nocodazole (Noco) and C2-ceramide on GLUT4 traffic in cell systems. It is important to validate or refute predictions from those studies and, largely through this group's work, the quest to examine these questions in isolated muscle fibers and intact muscles as feasible is commendable. The authors develop very interesting imaging approaches to this end, and quantify the results in a convincing and elegant fashion. The system to measure 2-DG uptake and glucose uptake by electrochemical sensing in isolated fibers using the microfluidic pump is very ingenious.<br /> The main conclusion that microtubules are important for GLUT4 proper localization is important and adds mechanistic insight beyond that obtained from work in myoblasts and pre/adipocytes. The observation that microtubules are not engaged in GLUT4 traffic in the first round of insulin action but it is thereafter is also very revealing and should lead to more insights into the first and subsequent rounds of GLUT4 translocation.

Reviewer #1 (Public Review):

The authors study the control of the timing of Q neuroblast migration, through the precisely timed expression of the Wnt receptor MIG-1/Frizzled, which halts migration of the QR.pa cell at its intended position. Understanding the underlying mechanism is important, as similar mechanisms might play a role in controlling the timing of biological processes in development much more broadly. The authors use precise measurements of mig-1 mRNA molecules, fitted to mathematical models of different mechanisms to control the timing of mig-1 expression, and couple this with experimental perturbations of mig-1 expression. In this way, the authors convincingly show that mig-1 dynamics is best explained by a model where mig-1 expression is controlled by the accumulation of an activator, rather than the degradation of a repressor, which is an important result. In addition, they show that the asymmetric division of QR.p into the larger QR.pa and smaller QR.pp cells is important for proper mig-1 expression in Qr.pa, likely by asymmetric inheritance of the activator. In the process, the authors identify novel conserved binding motifs that are responsible for different aspects of mig-1 dynamics, which will potentially allow identifying the putative activator in the future.

In its current form, I find the manuscript has two main weak points: First, the connection between the experiments and models is relatively weak. Now, the model is mostly used to aid the interpretation of experiments, by predicting rough trends. However, even though the model is in principle fitted to the experimental data in some cases, a detailed comparison between experimental results and the model is often lacking. For example, there are multiple occasions where the data appears to not fit the model in some aspects, but the potential origin of these mismatches is typically not discussed. Second, the authors present experimental evidence of an earlier model prediction, that positive feedback loops in mig-1 expression reduce variability in timing. Here, the authors speculate that this feedback loop might be due to the activation of mig-1 expression by mig-1-induced Wnt signaling, which in itself is an interesting idea. However, the genetic perturbation used here - manipulation of the Wnt pathway, rather than perturbing specifically the induction of mig-1 expression by Wnt signaling - likely changes the expression of many genes in the cell, making it difficult to establish whether the increased variability in Qr.pa position is indeed due breaking the proposed feedback loop.

Reviewer #2 (Public Review):

Schild et al. investigate the regulation of temporal control during neuroblast migration in the roundworm C. elegans. The authors find that expression of the Wnt pathway receptor Mig1 is regulated early through a specific noncoding conserved intronic element and later through two specific upstream conserved DNA elements. The expression levels of Mig1 in QR.pa cells are further regulated through Ced-3 and pig-1. The variability in the timing of later expression of Mig1 in QR.pa cells through bar-1 or a terminally truncated version of Bar1 was modulated but the mean expression did not change.

The single molecule RNA-FISH data is strong, and this method is sensitive enough to detect differences between different single cells and mutants. The mutants are very precise and straightforward to interpret. An additional strength is that many cells and replicas have been measured. The data analysis is simple.

The proposed model is simple with few intuitive parameters. This makes parameter identification straightforward. The qualitative predictions do make sense and are consistent with most experimental observations.

Overall the manuscript addresses the important question of timing regulation in transcription.

Reviewer #1 (Public Review)

This paper utilizes two well-established mathematical models of colorectal cancer (CRC) screening to estimate the impact of disruptions in screening caused by the COVID-19 pandemic on long-term outcomes related to CRC. For screening, the authors use two recommendations from the US Preventive Services Task Force (USPSTF) (which were informed by the results of these models): screening colonoscopy every 10 years at ages 50, 60, and 70, and annual fecal immunochemical tests (FIT) from ages 50-75. Separate model runs were performed for 8 different cohorts at the time of the pandemic based on age, screening history, and adherence to screening. For each cohort, microsimulations were performed for 3 different scenarios--no disruption, delays in screening, or discontinuation from screening. The primary outcome was life-years gained (LYG) from screening.

In general, severe prolonged disruptions in any screening led to the largest loss of benefit from screening - for example, unscreened 50-year-olds forced to wait until age 65 (Medicare eligibility) had the largest absolute and relative loss in screening-associated LYG compared to shorter delays of 18 months or less. Losses were also higher in those who were semi-adherent to screening recommendations. The prolonged disruption had a consistently much greater impact than short-term reductions, changes in regimen, or assumptions about test sensitivity. The results are consistent between the two models. The authors point out that, since pandemic-induced disruptions in insurance coverage had a greater impact on minority populations already at risk for reduced access to screening and other preventive services, the pandemic may lead to further exacerbations in existing disparities in CRC incidence and mortality.

The strengths of this paper include the use of well-validated models, the consistent results between the models, the relatively intuitive nature of the findings, and the use of LYG, a commonly used metric for screening recommendations. As the authors point out, estimates of the population impact of the pandemic given the current age structure of the US would be helpful, these would be inherently speculative given the lack of empirical data on pandemic effects on screening. Although prioritizing screening individuals with long pandemic-induced delays is clearly the optimal policy approach, how this might be achieved is unclear.

Reviewer #1 (Public Review):

In this study, the authors use open-access datasets of Neuropixel recordings to explore the relationship between ripple strength and propagation in the septal/dorsal hippocampal pole. They found that the ripple strength correlates with the direction of propagation and that the duration of the events is dependent on the site of initiation. Medial pole ripples are longer and engage significantly more neurons than lateral ripples. These findings may have theoretical and practical implications for the study of sharp-wave ripples, a main oscillatory event underlying memory consolidation. While the approach is not entirely novel (e.g. Patel et al., JN 2013; Kumar and Deshmukh 2020), the study provides some additional insights. The strength of evidence of propagation dynamics is solid and claims are broadly supported. Some points however may require revision. In particular, issues regarding the definition of the longitudinal and transversal axes, as well as additional analysis on microcircuit interactions and neuronal dynamics per cell types and hippocampal sectors should be more thoroughly addressed in support of mechanisms.

Reviewer #1 (Public Review):

Nikolaos Koutras et al shed light on potential distinct functions of the Src family kinases (SFKs) Lck and Lyn in lymphoid signal transduction. The authors therefore overexpress Lyn and ectopic Lck in the B lymphoid cell line BJAB in an elegant Dox-inducible manner and compare the SFK's ability to trigger and shape B-lymphoid signal transduction. The findings indicate that ectopic expression of Lck is sufficient to phosphorylate the B cell receptor (BCR) ITAMs in BJAB cells. In these cells, constitutive ITAM and ITIM phosphorylation by both overexpressed Lck and Lyn induces BCR signaling, as demonstrated by phosphorylation of Syk and Akt, as well as CD22 inhibitory signaling, as shown by SHP-1 phosphorylation. In direct comparison, the influence of Lyn on said phosphorylation is stronger when it is (over-)expressed in the same amounts as Lck. This outcome was somewhat expected, since ITIM/ITAM phosphorylation is considered to be the principal function of Lyn in B cells.

The study finds Lyn to be degraded more efficiently via the proteasome and to be more tightly controlled by phosphatases when compared to Lck. However, rather than interpreting the findings as distinct kinase-intrinsic properties, one could attribute the slower degradation and stricter PTP control of Lyn to the fact that Lyn is the principal and predominant SFK in B cells and thus a "standard target" of the B-lymphoid molecular machinery, to which it is better adapted to.

Next, the authors present a RNAseq transcriptome analysis of Lck- and Lyn-expressing B cells and validate selected findings via qPCR. The data show Lyn and Lck to regulate pathways and biological functions of critical importance to B lymphocytes. Generally, most of the Lck/Lyn-regulated biological functions and pathways shown here (antigen presentation, cytokine production, migration, apoptosis, autophagy, etc.) are well known to be controlled by BCR signaling, which the overexpression of SFKs are constitutively activating, as shown earlier. While the authors draw a Venn diagram depicting differentially regulated transcripts between Lck- and Lyn-expressing cells, it does not seem like Lck is able to regulate pathways which are not "canonically" regulated by Lyn. There is also the persisting problem of Lck being expressed to a much higher extent and the effect of the endogenously expressed Lyn, since the model systems are not based on a Lyn-deficient cell line.

Lastly, the authors follow up their finding of deregulated transcripts belonging to the ER/UPR ontology cluster. Flow cytometric analysis indeed shows an influence of Lck and Lyn expression on ER homeostasis, which can be reverted with SFK inhibitors. Alas, additional follow-up experiments to functionally investigate the deregulated pathways suggested by the RNAseq analysis are not included in this study.

While there definitely are implications for the role of ectopic expression of Lck in CLL cells, this work however presents no direct comparison of expression strength or signaling outcomes between the study's BJAB (Burkitt lymphoma) cell line-based model and a model of CLL - be it a mouse model, human patient samples or a CLL cell line. Since the B-lymphoid cell line used, the Burkitt lymphoma line BJAB, is not CLL-derived, the conclusions that can be drawn for the pathophysiology of CLL is limited.

In principal, the authors show that the Src kinase Lck - when ectopically expressed - largely fills out the role of the predominant B-lymphoid Src kinase Lyn, namely phosphorylation of the CD79-ITAMs and induction of constitutive antigen receptor signaling. Given that the established role of Lck is the phosphorylation of ITAMs and activation of the T cell receptor in T cells, where it is predominantly expressed, these findings provide limited advancement of our current understanding of antigen receptor signal transduction. As a distinct functional difference between Lck and Lyn is not established in this work, said SFKs' largely exclusive expression in T and B cells remains enigmatic.

Reviewer #2 (Public Review):

The normally T cell restricted Src family tyrosine kinase Lck is ectopically expressed in most B cell Chronic Lymphocytic Leukemias. This, along with the fact that ectopic expression of other SFKs, such are Fyn and Fgr, are not seen, suggests that Lck may have some unique function, distinct from the endogenous Lyn SFK, that promotes malignant transformation. Using inducible expression in a human B cell lymphoma, the study explores this possibility. Studies reveal no qualitative functional differences in Lck and Lyn that are likely to explain its unique ectopic expression of Lck in CLL.

The strengths of this study include the use of Lentiviral transfer of genes encoding SFKs in conjunction with Doxycycline inducible expression. This allows comparative analysis of acute Lyn and Lck overexpression effects, free of cell resetting artifacts consequent to long term expression of the SFK. Strength is also seen in the authors fluorescent tagging of the SFK so analysis could be gated on ectopic expression level. Strength exists in the authors dissection of SFK effects on early events in the BCR signaling pathway, which reveal the ability of both overexpressed SFKs to drive receptor ITAM tyrosine phosphorylation and initiating BCR signaling. These studies reveal little difference in the function of the SFKs, though it appears that Lck may be less sensitive to phosphatase regulation.

It is unclear from the material and methods whether the overexpressed Lyn is LynA or Lyn B. It appears in the text (lines 130-133) that they overexpress LynB specifically. A recent paper from Tania Freedman (Sci Adv 2022 PMID:35452291) suggests that LynA is more activating whereas LynB is more balanced with an inhibitory bias. The point is that it is important to discuss this because they may not be making a relevant comparison.

If Lck promotes pathophysiology by transduction of a qualitatively unique signal, one would expect that transcriptome analysis should reveal this difference. The authors look for this signal using transcriptome analysis of bulk populations expressing similar levels of SFK. Although differences were seen in the transcriptome, finding were not consistent with a qualitatively unique function. However, bulk transcriptomic analysis may miss important differences. Single cell RNAseq, e.g., by 10x, may have been more incisive because gene expression could have been normalized to SFK expression in individual cells.

Finally, while some interesting differences are seen in the biology of Lyn and Lck, weakness exists in the failure to explore the causality of these differences in driving CLL phenotype. A final thought relevant to this comment. It is a truism that "absence of proof is not proof of absence".

Reviewer #1 (Public Review):

Members of the SLC11/NRAMP family of transporters permit the movement of transition metals across cell membranes in all kingdoms of life. The current study builds off previous structural and mechanistic work on the SLC11/NRAMP family of transporters by Manatschal and colleagues reported in eLife; the current study presents a cryo-EM structure of a plant aluminum (Al3+) transporter that combats aluminum toxicity in soil. The structure was not determined in the presence of added metal ions, so the paper also employs a variety of established functional assays to test the effects of mutating suggested binding site residues. One notable result is the identification of a mutation (S68A) that maintains divalent transport but disrupts trivalent binding/transport. Strengths of the manuscript include the extensive legwork required to identify a combination of plant homologue, cameloid nanobody, and amphipol that is required to provide homogenous protein and interpretable cryo-EM data. The cryo-EM maps are reliable with low orientation bias and clear features. In addition, the authors perform a number of biochemical and transport assays with divalent metals to bolster their structural model.

Reviewer #2 (Public Review):

In this work, the authors aimed to understand the ion selectivity mechanism of a plant NRAMP-related aluminum transporter by structural and biochemical characterizations.

The authors successfully identified SiNRAT as a promising candidate for structural and biochemical analyses, showed that SiNRAT transport various divalent cations as well as binding to trivalent cations, determined the cryo-EM structure of SiNRAT, and performed structure-based mutational analysis to identify a potential binding site for metal ions. Unfortunately, the authors failed to show direct evidence of Al3- transport, due to technical problems. Furthermore, the structure of SiNRAT in complex with Al3+ was also not shown.

Despite such weakness, the structural comparison with other NRAMP members with different ion selectivity properties together with the extensive biochemical analyses would support the statement by the authors on a mechanism of ion selectivity for Al3+.

In the discussion section, the authors posed an important question. Considering the weak ion selectivity of SiNRAT over divalent cations, it is still unclear how NRAT proteins can function as an Al3+ transporter in a physiological condition where other divalent cations are also abundant. This would be an important question to be addressed in the related research field in the future.

The methods section is well written and the atomic coordinates and EM map file will be available to the community.

Reviewer #3 (Public Review):<br /> <br /> This paper addresses the structure and mechanism of a presumed Al3+ transporter from the NRAMP superfamily from the plant Setaria italica. This protein belongs to a small clade of NRAMPs, termed NRATs that are postulated to protect plants from Al3+ which is both toxic and prevalent in soil. The NRAT clade is characterized by the substitution of key amino acids at the substrate binding site which has been shown to coordinate either Mg2+ in NRMTs or Mn2+ in classical NRAMP transporters. Evidence for Al3+ transport comes from a previous study utilizing heterologous expression in yeast; this study concluded that NRAT1 from rice (Oryza sativa) is highly specific for Al3+ over Mn2+, Fe2+, Cd2+, Mg2+ which have been shown to be transported by homologs in other clades of the NRAMP family. The current study screened the expression of five homologues of NRAT1, choosing SiNRAT for structural and functional analysis. Unlike previous work on NRAT1, SiNRAT readily transported Mn2+, and experiments with Ca2+ and Mg2+ indicate that these ions are likely also transported. Unlike classical NRAMPs, Mn2+ transport appears to be passive and not coupled to proton transport. Although technical limitations precluded direct measurement of Al3+ transport, ITC measurements provided qualitative evidence for binding in the uM range. A cryo-EM structure is presented, showing an occluded conformation similar to the recent high-resolution X-ray structure of a classical NRAMP bound to Mn2+. The structure of SiNRAT does not show bound ions, but allows comparison of the substrate binding pocket and shows the disposition of key amino acids that distinguish the NRAT clade. Finally, mutagenesis was used to evaluate the role of four of these residues, thus concluding that Ser68 plays a role in coordinating Al3+ as well as its analog Ga3+. Thus, although the transport data with Mn2+ are rigorous, interactions of the putative substrate, Al3+, are only addressed in a qualitative way. The cryo-EM structure is similarly rigorous but provides only modest insight into substrate specificity. Furthermore, the discussion of proton coupling - or the lack thereof - is very speculative. Thus, although new information on this novel clade of NRAMP transporters will be welcomed by specialists in this field, the paper is likely to have only a modest impact beyond this cohort.

Reviewer #1 (Public Review):

In this paper the authors are estimating the amount of transmission (via the force of infection) of EV-D^8 in England. The strengths of the study are the use of serological data for understanding underlying transmission, and the assessment of the sensitivity of the conclusions to the seropositivity cut off and the model form used. The weaknesses are the data not being annually and the lack of link to HFMD cases,, but these do not detract from the conclusions that can be drawn from the paper. The results do support the conclusions.

Reviewer #2 (Public Review):

The authors use data from 3 cross-sectional age-stratified serosurveys on Enterovirus D68 from England between 2006 and 2017 to examine the transmission dynamics of this pathogen in this setting. A key public health challenge on EV-D68 has been its implication in outbreaks of acute flaccid myelitis over the past decade, and past circulation patterns and population immunity to this pathogen are not yet well-understood. Towards this end, the authors develop and compare a suite of catalytic models as fitted to this dataset and incorporate different assumptions on how the force of infection varies over time and age. They find high overall EV-D68 seroprevalence as measured by neutralizing antibodies, and detect increased transmission during this time period as measured by the annual probability of infection and basic reproduction number. Interestingly, their data indicate very high seroprevalence in the youngest children (1 year-olds), and to accommodate this observation, the authors separate the force of infection in this age class from the other groups. They then reconstruct the historical patterns of EV-D68 circulation using their models and conclude that, while the serologic data suggest that transmissibility has increased between serosurvey rounds, additional factors not accounted for here (e.g., changes in pathogenicity) are likely necessary to explain the recent emergence of AFM outbreaks, particularly given the broader age-profile of reported AFM cases. The Discussion mentions important current unknowns on the biological interpretation of EV-D68 neutralizing antibody titers for protection against infection and disease. The analysis is rigorous and the conclusions are well-supported, but a few aspects of the work need to be clarified and extended, detailed below:

1) Due to the lack of a clear single cut-point for seropositivity on this assay, the authors sensibly present results for two cut-points in the main text (1:16 and 1:64). While some differences that stem from using different cut-points are fully expected (i.e., seroprevalence being higher using the less stringent cut-point), differences that are less expected should be further discussed. For instance, it was not clear in Figure 2 why the annual probability of infection decreased after 2010 using the 1:64 cut-point, while it continued to increase using the 1:16 cut-point. It would also be helpful to explain why overall seroprevalence and R0 continue to increase over this time period using the 1:64 cut-point. Lastly, it would be useful to see the x-axis in Figure 4 extended to the start of the time period that FOI is estimated, with accompanying credible intervals.

2) Additional context of EV-D68 in the study setting of England would be useful. While the Introduction does mention AFM cases "in the UK and elsewhere in Europe" (line 53), a summary of reported data on EV-D68/AFM in England prior to this study would provide important context. The Methods refers to "whether transmission had increased over time (before the first reported big outbreak of EV-D68 in the US in 2014)" (lines 133-134), rather than in this setting. It would be useful to summarize the viral genomic data from the region for additional context - particularly since the emergence of a viral clade is highlighted as a co-occurrence with the increased transmissibility detected in this analysis.

Reviewer #3 (Public Review):

In the proposed manuscript, the authors use cross-sectional seroprevalence data from blood samples that were tested for evidence of antibodies against D68 for the UK. Samples were collected at 3 time points from individuals of all ages. The authors then fit a suite of serocatalytic models to explain the changing level of seropositivity by age. From each model they estimate the force of infection and assess whether there have been changes in transmissibility over the study period. D68 is an important pathogen, especially due to its links with acute flaccid myelitis, and its transmission intensity remains poorly understood. Serocatalytic models appear to be appropriate here. I have a few comments.

The biggest challenge to this project is the difficulty in assigning individuals as seronegative or seropositive. There is no clear bimodal distribution in titers that would allow obvious discrimination and apparently no good validation data with controls with known serostatus. The authors tackle this problem by presenting results to four different cut-points (1:16 to 1:128) - resulting in seropositivity ranging from around 50% to around 80%. They then run the serocatalytic models with two of these (1:16 and 1:64) - leading to a range of FoI values of 0.25-0.90 for the 1 year olds and 0.05-0.25 for older age groups (depending on model and cutpoint). This represents a substantial amount of variability. While I certainly see the benefit of attacking this uncertainty head on, it does ultimately limit the inferences that can be made about the underlying risk of infection in UK communities, except that it's very uncertain and possibly quite high.

I find the force of infection in 1 year olds very high (with a suggestion that up to 75% get infected within a year) and difficult to believe, especially as the force of infection is assumed much lower for all other ages.

The authors exclude all <1s due to maternal antibodies, which seems sensible, however, does this mean that it is impossible for <1s to become infected in the model? We know for other pathogens (e.g., dengue virus) with protection from maternal antibodies that the protection from infection is gone after a few months. Maybe allowing for infections in the first year of life too would reduce the very large, and difficult to believe, difference in risk between 1 year olds and older age groups. I suspect you wouldn't need to rely on <1 serodata - just allow for infections in this time period.

Relatedly, would it be possible to break the age data into months rather than years in these infants to help tease apart what happens in the critical early stages of life.

One of the major findings of the paper is that there is a steadily increasing R0. This again is difficult to understand. It would suggest there are either year on year increases in inherent transmissibility of the virus through fitness changes, or year on year increases in the mixing of the population. It would be useful for the authors to discuss potential explanations for an inferred gradual increase in R0.

On a similar note, I struggle to reconcile evidence of a stable or even small drop in FoI in the 1:64 models 4 and 5 from 2010/11 (Figure 3) with steadily increasing R0 in this period (Figure 4). Is this due to changes in the susceptibility proportion. It would be good to understand if there are important assumptions in the Farrington approach that may also contribute to this discrepancy.

The R0 estimates (Figure 4) should also be presented with uncertainty.

Finally, given the substantial uncertainty in the assay, it seems optimistic to attempt to fit annual force of infections in the 30 year period prior to the start of the sampling periods. I would be tempted to include a constant lambda prior to the dates of the first study across the models considered.

Reviewer #1 (Public Review):

In this paper, the authors developed a method that allows one to test a large number of drug combinations in a single cell culture sample. In principle, the experiments rely on the randomness of drug uptake in individual cells as a tool to create and encode drug treatments. They used a single sample containing thousands of cells treated with a combination of fluorescent barcoded drugs, and created transient drug gradients. They also developed segmentation- free image analysis capable of handling optical fields with a substantial number of cells. The major strength of this work is the demonstration of the feasibility of testing drug combinations in a relatively straightforward manner that could be used by many laboratories. As such this paper could have a significant impact on the early drug discovery of combinatorial therapy. One of the weaknesses in this manuscript is the absence of studies beyond just HeLa cells. In addition, the phenotype tested is cell death, which might limit the application to other drug interactions that might look at other phenotypes; e.g inhibition of cell proliferation or changes in differentiation phenotypes. Finally, there is a basic assumption that drug leakage does not occur or is minimal, but secondary uptake of the drug is likely and may not be homogeneous. Notwithstanding, the approach is feasible and likely will be applied in several laboratories.

Reviewer #2 (Public Review):

This manuscript explores a novel technique to use dyes co-injected with various pharmaceutical reagents, like chemotherapic agents, to assess cellular effects in a cell culture model.

The major premise is that dye diffusion can be detected through fluorescent microscopy and be used as a measure of co-injected drug concentration. In chemotherapy commonly multiple drugs are given simultaneously, however, understanding how to tailor the concentrations of a multi-drug cocktail to each individual is largely trial and error. The authors surmise that perhaps using a cell culture model whereby cancer cells are cultured and then exposed to dye-tracked molecules an optimal multi-drug combination and concentrations can be determined. In other words, the intermixing of various connected drugs can then be fluorescently monitored to elucidate optimal concentrations of multi-drug combinations.

The concept overall is interesting but is relatively preliminary in its proof of concept. The authors note that varying free-diffusion of drugs out of the cell could complicate interpretation and that most of the analysis was done on a relatively short time basis and not longer evaluation periods that were more typical of chemotherapy.

Reviewer #3 (Public Review):

The ability to rapidly test a large combination of drug cocktails on patient cells in culture would enhance personalized therapeutic regimens. Currently, testing 10 concentrations of 3 drugs in combination is intractable. Elgart & Loscalzo propose to take advantage of diverse drug responses within a single dish to streamline the exploration of multi-drug combinations. By sampling the population variation in uptake of multiple dyes within individual cells and delivering the dyes by a variety of modes (i.e. point injection, sequential homogenous mixing), a pipeline is developed for estimating a "response space" that arises from the complex intersections of multiple drug/dye concentration gradients.

The paper is in places very rigorous in establishing bounds in which this pipeline may have utility by defining the linearity of two-drug co-delivery, explicitly illustrating the pre-processing/binning performed on the data, reporting distributions of uptake under different environmental dye gradients, and finding a tight correlation between dye and drug response to justify the surrogate use of dye characterization for the end-goal of drug cocktail formulation. I am particularly impressed with the results depicted in Figure 6 and the associated supplemental figures as a demonstration of an application of this approach for nanocarrier-based combinatorial siRNA delivery. However, there are major weaknesses in interpretability and underlying assumptions.

A large body of work in the literature has established that the diversity in cells of identical genetic background occurs due to two components: 1) intrinsic noise - such as stochastic fluctuations in gene expression - as well as 2) extrinsic noise - variability that arises from sources that are external to the biochemical process of gene expression, such as abundances of ribosomes or stage in the cell cycle. Note that this widely-accepted definition does not separate intrinsic and extrinsic from intracellular and extracellular. The authors cite a few of these seminal papers (which focus on noise introduced to gene expression) but then define their interpretation of intrinsic noise much more broadly "... intrinsic noise as phenotype(s) fluctuations across isogenic cell populations cultured under the same conditions. Measurement noise in some cases can also be thought of as intrinsic noise. Fluctuations in cellular phenotype(s) driven by the global environment will be referred to as extrinsic noise." This misuse of widely accepted terminology creates significant confusion in the interpretation of the results.

A point of contention with redefining noise as the authors have done is that they are lumping all processes unique to the cell as intrinsic and all environmental factors as extrinsic. Thus, when statements are made such as "external factors that contribute to noise are principally manifest through convection" (line 40-41, page 2) the veracity of these assumptions must be established. For example, when a ligand binds and unbinds from a receptor due to thermal energy, that "noise" in cellular stimulation is not convection-based, yet an example of how extrinsic noise can influence cellular responses. The definition is important because the underlying premise for the pipeline presented is that "While intrinsic cell variability can be significant, we believe that it is the extrinsic factor(s) that drive sample variability in most experimental cellular systems" (lines 42-43, page 4).

Throughout, figures lack labels and sufficient explanation for interpretation, as well as the number of experiments used to generate the data that is processed through the pipeline for each condition. For a study designed to eliminate replicate culture conditions, the onus is on the authors to show that replicates are in fact fully recapitulated in the population variance after statistical binning/processing.

Ultimately, when the paper presents results such as Figure 9 as the culmination of the pipeline as applied to cell viability studies, it is unclear how useful insight is extracted from this methodology. Four drugs are applied in combination to adherent HeLa cells and time-dependent local cell density is provided as a proxy for cell viability. While it is stated that "The absolute drug concentration can be determined using the homogeneous delivery method discussed above" (line 421-422, page 19), this analysis is not performed, and I am left unsure of whether extrinsic factors are truly driving sample variability under this context. It is unclear to the reader how the point injections were administered, and no discussion of how the confounding factors of synergy or antagonism will be addressed through this methodology.

Reviewer #1 (Public Review):

In this manuscript, Nocka and colleagues reveal a novel layer of regulation of the Btk tyrosine kinase, a key signaling protein in B lymphocyte signaling and an important drug target with 3 recently FDA-approved drugs, by the SH3-SH2 domain-containing adaptor protein Grb2. The authors nicely demonstrate a critical role of the interaction of the Grb2 SH3 domains with the Pro-rich linker C-terminal to the Btk PH-TH domains on membranes for full kinase activation of Btk. Hence this interaction recruits Btk to scaffold-mediated signaling clusters.

This is a technically sound paper with high-quality experiments. The manuscript is easy to follow and excellently written. The findings are novel and of high relevance towards a complete understanding of Btk regulation and signaling in cancer and normal cells.

Reviewer #2 (Public Review):

The authors unexpectedly found that the protein Grb2, an adaptor protein that mediates the recruitment of the Ras guanine-nucleotide exchange factor, SOS, to the EGF receptor, can be recruited to membranes by the immune cell tyrosine kinase Btk. The authors show, using total internal reflection fluorescence (TIRF) microscopy that the interaction with Grb2 is reversible, dependent on the proline-rich region of Btk, and independent of PIP3. These experiments are well performed and unambiguous.

The authors next asked whether Grb2 binding to Btk influences its kinase activity, by evaluating (i) Btk autophosphorylation and (ii) the phosphorylation of a peptide from the endogenous substrate PLC1. The readout relies on non-specific antibody-mediated detection of phosphotyrosine but nevertheless reveals a concentration-dependent increase in both Btk autophosphorylation and PLCy1 phosphorylation. The experiments, however, have only been performed in duplicate and, particularly in the case of PLCy1 phosphorylation, exhibit enormous variability which is not reflected in the example blot the authors have chosen to display in Figure 3C. Comparison of the same, duplicate experiment presented in Figure 3 Supplement 2 paints a very different picture.

The authors next sought to determine which domains of Grb2 are required for activation of Btk. Again, these experiments were only performed in duplicates, and the authors' claims that Grb2 can moderately stimulate the SH3-SH2-kinase module of Grb2 are not well supported by their data (Figure 4C-D).

The authors next asked whether Grb2 stimulates Btk by promoting its dimerization and trans-autophosphorylation. The authors measured the diffusion coefficient of Btk on PIP3-containing supported lipid bilayers in the presence and absence of Grb2. They noted that the diffusion coefficient of individual Btk particles decreases with increasing unlabeled Btk, which they interpret as Btk dimerization. Grb2 does not appear to influence the diffusion of Btk on the membrane (Figure 5A). Presumably, the diffusion coefficient reported here is the average of a number of single-molecule tracks, which should result in error bars. It is unclear why these have not been reported. Next, the authors assessed the ability of Grb2 to stimulate a mutant of Btk that is impaired in its ability to dimerize on PIP3-containing membranes. In contrast to wild-type Btk, autophosphorylation of dimerization-deficient Btk is not enhanced by Grb2. Whilst the data are consistent with this conclusion, again, the experiment has only been repeated once and the western blot presented in Figure 5 Supplement 2 is unreadable. It is also puzzling why Grb2 gets phosphorylated in this experiment, but not in the same experiment reported in Figure 3 Supplement 2.

Finally, the authors argue that Grb2 facilitates the recruitment of Btk to molecular condensates of adaptor and scaffold proteins immobilized on a supported lipid bilayer (SLB) (Figure 6). This is a highly complex series of experiments in which various components are added to supported lipid bilayers and the diffusion of labelled Btk is measured. When Btk is added to SLBs containing the LAT adaptor protein (phosphorylated in situ by Hck immobilized on the membrane via its His tag), it exhibits similar mobility to LAT alone, and its mobility is decreased by the addition of Grb2. The addition of the proline-rich region (PRR) of SOS further decreases this mobility. In this final condition, the authors incubate the reactions for 1 h until LAT undergoes a phase transition, forming gel-like, protein-rich domains on the membrane, shown in Figure 6B. The authors' conclusion that Btk is recruited into these phase-separated domains based on a slow-down in its diffusion is not well supported by the data, which rather indicates that Btk is excluded from these domains (Figure 6B - Btk punctae (green) are almost exclusively found in between the LAT condensates (red)). As such, the restricted mobility of Btk that the authors report may simply reflect the influence of barriers to diffusion on the membrane that result from LAT condensation into phase-separated domains. The authors also present data in Figure 6 Supplement 1 indicating that Grb2 recruitment to Btk is out-competed by SOS-PRR and that Btk does not support the co-recruitment of Grb2 and SOS-PRR to the membrane. These data would appear to suggest that the authors' interpretation of the decreased mobility of Btk on the membrane may not be correct.

Reviewer #3 (Public Review):

The study of Nocka and colleagues examines the role of membrane scaffolding in Btk kinase activation by the Grb2 adaptor protein. The studies appear to make a case for a reinterpretation of the "Saraste dimer" of Btk as a signaling entity and assigns roles to the component domains in the Src module in Btk activation. The point of distinction from earlier studies is that this work ascribes a function to an adaptor protein as promoting the kinase activation, rather than vice versa, and also illustrates why Btk can be activated via modes distinct from its close relative, such as Itk. Importantly, these studies address these key questions through membrane tethering of Btk, which is a successful, reductionist way to mimic cellular scenarios. The writing could be improved and can absolutely be more economical in word choice and use; currently, there is a good deal of background to each section that is not always comprehensive or crucial to contextualise the findings, while key information is often omitted. The results are currently not described in a detailed manner so there is an imbalance between the findings, which should be the focus, relative to background and interpretations or models.

Reviewer #1 (Public Review):

The study by Oikawa and colleagues demonstrates for the first time that a descending inhibitory pathway for nociception exists in non-mammalian organisms, such as Drosophila. This descending inhibitory pathway is mediated by a Drosophila neuropeptide called Drosulfakinin (DSK), which is homologous to mammalian cholecystokinin (CCK). The study creates and uses several Drosophila mutants to convincingly show that DSK negatively regulates nociception. They then use several sophisticated transgenic manipulations to demonstrate that a descending inhibitory pathway for nociception exists in Drosophila.

Strengths:

This study creates the possibility of using Drosophila to study descending nociceptive systems.

CRISPR/Cas9 is used to generate mutants of dsk, CCKLR-17D1, and CCKLR-17D3. The authors then use these mutants to clearly show that DSK negatively regulates nociception.

Several GAL4s are used to clearly show that these effects are likely mediated by two sets of neurons in the brain, MP1 and Sv.

RNAi and rescue experiments further show that CCKLR-17D1, a DSK receptor, functions in Goro neurons to negatively regulate nociception.

Thermogenetic experiments nicely show that activation of DSK neurons attenuates the nociceptive response.

Weaknesses:

A minor weakness in the study is that it is unclear how DSK negatively regulates nociception. An earlier study at the Drosophila nmj shows that loss of DSK signaling impairs neurotransmission and synaptic growth. In the current study, loss of CCKLR-17D1 in Goro neurons seems to increase intracellular calcium levels in the presence of noxious heat. An interesting future study would be the examination of the underlying mechanisms for this increase in intracellular calcium.

Reviewer #2 (Public Review):

This is an exceptional study that provides conclusive evidence for the existence of a descending pathway from the brain that inhibits nociceptive behavioral outputs in larvae of Drosophila melanogaster. The authors identify molecular both molecular and neuronal/cellular components of this pathway. Converging lines of evidence and conclusive genetic experiments indicate that the neuropeptide, drosulfakinin (DSK), and its receptors (CCK1 and CCK2) function to inhibit nociception behaviors. Interestingly, the authors show that the relevant DSK neurons have cell bodies that are in the larval brain and that these neurons send projections into the thoracic ganglion and ventral nerve cord. Several lines of evidence support the hypothesis that fourth-order nociceptive neurons called Goro, are one relevant target for these outputs. RNAi knockdown of the CCK1 receptor in these cells sensitizes behavioral and physiological responses to noxious heat. Second, the axons of DSK neurons form physical contact with processes of Goro neurons as revealed by GRASP analysis. However, the authors' careful experiments indicate that the contacts between axons and Goro neurites might not be indicative of direct synapses and instead might operate through the bulk transmission of the peptidergic signals. The study raises many interesting questions for future study such as what behavioral contexts might depend on this pathway. Using the CAMPARI approach, the authors do not find that the DSK neurons are activated in response to nociceptive input but instead suggest that these cells may be tonically active in gating nociception. Future studies may find contexts in which the output of the DSK neurons is inhibited to facilitate nociception, or contexts in which the cells are more active to inhibit nociception.

Reviewer #3 (Public Review):

This study describes a descending circuit that can modulate pain perception in the drosophila larvae. While descending inhibition is a major component of mammalian pain perception, it is not known if a similar circuit design exists in fruit flies. Overall the authors use clean logic to establish a role for DSK and its receptor in regulating nociception. I have made a few suggestions that I believe would strengthen the manuscript as this is an important discovery.

Major comments:

1) It's not completely clear why the authors are staining animals with an FLRFa antibody. Can the authors stain WT and DSK KO animals with a DSK antibody? Also, can the authors show in supplemental what antigen the FLRFa antibody was raised against, and what part of that peptide sequence is retained in the DSK sequence? This overall seems like a weakness in the study that could be improved on in some way by using DSK-specific tools.

2) What is the phenotype of DSK-Gal4 x UAS-TET animals? They should be hyper-reactive. If it's lethal maybe try an inducible approach.

3) Figure 9. This was not totally clear, but I think the authors were evaluating spontaneous (i.e. TRPA1-driven) rolling at 35C. The critical question is "does activating DSK-expressing neurons suppress acute heat nociception" and this hasn't really been addressed. The inclusion of PPK Gal4 + DSK Gal4 in the same animal kind of clouds the overall conclusions the reader can draw. The essential experiment is to express UAS-dTRPA1 in DSK-Gal4 or GORO-Gal4 cells, heat the animals to ~29C, and then test latency to a thermal heat probe (over a range of sub and noxious temperatures). Basically prove the model in Figure 10 showing ectopic activation or inhibition for each major step, then test heat probe responses.

4) It would also then be interesting to see how strong the descending inhibition circuit is in the context of UV burn. If this is a real descending circuit, it should presumably be able to override sensitization after injury.

Reviewer #1 (Public Review):

Chan et al. tried identifying the binding sites or pockets for the KCNQ1-KCNE1 activator mefenamic acid. Because the KCNQ1-KCNE1 channel is responsible for cardiac repolarization, genetic impairment of either the KCNQ1 or KCNE1 gene can cause cardiac arrhythmia. Therefore, the development of activators without side effects is highly demanded. Because the binding of mefenamic acid requires both KCNQ1 and KCNE1 subunits, the authors performed drug docking simulation by using KCNQ1-KCNE3 structural model (because this is the only available KCNQ1-KCNE structure) with substitution of the extracellular five amino acids (R53-Y58) into D39-A44 of KCNE1. That could be a limitation of the work because the binding mode of KCNE1 might differ from that of KCNE3. Still, they successfully identified some critical amino acid residues, including W323 of KCNQ1 and K41 and A44 of KCNE1. They subsequently tested these identified amino acid residues by analyzing the point mutants and confirmed that they attenuated the effects of the activator. They also examined another activator, yet structurally different DIDS, and reported that DIDS and mefenamic acid share the binding pocket, and they concluded that the extracellular region composed of S1, S6, and KCNE1 is a generic binding pocket for the IKS activators.

The data are solid and well support their conclusions, although there are a few concerns regarding the choice of mutants for analysis and data presentation.

Other comments:

1. One of the limitations of this work is that they used psKCNE1 (mostly KCNE3), not real KCNE1, as written above. It is also noted that KCNQ1-KCNE3 is in the open state. Unbinding may be facilitated in the closed state, although evaluating that in the current work is difficult.<br /> 2. According to Figure 2-figure supplement 2, some amino acid residues (S298 and A300) of the turret might be involved in the binding of mefenamic acid. On the other hand, Q147 showing a comparable delta G value to S298 and A300 was picked for mutant analysis. What are the criteria for the following electrophysiological study?<br /> 3. It is an interesting speculation that K41C and W323A stabilize the extracellular region of KCNE1 and might increase the binding efficacy of mefenamic acid. Is it also the case for DIDS? K41 may not be critical for DIDS, however.<br /> 4. Same to #2, why was the pore turret (S298-A300) not examined in Figure 7?

Reviewer #2 (Public Review):

The voltage-gated potassium channel KCNQ1/KCNE1 (IKs) plays important physiological functions, for instance in the repolarization phase of the cardiac action potential. Loss-of-function of KCNQ1/KCNE1 is linked to disease. Hence, KCNQ1/KCNE1 is a highlighted pharmacological target and mechanistic insights into how channel modulators enhance the function of the channel is of great interest. The authors have through several previous studies provided mechanistic insights into how small-molecule activators like ML277 act on KCNQ1. However, less is known about the binding site and mechanism of action of other type of channel activators, which require KCNE1 for their effect. In this study, Chan and co-workers use molecular dynamics approaches, mutagenesis and electrophysiology to propose an overall similar binding site for the KCNQ1/KCNE1 activators mefenamic acid and DIDS, located at the extracellular interface of KCNQ1 and KCNE1. The authors propose an induced-fit model for the binding site, which critically engages residues in the N-terminus of KCNE1. Moreover, the authors discuss possible mechanisms of action of how drug binding to this site may enhance channel function.

The authors address an important question, of broad relevance to researchers in the field. The manuscript is generally well written and the text easy to follow. A strength of the work is the parallel use of experimental and simulation approaches, which enables both functional testing and mechanistic predictions and interpretations. For instance, the authors have experimentally assessed the putative relevance of a large set of residues based on simulation predictions. A limitation is that several methods need to be described in more detail to allow for evaluation of the presented data. Also, a more extensive presentation of representative data would be useful, along with discussions on the putative impact on drug effects of the diverse intrinsic properties of tested mutants.

Reviewer #3 (Public Review):

The author is trying to identify the mefenamic (Mef) binding site and DIDS binding site on the KCNQ1 KCNE1 complex. The authors also try to identify the mechanism of interactions using electrophysiological recording, calculating V1/2 of different mutants, and looking at the instantaneous current and the tail current. The contribution of each residue within the binding pocket was analysed using GBSA and PBSA and traditional molecular dynamics simulation. The author is trying to argue that they share the same binding pocket and their mechanism of activation.

Strengths:

1. The effect of the WT channel in the presence of 100 uM Mef is very clear, and such an effect is clearly decreased with the E1-K41C and W323A mutation. The milder effect was observed with Q147C and Y148C mutants.

2. The effect of the WT channel in the presence of 100 uM DIDS is, again, very clear, and such an effect is clearly decreased with the E1-Y46C.

3. The author has indeed achieved their aim in addressing that the binding site for both DIDS and Mef are adjacent to each other and may indeed share a pocket in the S1-E1-pore pocket. This may help the field with drug development, targeting that region in the future.

Weaknesses:

1. The computational aspect of the work is rather under-sampled - Figure 2 and Figure 4. The lack of quantitative analysis on the molecular dynamic simulation studies is striking, as only a video of a single representative replica is being shown per mutant/drug. Given that the simulations shown in the video are extremely short; some video only lasts up to 80 ns. Could the author provide longer simulations in each simulation condition (at least to 500 ns or until a stable binding pose is obtained in case the ligand does not leave the binding site), at least with three replicates per each condition? If not able to extend the length of the simulations due to resources issue, then further quantitative analysis should be conducted to prove that all simulations are converged and are sufficient. Please see the rest of the quantitative analysis in other comments.

2. Given that the protein is a tetramer, at least 12 datasets could have been curated to improve the statistic. It was also unclear how frequently the frames from the simulations were taken in order to calculate the PBSA/GBSA.

3. The lack of labels on several structures is rather unhelpful (Figure 2B, 2C, 4B). The lack of clarity of the interaction map in Figures 2D and 6A.

4. The RMSF analysis is rather unclear and unlabelled thoroughly. In fact, I still don't quite understand why n = 3, given that the protein is a tetramer. If only one out of four were docked and studied, this rationale needs to be explained and accounted for in the manuscript.

5. For the condition that the ligands suppose to leave the site (K42C for Mef and Y46A for DIDS), can you please provide simulations at a sufficient length of time to show that ligand left the site over three replicates? Given that the protein is a tetramer, I would be expecting three replicates of data to have four data points from each subunit. I would be expecting distance calculation or RMSD of the ligand position in the binding site to be calculated either as a time series or as a distribution plot to show the difference between each mutant in the ligand stability within the binding pocket. I would expect all the videos to be translatable to certain quantitative measures.

6. Given that K41 (Mef) and Y46 are very important in the coordination, could you calculate the frequency at which such residues form hydrogen bonds with the drug in the binding site? Can you also calculate the occupancy or the frequency of contact that the residues are making to the ligand (close 4-angstrom proximity etc.) and show whether those agree with the ligand interaction map obtained from ICM pro in Figure 2D?

7. Given that the author claims that both molecules share the same binding site and the mode of ligand binding seems to be very dynamic, I would expect the authors to show the distribution of the position of ligand, or space, or volume occupied by the ligand throughout multiple repeats of simulations, over sufficient sampling time that both ligand samples the same conformational space in the binding pocket. This will prove the point in the discussion - Line 463-464. "We can imagine a dynamic complex... bind/unbind from Its at a high frequency".

8. I would expect the authors to explain the significance and the importance of the PBSA/GBSA analysis as they are not reporting the same energy in several cases, especially K41 in Figure 2 - figure supplement 2. It was also questionable that Y46, which seems to have high binding energy, show no difference in the EPhys works in figure 3. These need to be commented on.

9. Can the author prove that the PBSA/GBSA analysis yielded the same average free energy throughout the MD simulation? This should be the case when the simulations are converged. The author may takes the snapshots from the first ten ns, conduct the analysis and take the average, then 50, then 100, then 250 and 500 ns. The author then hopefully expects that as the simulations get longer, the system has reached equilibrium, and the free energy obtained per residue corresponds to the ensemble average.

10. The phrase "Lowest interaction free energy fort residues in ps-KCNE1 and selected KCNQ1 domains are shown as enlarged panels (n=3 for each point)" needs further explanation. Is this from different frames? I would rather see this PBSA and GBSA calculated on every frame of the simulations, maybe at the one ns increment across 500 ns simulations, in 4 binding sites, in 3 replicas, and these are being plotted as the distribution instead of plotting the smallest number. Can you show each data point corresponding to n = 3?

11. I cannot wrap my head around what you are trying to show in Figure 2B. This could be genuinely improved with better labelling. Can you explain whether this predicted binding pose for Mef in the figure is taken from the docking or from the last frame of the simulation? Given that the binding mode seems to be quite dynamic, a single snapshot might not be very helpful. I suggest a figure describing different modes of binding. Figure 2B should be combined with figure 2C as both are not very informative.

12. Similar to the comment above, but for figure 4B. I do not understand the argument. If the author is trying to say that the pocket is closed after Mef is removed - then can you show, using MD simulation, that the pocket is openable in an apo to the state where Mef can bind? I am aware that the open pocket is generated through batches of structures through conformational sampling - but as the region is supposed to be disordered, can you show that there is a possibility of the allosteric or cryptic pocket being opened in the simulations? If not, can you show that the structure with the open pocket, when the ligand is removed, is capable of collapsing down to the structure similar to the cryo-EM structure? If none of the above work, the author might consider using PocketMiner tools to find an allosteric pocket (https://doi.org/10.1038/s41467-023-36699-3) and see a possibility that the pocket exists.

13. Figure 4C - again, can you show the RMSF analysis of all four subunits leading to 12 data points? If it is too messy to plot, can you plot a mean with a standard deviation? I would say that a 1-1.5 angstroms increase in the RMSF is not a "markedly increased", as stated on line 280. I would also encourage the authors to label whether the RMSF is calculated from the backbone, side-chain or C-alpha atoms and, ideally, compare them to see where the dynamical properties are coming from.

14. In the discussion - Lines 464-467. "Slowed deactivation of the S1/KCNE1/Pore domain/drug complex ....... By stabilising the activated complex. MD simulation suggests the latter is most likely the case." Can you point out explicitly where this has been proven? If the drug really stabilised the activated complex, can you show which intermolecular interaction within E1/S1/Pore has the drug broken and re-form to strengthen the complex formation? The authors have not disproven the point on steric hindrance either. Can this be disproved by further quantitative analysis of existing unbiased equilibrium simulations?

15. Figure 4D - Can you show this RMSF analysis for all mutants you conducted in this study, such as Y46C? Can you explain the difference in F dynamics in the KCNE3 for both Figure 4C and 4D?

16. Line 477: the author suggested that K41 and Mef may stabilise the protein-protein interface at the external region of the channel complex. Can you prove that through the change in protein-protein interaction, contact is made over time on the existing MD trajectories, whether they are broken or formed? The interface from which residues help to form and stabilise the contact? If this is just a hypothesis for future study, then this has to be stated clearly.

17. The author stated on lines 305-307 that "DIDS is stabilised by its hydrophobic and vdW contacts with KCNQ1 and KCNE1 subunits as well as by two hydrogen bonds formed between the drug and ps-KCNE1 residue L42 and KCNQ1 residue Q147" Can you show, using H-bond analysis that these two hydrogen bonds really exist stably in the simulations? Can you show, using minimum distance analysis, that L42 are in the vdW radii stably and are making close contact throughout the simulations?

18. Discussion - In line 417, the author stated that the "S1 appears to pull away from the pore" and supplemented the claim with the movie. This is insufficient. The author should demonstrate distance calculation between the S1 helix and the pore, in WT and mutants, with and without the drug. This could be shown as a time series or distribution of centre-of-mass distance over time.

19. Given that all the work were done in the open state channel with PIP2 bound (PDB entry: 6v01), could the author demonstrate, either using docking, or simulations, or alignment, or space-filling models - that the ligand, both DIDS and Mef, would not be able to fit in the binding site of a closed state channel (PDB entry: 6v00). This would help illustrate the point denoted Lines 464-467. "Slowed deactivation of the S1/KCNE1/Pore domain/drug complex... By stabilising the activated complex. MD simulation suggests the latter is most likely the case."

20. I struggle with the term "normalised response" on Line 208. What is it being normalised to? Can this be put more explicitly in the text? If normalised to WT, why is WT EQ response only 0.8?

21. The author stated that the binding pose changed in one run (lines 317 to 318). Can you comment on those changes? If the pose has changed - what has it changed to? Can you run longer simulations to see if it can reverse back to the initial confirmation? Or will it leave the site completely?

22. Binding free energy of -32 kcal/mol = -134 kJ/mol. If you try to do dG = -RTlnKd, your lnKd is -52. Your Kd is e^-52, which means it will never unbind if it exists. I am aware that this is the caveat with the methodologies. But maybe these should be highlighted throughout the manuscript.

Reviewer #1 (Public Review):

This is a valuable study demonstrating convincingly that PI3K signaling lies downstream of Pdgfra signaling in zebrafish cardiomyocyte progenitors as they undergo latero-medial migration and midline fusion, essential for heart tube formation, likely via chemotaxis. Whereas the authors used both multiple inhibitory drugs and dominant negative transgene expression to interrupt PI3K expression, with findings strongly aligning, the manuscript would have been stronger if genetic approaches were used to complement the above approaches. Nonetheless, the impact of dnPI3K inhibition allowed the authors to suggest that the effects were cell autonomous to migrating cardiomyocytes. The authors used contemporary live imaging techniques allowing quantification of key cell behaviors, and this is a strength of the paper. There are some issues about the inter-study alignment of trajectory data that need to be addressed. Perhaps the most conspicuous weakness is that the authors have not advanced the model for cardiomyocyte migration beyond adding the involvement of PI3K downstream of Pdgfra, which is to a significant degree expected. The recording of cardiomyocyte protrusions biased in their orientation towards the direction of migration, which is lost in the mutants, is an interesting advance, although it was not shown whether protrusions are causally related to migration.

Reviewer #2 (Public Review):

The authors provide comprehensive results showing that pharmacological inhibition of PI3K negatively affects heart tube formation via misoriented and slower cardiac movements. They used several cellular and molecular assays to demonstrate the potential mechanisms involved in PI3K-dependent cardiac fusion defects. Moreover, they use several imaging techniques and quantitative assessments to support their findings. Although the manuscript is well-written and most of their results support their conclusions, the manuscript and its findings heavily rely on high concentrations of PI3K small-molecule inhibitors, which will have off-target effects. The off-targets of PI3K pharmacological inhibition should be interpreted with caution and further evaluated. The authors suggest PI3K inhibition mediates heart tube formation throughout PI3K-mediated migration defects rather than PI3K-mediated proliferative defects. However, the authors did not further evaluate this later point; it should be considered carefully.

Reviewer #3 (Public Review):

This manuscript provides new insights into an important process during cardiac development that is not well understood. The authors combined chemical inhibition experiments for PI3K as well as a genetic tool to overexpress a dominant negative PI3K specifically in cardiac progenitor cells and found that PI3K is important during cardiac fusion. By incubating embryos with the chemical inhibitor at different stages they concluded that PI3K is required between 12-20 somite stages, which corresponds to the time points that cardiac fusion occurs. They performed live imaging on cardiac progenitors during cardiac fusion and observed that inhibiting Pi3K reduces the velocity at which the cells move and affects their direction. The latter seems consistent with the observation that PI3K is not required for protrusion formation but affects the location of these protrusions. Finally, using a low dose of the PI3K inhibitor together with the previously identified Pdgf mutant suggests that both act in the same pathway to regulate the direction of migration of cardiac progenitor cels towards the midline. Overall, the manuscript is well written and experiments are well controlled providing sufficient evidence to substantiate most of their conclusions. Some open questions remain unanswered such as the mode of migration (individual or collective) that drives cardiac fusion.

Reviewer #1 (Public Review):

This manuscript addresses the important and understudied issue of circuit-level mechanisms supporting habituation, particularly in pursuit of the possible role of increases in the activity of inhibitory neurons in suppressing behavioral output during long-term habituation. The authors make use of many of the striking advantages of the larval zebrafish to perform whole brain, single neuronal calcium imaging during repeated sensory exposure, and high throughput screening of pharmacological agents in freely moving, habituating larvae. Notably, several blockers/antagonists of GABAA(C) receptors completely suppress habituation of the O-bend escape response to dark flashes, suggesting a key role for GABAergic transmission in this form of habituation. Other substances are identified that strikingly enhance habituation, including melatonin, although here the suggested mechanistic insight is less specific. To add to these findings, a number of functional clusters of neurons are identified in the larval brain that has divergent activity through habituation, with many clusters exhibiting suppression of different degrees, in line with adaptive filtration during habituation, and a single cluster that potentiates during habituation. Further assessment reveals that all of these clusters include GABAergic inhibitory neurons and excitatory neurons, so we cannot take away the simple interpretation that the potentiating cluster of neurons is inhibitory and therefore exerts an influence on the other adapting (depressing) clusters to produce habituation. Rather, a variety of interpretations remain in play.

Overall, there is great potential in the approach that has been used here to gain insight into circuit-level mechanisms of habituation. There are many experiments performed by the authors that cannot be achieved currently in other vertebrate systems, so the manuscript serves as a potential methodological platform that can be used to support a rich array of future work. While there are several key observations that one can take away from this manuscript, a clear interpretation of the role of GABAergic inhibitory neurons in habituation has not been established. This potential feature of habituation is emphasized throughout, particularly in the introduction and discussion sections, meaning that one is obliged as a reader to interrogate whether the results as they currently stand really do demonstrate a role for GABAergic inhibition in habituation. Currently, the key piece of evidence that may support this conclusion is that picrotoxin, which acts to block some classes of GABA receptors, prevents habituation. However, there are interpretations of this finding that do not specifically require a role for modified GABAergic inhibition. For instance, by lowering GABAergic inhibition, an overall increase in neural activity will occur within the brain, in this case below a level that could cause a seizure. That increase in activity may simply prevent learning by massively increasing neural noise and therefore either preventing synaptic plasticity or, more likely, causing indiscriminate synaptic strengthening and weakening that occludes information storage. Sensory processing itself could also be disrupted, for instance by altering the selectivity of receptive fields. Alternatively, it could be that the increase in neural activity produced by the blockade of inhibition simply drives more behavioral output, meaning that more excitatory synaptic adaptation is required to suppress that output. The authors propose two specific working models of the ways in which GABAergic inhibition could be implemented in habituation. An alternative model, in which GABAergic neurons are not themselves modified but act as a key intermediary between Hebbian assemblies of excitatory neurons that are modified to support memory and output neurons, is not explored. As yet, these or other models in which inhibition is not required for habituation, have not been fully tested.

This manuscript describes a really substantial body of work that provides evidence of functional clusters of neurons with divergent responses to repeated sensory input and an array of pharmacological agents that can influence the rate of a fundamentally important form of learning.

Reviewer #2 (Public Review):

In this study, Lamire et al. use a calcium imaging approach, behavioural tests, and pharmacological manipulations to identify the molecular mechanisms behind visual habituation. Overall, the manuscript is well-written but difficult to follow at times. They show a valuable new drug screen paradigm to assess the impact of pharmacological compounds on the behaviour of larval zebrafish, the results are convincing, but the description of the work is sometimes confusing and lacking details.

The volumetric calcium imaging of habituation to dark flashes is valuable, but the mix of responses to visual cues that are not relevant to the dark flash escape, such as the slow increase back to baseline luminosity, lowers the clarity of the results. The link between the calcium imaging results and free-swimming behaviour is not especially convincing, however, that is a common issue of head-restrained imaging with larval zebrafish.

The strong focus on GABA seems unwarranted based on the pharmacological results, as only Picrotoxinin gives clear results, but the other antagonists do not give a consistent results. On the other hand, the melatonin receptor agonists, and oestrogen receptor agonists give more consistent results, including more convincing dose effects.

The pharmacological manipulation of the habituation circuits mapped in the first part does not arrive at any satisfying conclusion, which is acknowledged by the authors. These results do reinforce the disconnect between the calcium imaging and the behavioural experiments and undercut somewhat the proposed circuit-level model.

Overall, the authors did identify interesting new molecular pathways that may be involved in habituation to dark flashes. Their screening approach, while not novel, will be a powerful way to interrogate other behavioural profiles. The authors identified circuit loci apparently involved in habituation to dark flashes, and the potentiation and no adaptation clusters have not been previously observed as far as I know.

The data will be useful to guide follow-up experiments by the community on the new pathway candidates that this screen has uncovered, including behaviours beyond dark flash habituation.

Reviewer #3 (Public Review):

To analyze the circuit mechanisms leading to the habituation of the O-bed responses upon repeated dark flashes (DFs), the authors performed 2-photon Ca2+ imaging in larvae expressing nuclear-targeted GCaMP7f pan-neuronally panning the majority of the midbrain, hindbrain, pretectum, and thalamus. They found that while the majority of neurons across the brain depress their responsiveness during habituation, a smaller population of neurons in the dorsal regions of the brain, including the torus longitudinalis, cerebellum, and dorsal hindbrain, showed the opposite pattern, suggesting that motor-related brain regions contain non-depressed signals, and therefore likely contribute to habituation plasticity.

Further analysis using affinity propagation clustering identified 12 clusters that differed both in their adaptation to repeated DFs, as well as the shape of their response to the DF.

Next by the pharmacological screening of 1953 small molecule compounds with known targets in conjunction with the high-throughput assay, they found that 176 compounds significantly altered some aspects of measured behavior. Among them, they sought to identify the compounds that 1) have minimal effects on the naive response to DFs, but strong effects during the training and/or memory retention periods, 2) have minimal effects on other aspects of behaviors, 3) show similar behavioral effects to other compounds tested in the same molecular pathway, and identified the GABAA/C Receptor antagonists Bicuculline, Amoxapine, and Picrotoxinin (PTX). As partial antagonism of GABAAR and/or GABACR is sufficient to strongly suppress habituation but not generalized behavioral excitability, they concluded that GABA plays a very prominent role in habituation. They also identified multiple agonists of both Melatonin and Estrogen receptors, indicating that hormonal signaling may also play a prominent role in habituation response.

To integrate the results of the Ca2+ imaging experiments with the pharmacological screening results, the authors compared the Ca2+ activity patterns after treatment with vehicle, PTX, or Melatonin in the tethered larvae. The behavioral effects of PTX and Melatonin were much smaller compared with the very strong behavioral effects in freely-swimming animals, but the authors assumed that the difference was significant enough to continue further experiments. Based on the hypothesis that Melatonin and GABA cooperate during habituation, they expected PTX and Melatonin to have opposite effects. This was not the case in their results: for example, the size of the 12(Pot, M) neuron population was increased by both PTX and Melatonin, suggesting that pharmacological manipulations that affect habituation behavior manifest in complex functional alterations in the circuit, making capturing these effects by a simple difficult.

Since the 12(𝑃𝑜𝑡, 𝑀) neurons potentiate their responses and thus could act to progressively depress the responses of other neuronal classes, they examined the identity of these neurons with GABA neurons. However, GABAergic neurons in the habituating circuit are not characterized by their Adaptation Profile, suggesting that global manipulations of GABAergic signaling through PTX have complex manifestations in the functional properties of neurons.

Overall, the authors have performed an admirably large amount of work both in whole-brain neural activity imaging and pharmacological screening. However, they are not successful in integrating the results of both experiments into an acceptably consistent interpretation due to the incongruency of the results of different experiments. Although the authors present some models for interpretation, it is not easy for me to believe that this model would help the readers of this journal to deepen the understanding of the mechanisms for habituation in DF responses at the neural circuit level.

This reviewer would rather recommend the authors divide this manuscript into two and publish two papers by adding some more strengthening data for each part such as cellular manipulations, e.g. ablation to prove the critical involvement of 12(Pot, M) neurons in habituation.

Reviewer #1 (Public Review):

Rosas et al studied the mechanism/s that enabled carbapenems resistance of a Klebsiella isolate, FK688, which was isolated from an infected patient. To identify and characterize this mechanism, they used a combination of multiple methods. They started by sequencing the genome of this strain by a combination of short and long read sequencing. They show that Klebsiella FK688 does not encode a carbapenemase, and thus looked for other mechanisms that can explain this resistance. They discover that both DHA-1 (located on the mega-plasmid) and an inactivation of the porin OmpK36, are required for carbapenem resistance in this strain. By using experimental evolution, it was shown that resistance is lost rapidly in the absence of antibiotics selection, by a deletion in pNAR1 that removed blaDHA-1. Moreover, their results suggested that it is likely that exposure to other antibiotics selected for the acquisition of the mega-plasmid that carries DHA-1, which then enabled this strain to gain resistance to carbapenemase by a single deletion.

The major strength of this study is the use of various approaches, to tackle an important and interesting problem.

The conclusions of this paper are mostly well supported by data, but one aspect is not clear enough. The description of the evolutionary experiment is not clear. I could not find a clear description of the names of the evolved populations. However, the authors describe strains B3 and A2, but their source is not clear. The legends of the relevant figure (Figure 5) are confusing. For example, the text describing panel B is not related to the image shown in this panel. Moreover, it is shown in panel C (and written in the main text) that the OmpK36+ evolved populations had only translucent colonies, so what is the source of B3(o)?

Reviewer #2 (Public Review):

The authors sequenced a clinical pathogen, Klebsiella FK688, and definitively establish the genetic basis of the carbapenem-resistance phenotype of this strain. They also show that the causal mutations confer reduced fitness under laboratory conditions, and that carbapenem sensitivity readily re-evolves in the lab due to the fitness costs associated with the resistance mutations in the clinical isolate. They also establish that subinhibitory concentrations of ceftazidime select for the otherwise deleterious blaDHA-1 gene. Based on this finding the authors speculate that prior beta-lactam selection faced by the ancestors of Klebsiella FK688 potentiated the evolution of the carbapenem-resistance phenotype of this strain. If this hypothesis is true, then prior history of beta-lactam exposure may generally potentiate the evolution of carbapenem resistance.

Strengths:

From a technical perspective, the findings in this paper are solid. In addition, the authors establish a simple genetic basis for carbapenem resistance in a clinical strain, which is a valuable and non-trivial finding (i.e. they show that the CRE phenotype in this strain is not an omnigenic trait distributed over hundreds of loci).

Weaknesses:

The main weakness of this paper is that the authors draw overly broad conclusions of a conceptual nature from narrow experimental findings. This could be addressed by drawing more modest and narrow implications from the findings.

1) The title of this paper is "Treatment history shapes the evolution of complex carbapenem-resistant phenotypes in Klebsiella spp." But they provide no data on the treatment history of the patient from whom this strain was isolated from. Therefore, the authors have no evidence to support their central claim. Indeed, it is completely possible that this strain never faced beta-lactam selection in the past, or that the patient's hypothetical history of betalactamase was irrelevant for the evolution of FK688. First, it is completely possible that this is a hospital-acquired infection, such that the history of this strain is due to selection in other contexts in the hospital that have little to do with the patient's treatment history. Second, it is completely possible that this strain (the chromosome anyway) has no prior history of beta-lactamase selection, and that it acquired the megaplasmid containing blaDHA-1 via conjugation from some other strain. In this second hypothetical scenario, it is possible that the fitness cost of the blaDHA-1 gene is not particularly high in a different source strain, but that it has some cost in the FK688 strain that it was isolated from. And of course, fitness costs in the human host could be very different than fitness costs in the laboratory, where strains are evolving under strong selection for fast growth. And given the benefit of resistance, it's clear that this strain clearly has a strong fitness advantage over faster-growing sensitive strains in the context of the source patient under antibiotic treatment.

My general point here is that the broad claims made about patient history or prior history shaping the evolution of this strain are largely indefensible because there is no data here to make solid inferences about *how* prior history shaped the evolution of this strain.

2) Historical contingency. The authors claim that their work shows how historical contingency shapes the evolution of resistance. One problem with this claim is that it is trivial- this is only a significant claim if the reader believes that prior history is not important in the evolution of antibiotic resistance, which is a straw-man null hypothesis, to mix a couple metaphors. To be more concrete, clearly strain background (prior history) matters-eliminating the plasmid with the resistance gene eliminates resistance. But that is not particularly surprising, given the past 50 years of evolutionary microbiology literature on plasmids and resistance. By contrast to this work, the major contribution of papers that examine the role of historical contingency in evolution (i.e. various Lenski papers) is that those works *quantitatively* measure the role of history in comparison to other factors (chance, adaptation). Since this work is a deep dive into a single clinical isolate, the data presented here do not and cannot shed light on the role of historical contingency in the emergence of this strain. The authors' claims about the prior history that led to the CRE phenotype are reasonable- but are fundamentally speculative. I have nothing against speculation, as long as it is clear what claims are speculative, and what are concrete implications. But the authors frame these speculative claims as concrete implications of their findings.

3) The authors claim that "[This work] suggests that the strategic combinations of antibiotics could direct the evolution of low-fitness, drug-resistant genotypes". I suppose this is true, but I also think this is a stretch of an implication given these findings. To be blunt, while I suppose it's better to have costly resistance variants that re-evolve sensitivity than to have low-cost high-resistance strains circulating, I think the patient's family would probably disagree that the evolution of a low-fitness drug-resistant genotype was good or strategic in the clinical context, even if better from a public health perspective. Low-fitness drug-resistant strains are just as lethal under clinical antibiotic concentrations!

The authors do show the plausibility of their hypothesis/model that prior beta-lactam selection is sufficient to potentiate the evolution of carbapenem-resistance (by the additional ompK loss-of-function mutation). I think those findings are very nice. But the authors undermine their results by extrapolating too far from their data. Hence, I think narrowing the scope of the implications would improve this paper.

In addition to narrowing the scope of the implications as written, I also would like to add that there may be other ways of framing this paper (other than historical contingency) that may make the significance of this work more apparent to a broader audience. This may be worth considering during the revision process.

Reviewer #1 (Public Review):

The glideosome-associated connector is an essential piece of the machinery used by the apicomplexa parasites as they invade host cells. This GAC makes important interactions with the membrane and with actin during this process. Here, Kumar et al present the first structure of the GAC from T. gondii, showing a complex fold in a closed form. This structure was determined at pH 5, and they show that at more physiological pH values the structure is far more open. However, this is not in the context of actin, membrane, or other binding partners, and so the question remains about how open the structure is in its physiological context. The authors next use molecular dynamics, NMR, and mutagenesis to identify the residues involved in membrane binding and also assess actin binding through modelling which is not validated by experiment. This paper presents an important contribution to our understanding of the molecular machinery involved in host cell invasion but leaves many questions remaining about how this protein links to the cytoskeleton and functions during the invasion process.

• The structure of TgGAC provides the first such structure of this complex and is an important contribution to our understanding. The structure presented in Figure 1A is a composite, containing the crystal structure of the majority of the protein, determined at pH 5, to which has been docked the PH domain structure, determined by NMR. It would be good to see more clarity in the figure about what is experimentally determined and what is modelled.<br /> • SAXS data shows that, at pH 8, a substantial fraction of the protein is in a very extended conformation, which differs significantly from the compact structure seen in crystals at pH 5. I would prefer to see the models in Figure 2d represented as spheres or surfaces, to prevent over-interpretation associated with showing models with low-resolution data. However, the SAXS findings are robust and this is clearly a dynamic molecule in solution. It will be interesting to see what the situation is in the context of binding partners.<br /> • Molecular dynamic simulations next indicate the region which binds to a lipid bilayer, with contact residues forming a consistent interaction surface in three independent simulations. This identified the PH domain and neighbouring residues as the membrane interaction surface.<br /> • Switching to Plasmodium falciparum protein, the authors next use NMR to investigate the binding of the PH domain to membrane nanodiscs, and show that the same protein region identified in the MD simulations was found to bind in the NMR experiments.<br /> • These membrane binding assays were then followed up through liposome pelleting assays, using TgGAP, which showed that the protein only pellets in the presence of PA lipid and that mutation of residues identified through NMR abolished liposome binding. The mutations didn't have the same effect on full-length and PH domains (noting KER for example) suggesting that lipid binding is not entirely mediated by the PH domain in the full-length protein.<br /> • The authors next put the mutants into toxoplasma and assay the effect on apical localisation and on invasion percentage. Interestingly the mutants had little effect, perhaps due to the role of other regions of the GAC on lipid binding, suggesting that abolishing PH domain lipid binding is not sufficient. Unfortunately, as the mutations only partly reduced lipid binding in the context of full-length GAC, as shown in liposome experiments, it is hard to come to a firm conclusion about the importance of lipid binding from this data as the protein used in this experiment will still have partial lipid binding properties.<br /> • The authors next investigate actin binding by TgGAC and show that most of the N-terminal half of the protein is required for this function. The authors propose, using AlphaFold2 and similarities to catenins, how GAC might bind to actin. In the absence of any validation from experimental data, caution is needed here, and I would personally not rely on the accuracy of these models.

Reviewer #2 (Public Review):

Toxoplasma gondii (Tg) and Plasmodium falciparum (Pf) are two protozoan parasites that both present threats to global human health as the causal agents of toxoplasmosis and malaria, respectively. In absence of effective vaccines, disease control relies heavily on the use of drugs aimed at treating infected patients to inhibit parasitic growth and eventually kill parasites to interrupt the parasitic lifecycle. These obligate intracellular vacuole-dwelling parasites quickly attach to their host cells before actively pinching through their plasma membranes and completing their complex respective lifecycles.

Kumar et al. seek to understand the complex process of host cell recognition, attachment, and invasion in order to devise possible strategies to possibly interfere and/or block to prevent invasion of the host cell or compromise egress from the infected cell. Characterizing the 3D structure at atomic resolution and dynamics of the glideosome molecular machinery involved in parasite attachment and invasion/egress provides grounds for the future rational design of novel anti-parasitic therapies targeting novel molecular targets and phylum-specific biological processes. Toxoplasma belongs to the same large family of obligate intracellular parasites such as the malaria parasite Plasmodium. These protozoa actively attach and glide at the surface of their target host cell before invading it. Such motility and propulsion at the surface of the host cell are powered by a large protein complex, the glideosome.

The article elegantly combines structural, biophysical, biochemical, computational, and cell biology approaches to dissect the structure and mechanism of action of TgGAC (and PfGAC).

The crystal structure of TgGAC was solved at an apparent 2.7A resolution by se-mad and although it is overall well described it requires further polishing in terms of model quality and accuracy. This is a very large protein, so it represents a considerable amount of work to build and refine. We note deficiencies in the way refinement (atomic displacement parameters and model building in general) and phasing statistics description were carried out or presented. This warrants further inspection and requires significant improvement and corrections to meet the usual standards expected from this field of research.

Solution scattering data while supporting the model of a conformational change between a compact (closed) conformation observed in the crystal obtained at pH 5 and an extended monomeric conformation observed at pH 8 more amenable to interactions with other cellular partners in the context of a functional glideosome needs some clarification. Because of the way proteins seem to be prepared for the SAXS analysis, I have some objections to the interpretation of some of the data.

The biochemical analysis of lipid binding specificity of the small c-terminal pleckstrin-like domain of TgGAC and PfGAC (full-length or c-terminal domain) using liposome binding assays, elegant NMR relaxation methods but also molecular dynamics on full-length GAC models are extremely convincing and support all authors claim.

The fact that however the CTD lipid binding activity is not required in vivo is a bit surprising although CTD seems required to stabilize the protein in vitro.

The section describing the hydrogen-deuterium exchange analysis of TgGAC conformation is confusing as it stands and requires clarification. It fails to be compelling in my personal opinion.

Reviewer #3 (Public Review):

The authors present a multi-disciplinary structural analysis of the glideosome-associated connector (GAC), which is important for the motility of parasites within the Apicomplexa phylum. Strengths of the study include the first crystal of the GAC, revealing an elaborate pyramid structure with a protruding arch bearing a PH domain. The lipid binding analyses, featuring NMR experiments and simulations to identify key residues, provide a nice complement to the crystal structure. There are interesting differences between the structure obtained and the small-angle X-ray scattering data, which are plausibly (but not conclusively) explained by a model in which GAC uses multiple conformations. It is also puzzling that the lipid binding residues in the PH domain do not seem vital for parasite invasion, although this may be explained by the second lipid binding site in the GAC arch. The AlphaFold prediction of the interface between the GAC and a peptide from MIC2 is interesting, in that it is reminiscent of the B-catenin/E-cadherin interaction, but requires validation. The study will be useful for researchers investigating the structural mechanism of parasite motility.

Reviewer #1 (Public Review):

During the height of the Covid19-pandemic, there was great and widely spread concern about the lowered protection the screening programs within the cancer area could offer. Not only were programs halted for some periods because of a lack of staff or concern about the spreading of SARS CoV2. When screening activities were upheld, participation decreased, and follow-up of positive test results was delayed. Mariam El-Zein and coworkers have addressed this concern in the context of cervical screening in Canada, one of the rather few countries in the world with well organized, population-based, although regionalized, cervical screening program.

Despite the existence of screening registries, they choose to do this in form of a survey on the internet, to different professional groups within the chain of care in cervical screening and colposcopy. The reason for taking this "soft data" approach is somewhat diffuse. The authors claim they want to "capture modifications". However, the suggestions that come from this study are limited and are submitted for publication 2 years after the survey when the height of the pandemic has passed long since, and its burden on the screening program has largely disappeared. The value of the study had been larger if either the conclusions had been communicated almost directly, or if the survey had been done later, to sum up the total effect of the pandemic on the Canadian cervical screening program.

Another major problem with this study is the coverage. The results of persistent activities to get a large uptake is somewhat depressing although this is not expressed by the authors. 510 professionals filled out the survey partially or in total. 10 professions were targeted. The authors make no attempt to assess the coverage or the validity of the sample. They state the method used does not make that possible. But the number of family practicians, colposcopists, cytotechnicians, etc. involved in the program should roughly be known and the proportion of those who answered the survey could have been calculated. My guess is that it is far below 10%. Also, the national distribution seems shewed despite the authors boosting its pan-Canadian character. I am just faintly familiar with the Canadian regions, but, as an example, only 2 replies from Quebec must question the national validity of this survey.

The result section is dominated by quantitative data from the responses to the 61 questions. All questions and their answers are tabulated. As there is no way to assess the selection bias of the answers these quantitative results have no real value from an epidemiological standpoint. The replies to the open-ended questions are summarized in a table and in the text. The main conclusion of the content analysis of the answers to the direct questions, and one of the main conclusions of the study, is that the majority favors HPV self-sampling in light of the pandemic. However, this not-surprising view is taken by only 80 responders while almost as many (n=60) had no knowledge about HPV self-sampling.

The authors conclude that their study identified the need for recommendations and strategies and building resilience in the screening system. No one would dispute the need, but the additional weight this study adds, unfortunately, is low, from a scientific standpoint.

The conclusion I draw from this study is that the authors have done a good job in identifying some possible areas within the Canadian screening programs where the SARS-Cov2 pandemic had negative effects and received some support for that in a survey. Furthermore, they listed a few actions that could be taken to alleviate the vulnerability of the program in a future similar situation, and received limited support for that. No more, no less.

Reviewer #2 (Public Review):

The study aimed to provide information on the extent to which the COVID-19 pandemic impacted cervical cancer (CC) screening and treatment in 3 Canadian provinces. The survey methodology is appropriate, and the results provide detailed descriptive statistics by province and type of practice. The results support the authors' conclusions. This evidence together with data gathered from other national surveys may provide baseline data on the impact of the pandemic on CC outcomes such as late-stage diagnoses and CC treatment outcomes due to these delays.

Reviewer #1 (Public Review):

OTOP ion channels are proton-activated, proton-permeable proteins that participate in sour tasting but for which other physiological roles are just beginning to be elucidated. The authors of this manuscript noticed that the isoform OTOP3 shows activation by protons that are potentiated in the presence of Zn2+ and other divalent ions, while other isoforms are not weakly or not at all potentiated. This allowed them to apply a chimeric approach to define which regions of the protein are responsible for the Zn2+ effect. The authors found that a single extracellular loop and a single histidine residue located in it are sufficient to explain the potentiation and propose that this histidine is part of a binding site that allosterically couples to yet undefined proton binding sites(s) responsible for proton gating.

The authors have performed very high-quality experiments and carried out a careful analysis of the data. This characterization of gating behavior of OTOP channels should be a step in elucidating physiological roles and in understanding the dynamics of these proteins. For these reasons, it should be of interest to researchers working in molecular biophysics and the physiological roles of ion channels.

Reviewer #2 (Public Review):

OTOP channels are relatively newly discovered and their physiology is poorly understood. Zn activation appears to be a differentiating feature of OTOP function and Zn is a pharmacological tool for research. The Zn potentiation of OTOP3 is a curious phenomenon that is studied very carefully here. The language in this manuscript is appropriately nuanced in the interpretation of results and is delightfully agnostic with regards to function vs binding. The major strengths of this work are the very thorough characterization of the zinc effect and the identification of the 11-12 loop as necessary and sufficient for the zinc effect.

Reviewer #3 (Public Review):

The authors characterized the effect of Zn2+ in potentiating OTOP1 and OTOP3 proton-activated H+ currents. They took advantage of a set of chimeras with swapped extracellular loops between OTOP3 (Zn2+-dependent potentiation) and OTOP2 (no potentiation) by neatly identifying an extracellular loop that is sufficient to confer Zn2+ potentiation. The results support the idea that within this loop resides at least part of the Zn2+ binding site, a hypothesis also confirmed by the role of a histidine residue. The authors suggested that Zn2+ potentiation of OTOP3 involves different structural elements than those required for inhibition, the conclusion that is supported by the data on the OTOP3-OTOP2 chimeras. These results shed light on a new aspect of the gating mechanism of these channels, adding an important piece to the puzzle to decipher their role in cells. This manuscript provides an important result for scientists whose research is focused on proton channels, and ion channel gating mechanisms.

Weaknesses: Although the identification of the extracellular loop represents an important result to define the structural element that confers Zn2+ potentiation to OTOP3, there are several aspects of the gating mechanism that would require a deeper analysis. The mutagenesis of the OTOP3 tm11-12 linker is very limited and does not include mutagenesis experiments in OTOP2 and OTOP1 that would further support the conclusion proposed by the authors and extend the importance of the tm11-12 linker to all the three OTOP channels (as stated in the manuscript title).<br /> Moreover, only one residue has been identified as important for Zn2+ binding. Given the three-dimensional structures of OTOP channels available to this date, particularly the chicken OTOP3 structure (PDB:6NF6), a structural analysis would certainly provide a set of putative partners for the histidine identified as the key residue for Zn2+ potentiation. Even if it is hard to understand what conformational state is represented in the structure, this analysis will provide a valid starting point to investigate the functional relevance of these residues.

Reviewer #1 (Public Review):

In this study, the authors set out to determine the degree to which early language experience affects neural representations of concepts. To do so, they use fMRI to measure responses to 90 words in adults who are deaf. One group of deaf adults (n=16) were native signers (and thus had early language exposure); a second group (n=21) was exposed to sign language later on. The groups were relatively well-matched in other respects. The primary finding was that the high dimensional representations of concepts in the left lateral anterior temporal lobe (ATL) differed between native and delayed signers, suggesting a role for early language experience in concept representation.

The analyses are carefully conducted and reflect a number of thoughtful choices. These include the "inverted MDS" method for constructing semantic RDMs, a normal hearing comparison group for both behavioral and fMRI data, and care taken to avoid bias in defining functional ROIs. And, comparing early and delayed signing groups is a clever way to study the role of early language experience on adult language representations.

One interesting result that I struggled to put in a broader context relates to the disconnect between behavioral and neural results. Specifically, the behavioral semantic RDMs (Figure 1a) did not differ between any of the groups of participants. This suggests that the representations of the 90 concepts are represented similarly in all of the participants. However, the similarity of the neural RDMs in left lateral ATL differs between the native and delayed signing groups (but not in other regions). Given the similarity of the behavioral semantic RDMs, it is unclear how to interpret the difference in left lateral ATL representations. In other words, the neural differences in left ATL do not affect behavior (semantic representation). The importance of the differences in neural RDMs is therefore questionable.

An important point is that, if I understand correctly, the semantic space is defined by the 90 experimental items. That is, behavioral RDMs were created by having normal hearing participants arrange 90 items spatially, and neural RDMs were created by comparing patterns of responses to these 90 experimental items. This 90-dimensional space is thus both (a) lower dimensional than many semantic space models that include hundreds of directions and (b) constrained by the specific 90 experimental items chosen. On the one hand, this seems to limit the generalizability of the findings for semantic representations more broadly.

The logic behind using a categorical semantic RDM (e.g., Figure 2a) was not clear. The behavioral semantic RDMs (Figure 1a) clearly show gradations in dissimilarity, particularly for the abstract categories. It would seem that using the behavioral semantic RDM would capture a more accurate representation of the semantic space than the categorical one.

Reviewer #2 (Public Review):

The authors investigated patterns of fMRI activation for familiar words in two groups of deaf people. One "language rich" group received exposure to sign from birth, whereas the "language poor" group included kids born to hearing parents who had limited exposure to language during the first few years of life. The primary findings involved group differences in BOLD activation patterns across different areas of interest within the semantic network when participants made intermittent 1-back category judgments for words appearing in succession.

There was much to be liked about this study, including the rigor of the methods and the novel contrasts of two deaf samples. These strengths were balanced by a number of questions about the assumptions and theoretical interpretations underlying the data. I will elaborate on the major points in the paragraphs to follow, but briefly, the ways in which the authors are framing critical period constraints in language fundamentally differ from the standard nativist perspectives (e.g., Chomsky, Lenneberg). The assumptions of what constitutes a deprivation model require further justification and perhaps recasting to avoid unnecessary stigma (i.e., this reviewer was uncomfortable with the assertion that being born deaf to hearing parents by default constitutes deprivation). The introduction lacked principled hypotheses that motivated the choice of comparing abstract and concrete words, and potential accounts of group differences were underdeveloped (e.g., how do parents in China typically react to having a deaf child, and what supports are in place for preventing language deprivation? Are newborn infants universally screened for hearing loss in China? The answers to these questions might help the readers to understand why/how deaf children in this circumstance might experience deprivation).

References to critical periods require a bit more elaboration with respect to lexical-semantic vs. semantic acquisition. The nature of the critical period in language acquisition remains controversial with respect to its constraints. Lenneberg and Chomsky speculated that the limit of the critical period for language acquisition was about puberty (13ish years of age). This is much older than the deaf sample tested here so arguments about aging out of the critical period at least for language acquisition need more nuance. Another issue relates to learning semantic mappings vs. learning language as falling under the same critical period umbrella. This seems highly unlikely as semantic acquisition in early childhood is aided by linguistic labeling but would likely occur in parallel even in the context of language deprivation. Much of the prior literature on critical periods and nativist approaches to language development has focused on syntactic acquisition and elements such as recursion rather than a mapping of symbols to conceptual referents. This makes the critical period group comparison somewhat tenuous because what you are really interested in is a critical period for word meaning acquisition not the more general case of syntactic competency.

The point above is highlighted in the following statement underlying one of the primary assumptions of the study:<br /> Pg. 3, "Here, we take advantage of a special early-life language-deprivation human model: individuals who were born profoundly deaf in hearing families and thus had very limited natural language exposure (speech or sign) during the critical period of language acquisition in early childhood"

"hypofunction of the language system as a result of missing the critical period of language acquisition" (pg 3), same critique as previous - the critical period window is thought to be 13ish years old.

There are a couple of problems with this assertion/assumption. Although it is true that most children who are born deaf have hearing parents, it is not justifiable to label this condition an early-life deprivation model. Hearing parents who are extremely motivated to learn sign language and pursue related language enrichment strategies can successfully offset many of these effects. Similarly, it is not inconceivable that a deaf child born to a deaf parent might be neglected or abandoned without the benefit of early sign exposure. My argument here is that classifying deaf children born to hearing parents as automatically 'language deprived' is potentially both stigmatizing and scientifically unjustified.

Pg. 6 "It should be noted that the neural semantic abstractness effect does not equate with language-derived semantic knowledge, as it might arise from some nonverbal cognitive processes that are more engaged in abstract word processing (Binder et al., 2016)." - I had great difficulty understanding what this meant.

Reviewer #3 (Public Review):

This work extends earlier findings from this group which showed in congenitally blind individuals preserved, presumably language-derived, representations of colour knowledge are present only in dATL. While the present study confirms the importance of language in representations in dATL, the specificity of dATL hinges on descriptive rather than inferential statistics, and future studies may be needed to demonstrate the primacy of dATL in language-based representation as well as the generalisability of effects across different flavours of conceptual knowledge.

Reviewer #1 (Public Review):

In this paper, the authors present a method for discovering response properties of neurons, which often have complex relationships with other experimentally measured variables, like stimuli and animal behaviors. To find these relationships, the authors fit neural data with artificial neural networks, which are chosen to have an architecture that is tractable and interpretable. To interpret the results, they examine the first- and second-order approximations of the fitted artificial neural network models. They apply their method profitably to two datasets.

The strength of this paper is in the problem it is attempting to solve: it is important for the field to develop more useful ways to analyze and understand the massive neural datasets collected with modern imaging techniques.

The weaknesses of this paper lie in its claims (1) to be model free and (2) to distinguish the method from prior methods for systems identification, including spike triggered averaging and covariance (or rather their continuous response equivalents). On the first claim, the systems identification methods are arguably substantially more model free approach. On the second claim, this reviewer would require more evidence that the presented approach is substantially different from or an improvement on systems identification methods in common use applied directly to the data.

Reviewer #2 (Public Review):

This paper describes a relatively unbiased and sensitive method for identifying the contributions of different behavioral parameters to neural activity. Their approach addresses, in an elegant way, several difficulties that arise in modeling of neuronal responses in population imaging data, namely variations in temporal filtering and latency, the effects of calcium indicator kinetics, interactions between different variables, and non-linear computations. Typical approaches to solving these problems require the introduction of prior knowledge or assumptions that bias the output, or involve a trade-off between model complexity and interpretability. The authors fit individual neuron's responses using neural network models that allow for complex non-linear relationships between behavioral variables and outputs, but combine this with analysis, based on Taylor series approximations of the network function, that gives insight into how different variables are contributing to the model.

The authors have thoroughly validated their method using simulated data as well as showing its applicability to example state of the art data sets from mouse and zebrafish. They provide evidence that it can outperform current approaches based on linear regression for the identification of neurons carrying behaviorally relevant signals. They also demonstrate use cases showing how their approach can be used to classify neurons based on computational features. They have provided Python code for the implementation and have explained the methods well, so it will be easy for other groups to replicate their work. The method could be applied productively to many types of experiments in behavioral and systems neuroscience across different model systems. Overall, the paper is clearly written and the experiments are well designed and analysed, and represent a useful contribution to the neuroscience field.