Reviewer #3:

-The authors claim in the first part of the results that the frequency of CSF-cN spontaneous activity is the same in juvenile and adult mice. In Fig.1G, 61 neurons from 7 animals are illustrated. The authors should state how many juvenile (P14-P24) and adult (P36-P47) mice have been included in the analysis (3 and 4 is different from 5 and 2) and how many neurons have been recorded in each animal. In the methods section, they indicate that acute slices were obtained from P14 to P55 mice. If the reviewer is correct, neurons from P55 mice are not included in Fig. 1G?

-The immunohistochemical data have been obtained in P30-P52 mice. Are P14 CSF-cNs all VGaT positive?

-The frequency of CSF-cN spontaneous activity could be the same but underlying mechanisms could completely differ with age. In Fig. 3, TTX fails to alter spontaneous Ca2+ spike expression in 3 animals. How old are these mice? Same questions for the results with Cd (2 animals, sample a little bit small...), ML218 4 animals (4 animals)...etc

-The focal ejection of 40mM K+ triggers a depolarization of all CSF-cNs "including those previously silent". This is the first time page 9 that the authors mention the fact that some CSF-cNs are not spontaneously active. Is the proportion of silent CSF-cNs different with age? The effects of Cd have been tested in 1 animal. Same for the effect of MCA on Ach-evoked Ca2+ spikes. In my opinion, the sample size has to be increased.

Reviewer #3:

Jacob and colleagues developed a new experimental "facility" or environment for training macaque monkeys to perform behavioral tasks. Using this facility, the authors trained freely moving macaques to perform a visual "same-different" task using operant conditioning, and under voluntary head restraint. The authors demonstrate that they could obtain reliable eye-tracking data and high performance accuracy from macaques in this facility. They also noted that subordinate macaques can learn to perform basic aspects of the task by observing their dominant conspecifics perform the task in this facility. The authors conclude that this naturalistic environment can facilitate the study of brain activity during natural and controlled behavioral tasks.

The manuscript is doubtless a hard-fought effort. The new experimental platform introduced by the authors has the capacity to transform how researchers approach the behavioral training of monkeys for some (but not all) tasks. However, in my opinion, the manuscript would have significantly broader impact and appeal if the authors had succeeded in performing wireless neural recordings in this same environment. Without these proof-of-principle neural data, the scope of this manuscript seems more limited. If the authors can obtain these neural data, the manuscript would be substantially stronger.

There are a few other concerns related to methodology and interpretation that should be addressed.

Major comments:

1) In the abstract, the authors state that macaques are widely used to study the neural basis of cognition - but in fact these animals are a valuable model organism for studying many other aspects of brain function beyond cognition. The authors seem to be missing an opportunity to highlight the broad impact of their work.

2) A gaze window of 3 degrees is rather large for most visual-based experiments. Do the authors think that it would be possible to train animals to maintain tighter fixation windows? And have they tried to do so?

3) Are these animals water deprived before entering the experimental environment? And how long do the animals typically work in this environment? For how many hours, and for how much fluid?

4) How did the authors ensure that the macaques do not fight inside the facility? Are the animals continuously housed in this facility or are they moved into this facility only during testing?

5) Line 227: the authors state the following: "Remarkably, M2 learned the task much faster using social observation and learning than M1 & M3 did using the TAT paradigm". How do the authors rule out the possibility that M2 is simply a "smarter" animal?

6) Line 354-364: the authors describe their insights about how animals may learn to perform the task in two phases. How can the authors make these strong claims based on data from N=1 macaque?

Reviewer #3:

The authors present a simple model that explains important outstanding controversies in the field of long-range gene regulation. These controversies include the fact that insulation boundaries tend to be weak; that acute inactivation of CTCF or cohesin (that leads to inactivation of insulation boundaries) leads to only minimal gene expression and that in live cells enhancer-promoter contacts appear not correlated with transcriptional bursting. The model involves a futile cycle of tag addition and removal from promoters, stimulation of more tag addition when tag is already present, and stimulation of tag addition by contacts with distal enhancers. The authors show that such a model explains all the above controversies, and indicate that the controversies are not inconsistent with mechanisms where long-range gene activation is driven by physical contacts with distal regulatory elements.

The authors have explained and explored the properties of the model well. I have only minor comments.

1) An alternative explanation for TAD-specific enhancer action is that an E-P interaction within a TAD (between two convergent CTCF sites), one that is brought about by extruding cohesin, is not equivalent to an interaction that occurs between two loci on either side of a CTCF site and that can be a random collision that is not mediated by extruding cohesin. In other words, two interactions can be of the same frequency but can be of a very different molecular nature. I agree that this model would not explain the results of the experiment where cohesin is acutely removed.

2) In the beginning of the introduction the authors introduce TADS. I recommend that the authors present this in a more nuanced way: compartment domains also appear as boxes along the diagonal, an issue that has led some in the chromosome folding field to be confused. This reviewer believes TADS are those domains that strictly depend on cohesin mediated loop extrusion, whereas compartment domains are not. If the authors agree, perhaps they can rewrite this section?

3) If I understand the model correctly, the nonlinearity arises because of the increased rate of tag addition when tag is already present. The authors then speculate histone modifications can be one such tag. However, there are only so many sites of modification at a promoter. Can the authors analyze how the possible range of tag densities affects performance of the model? Is the range required biologically plausible?

4) Can the authors do more analysis to explore how rapid changes in gene expression may occur (e.g. upon signaling a gene may go up within minutes)? How much more frequent does the E-P interaction need to be for rapid switch to the active promoter state? Can the authors do an analysis where they change the rates of the futile cycle upon some signal: at what time scale does transcription then change (keeping E-P frequency the same)?

Reviewer #3:

The manuscript explores ageing-associated changes in the Drosophila escape-response (Giant Fiber, GF) circuit and the circuits converging onto the GF. This a convenient system amenable to detailed physiological analyses and the authors made a good effort in extracting a large amount of useful information using a wide range of electrophysiological readouts. The authors identified several physiological parameters that are potentially useful for indexing ageing progression in flies such as ID spike generation and ECS-evoked seizure threshold. The host lab is well-known for its expertise in the field of GF physiology; consequently, the experiments were done with a high level of technical competence and presented (mostly) in a clear and informative manner. There is, however, one major issue that could restrict the usefulness of the data presented in the manuscript (please, see major comment 1).

Major comments:

1) Standards for conducting ageing studies in Drosophila and other model systems have gone significantly up in the last ~15 years following experimental evidence that genetic background can (and does) have a significant effect on the outcome of 'ageing' experiments (see Partridge and Gems, Nature, 2007). Today, 'backcrossing' relevant lines into a reference wild-type strain multiple times (to remove any second-site mutations) is a gold standard for virtually all ageing studies in Drosophila. Furthermore, this approach is being widely adopted even in the studies investigating physiological properties in developing flies (for example, in Imlach, Cell, 2012, the authors obtained very different electrophysiological results after 'isogenizing' the genetic background via backcrossing, and concluded that "the previous finding may have been due to a second site mutation"). As this important step is not mentioned in either the main text or in 'Methods' section, it is reasonable to conclude that the authors did not perform this step prior to conducting the experiments. Recent papers, one of which was referenced by the authors (Augustin et al PloSBiol 2017 and NeuroAging 2018) repeatedly demonstrated a significant, age-associated increase in the short-response (TTM and DLM) latency in the GF circuit following a strong stimulation of the GF cell bodies in the brain. It is likely that these age-related changes in the GF circuit remained undetected in the flies with non-uniform genetic background likely used in this work. The same problem affects the paper (Martinez, 2007) referenced by the authors throughout the manuscript.

It is difficult to say which of the findings reported here are most affected by the variability in the genetic background, but any kind of correlation between the lifespans (Figure 1B) and physiological parameters should be taken with a high dose of scepticism.

2) The manuscript is entirely 'phenomenological' in the sense that it does not investigate the causes of the observed physiological changes. The manuscript (with minor exceptions) does not discuss the possible reasons behind the functional readouts or speculate about what makes the (sub)circuits differentially susceptible to the effect of ageing. For example, when mentioning the effects of temperature and Sod mutation on the fly physiology, the authors limit their comments to generic and obvious statements such as 'oxidative stress exerts strong influences differentially on some of the physiological parameters and the outcomes are distinct from the consequences of high-temperature rearing'. Some of the possible questions the authors could ask are: could changes in the kinetics of relevant ion channels explain some of the results obtained under different temperatures; could the previously demonstrated effect of ROS on voltage-gated sodium channels explain some of the Sod1 phenotypes, etc?

Reviewer #3:

In this interesting paper authors compare MEG recordings of svPPA patients and 44 healthy controls during living vs. non-living categorization tasks. Both patients and the control group performed this task with similar accuracy. In addition, svPPA patients showed greater activation over bilateral occipital cortices and superior temporal gyrus, and inconsistent engagement of frontal regions. The authors conclude that patients with svPPA compensate for their semantic deficit by recruiting regions involved in perceptual processing.

This is a well written study and the results are presented clearly. The findings are novel and interesting.

1) One question for clarification is whether the recruitment of the occipital areas in semantic PPA is truly "compensatory" - does it indicate a shift of resources due to the anterior temporal atrophy? Is the recruitment of the parieto-occipital regions associated with more accurate performance?

2) The main results concentrate on the differences between patients and controls in the low gamma range. There are also significant effects in the other frequency bands (e.g., high gamma, beta and alpha). Could the authors discuss the functional significance of these effects?

Reviewer #3:

Neuronal ensembles have been shown by this lab and others to constitute one basic functional unit for the representation of information in cortical circuits. It is therefore important to determine how stable these blocks of representation might be. If these ensembles were preserved across time and sensory stimuli, this would indicate a significant degree of structure underlying cortical representations. In a first attempt to address these important issues, this manuscript analyzes the long-term stability of ensembles of coactive neurons in the layer 2/3 of mouse visual cortex across several days. Ensembles were recorded during periods of spontaneous activity as well as during visual stimulation (evoked). For this, the authors record spontaneous and evoked activity using two-photon calcium imaging one, ten and 40 days after the first recording session. In order to maximize overlap between successive imaging sessions, the authors record three planes separated by 5 microns almost simultaneously (9ms interval) using an electrically-tunable lens. They show that ensembles extracted during visual stimulation periods are more stable on days 2 and 10 than those computed during spontaneous activity. Stable ensembles display a higher "robustness" (a parameter that quantifies how many times a given ensemble is repeated and how similar these repeats are) . Neurons displaying stable membership are more functionally connected than unstable ones. It is concluded that such observed stability of spontaneous and evoked ensembles across weeks could provide a mechanism for memories. Long-term calcium imaging within the same population of neurons is a real challenge that the authors seem to overcome in the study. The conclusions are important, my main concern relates to the number of experiments and analyses supporting these findings as detailed below.

Number of experiments and statistics: According to Table 1, two mice with GCamP6f have been through the complete imaging protocol (days 1,2, 10 and 43) but none with the 6s, since 3 missed the intermediate measure (day 10) and one the last point (day 40+). Therefore five mice have been recorded over weeks with two different indicators, but only two were sampled on day 10. One mouse was only recorded until day 10. Altogether, this is quite a low sampling, but the experiments are certainly difficult. However, the total number of experiments analyzed is higher, due to the repeat of 3 sessions on the same mouse per day. This certainly contributes to reaching significance. However, the three samples from the same mouse are not independent points. Are the FOVs different for each session in the same mouse? If they are the same, then the statistics should be repeated but treating all experiments from the same mouse as single experiments. I would suggest repeating the analysis but using only one data point per mouse per day. Also, given that two different indicators were used (6s and 6f), one would need to see whether the statistics are the same in the two conditions.

Robustness: the authors compute this metric, as the product of ensemble duration and average of the Jaccard similarity and find that stable ensembles display higher robustness: isn't it expected that robustness is higher in stable ensembles given that stable ensembles should be observed more often?

Evoked ensembles: It seems to me that evoked ensembles are ensembles extracted during continuous imaging periods that include stimulation. However, one would expect evoked ensembles to be the cells activated time-locked to the visual stimulation. This notion only appears at the end of the paper with "tuned" neurons in Fig. 4. In the discussion, authors conclude lines 205-207 that "sensory stimulus reactivate existing ensembles" . I do not think this is supported by the analysis performed here. For this, I believe that one would need to compare, within the same mouse the amount of overlap between spontaneous ensembles and "tuned neurons".

How representative are the illustrated examples in Figs. 2&3? The authors report that about 20 neurons remain active from day 1 to 46 but their main figures display example rasterplots with more than 60 neurons, which is three times more than the average. Is this example representative? Which indicator was used? Is there a difference in stability between 6f and 6s?

Rasterplot filtering: The authors chose to restrict their ensemble analysis to frames with "significant coactivation". Why not use a statistical threshold to determine the number of cells above which a coactivation is significant instead of arbitrarily setting this number to three coactive neurons? In cases of high activity this number may be below significance.

Demixing neuronal identity: The authors assign a neuron to an ensemble if it displays at least a functional connection with another neuron. They use reshuffling to test significance of functional links but still it seems that highly active neurons are more likely to display a high functional connectivity degree and therefore to be stable members of a given ensemble with that definition of ensemble membership. What is the justification to define membership based on pairwise functional connectivity? The finding that core ensemble members display a high functional degree may be just a property reflecting a property of highly active neurons (as previously described by Mizuseki et al. 2013).

Type of neurons imaged: The authors use Vglut1-Cre mice, therefore they are excluding GABAergic cells from their study, this should be clearly mentioned and even discussed.

Volumetric imaging: I am not sure one can say that "volumetric imaging" was performed here, rather this is multi-plane imaging.

Mouse behavior: there is little detail concerning mouse behavior, are mice allowed to run? What is the correlation between ensemble activation and running?

Abstract: the authors should say that 46 days is the longest period they have been recording, otherwise it gives the wrong impression that after 46 days ensembles are no longer stable. Also "most visually evoked ensembles" should be replaced by "ensembles observed during periods of visual stimulation" (see above). "In stable ensembles most neurons still belonged to the same ensemble after weeks": how could ensembles be stable otherwise?

Discussion: I found the discussion quite succinct. It lacks discussion of the circuit mechanisms for assembly stability and plasticity (role of interneurons for example?), the limitations and possible biases in the analysis and the placing of the results in the perspective of other studies analyzing the long-term stability of neuronal dynamics.

Reviewer #3:

From the technical perspective this manuscript provides clear results that are consistent with, but do not prove, what this reviewer believes is the main objective of the work; to establish the relevance of the open structure of the eukaryotic cysteine desulfurase complex. This reviewer has no good basis to either accept or reject the open structure as having physiological relevance. This could well be the case but it is not clear from my (limited) knowledge of the published literature that the relevance of the open structure is generally accepted. From this perspective I believe the manuscript is sound from the technical approach and experimental implementation but suffers from a lack of clarity about the case for and against the relevance of the open structure. If this is a point of controversy in the field the topic should be discussed in depth and the position of the authors more clearly articulated.

Reviewer #3:

This study combines two cutting-edge approaches for the study of polyclonal antibody responses to understand the molecular profiles of antibodies elicited by HIV envelope trimer immunization in a rabbit model. In one arm of the study, the authors performed mutational profiling of serum antibody neutralization escape variants, and in the second arm they used electron microscopy polyclonal epitope mapping (EMPEM) to track antibody binding sites. These authors performed large-scale data collection and present high-quality validation data and explorations of the resulting datasets that compare antibody binding and virus neutralization profiles. These approaches provide a comprehensive window into the molecular specificity and performance of HIV immunization and are expected to inform advanced HIV-1 vaccine designs.

Summary of any substantive concerns:

The authors have done a nice job validating the integrity of the NGS data, and the strong data in Figs 4/5/2B show the power of the NGS-based neutralization mapping assays. This adds a solid confirmation of the study findings and demonstrates the quality of the techniques. Overall this is a solid study and the findings are informative. I see just a few methods updates and analyses that would help finalize the presentation of methods and data.

1) Additional information on the bioinformatic methods for data analysis is needed. How did the authors handle discrepancies in data across replicates or libraries, for example if a mutation that was enriched in one library or replicate, but deleted in another? Were there any quality filters or metrics used to estimate true signal vs. noise?

2) Differential selection statistics are mentioned briefly, along with citations to prior publications. Prior citations are definitely helpful. I think it is still important to state the key steps used in processing NGS data and the statistical techniques and quality metrics that were used. The authors should also state any criteria for acceptance or rejection or binning of individual data points, or acceptance/rejection of datasets or replicates, if quantitative criteria or metrics were used.

3) Several replicates showed a low percentage infectivity (Fig S1, e.g. animals 5724 and 2124), but the text indicates averages between 0.3% and 2.7% infectivity. Were some groups omitted from analysis, or were all groups included?

4) How well did the mutational profiles correlate between different libraries or replicates of the same samples?

Reviewer #3:

The authors probe mechanosensory processing in Hydra by measuring calcium activity in neurons and muscles in response to precise mechanosensory stimulation in whole and resected animals. The authors' claims are well supported by the evidence. The development of a mechanosensory delivery system for Hydra is also a significant methodological advancement. Taken together, the work advances our understanding of the Hydra nervous system and is a needed step towards developing Hydra as a powerful model for systems neuroscience.

Substantive concerns:

1) One weakness is that different measures of "mechanosensory response" are used at different places in the manuscript. In some contexts, a response is defined as calcium activity in neurons (Fig 2), and elsewhere as calcium activity in muscles (Fig 3 and 4). And in Fig2 SuppFig2 muscle contractions are also measured using MeKs. The relation between neural activity, muscle activity and body movement is of course of high interest, and the paper explores this. But, if technically possible, it would be helpful to report a single metric of behavior that could be used in all experiments. For example, it might be possible to use video of the animal's pose or body length to measure contractions in all experiments. At a minimum the reasoning behind choice of measurement of response for each experiment could be discussed explicitly.

2) Related: Without a consistent measure of behavior, it will be important to further clarify figures so that a reader can tell at-a-glance how contraction probability is being measured.

Reviewer #3:

The manuscript describes interesting experimental and modelling results of a novel study of human navigation in virtual space, where participants had to move towards a briefly flashed target using optic flow and/or vestibular cues to infer their trajectory via path integration. To investigate whether control dynamics influence performance, the transfer function between joystick deflection and self-motion velocity was modified trial-by-trial in a clever way. To explain the main result that navigation error depends on control dynamics, the authors propose a probabilistic model in which an internal estimate of dynamics is biased by a strong prior. Even though the paper is clearly written and contains most of the necessary information, the study has several shortcomings, as outlined below, and an important alternative hypothesis has not been considered, so that some of the conclusions are not fully supported by results and modelling.

Substantive concerns

1) The main idea of the paper for explaining the influence of control dynamics is that for accurate path integration performance participants have to estimate dynamics. This idea is apparently inspired by studies on limb motor control. However, tasks in these studies are often ballistic, because durations are short compared to feedback delays. In navigation, this is not the case and participants can therefore rely on feedback control (for another reason, why reliance on sensory feedback in the present study is a good idea, see point 2 below). This means that the task can be solved, even though not perfectly, without actually knowing the control dynamics. Thus, an alternative hypothesis for explaining the results that has not been considered is that the error dependence of control dynamics is a direct consequence of feedback control. Feedback control models have previously been suggested for goal-directed path integration (e.g., Grasso et al. 1999; Glasauer et al. 2007).

To test this assumption, I modelled the experiment assuming a simple bang-bang feedback control that switches at a predefined and constant perceived distance from the target from +1 to -1 and stops when perceived velocity is smaller than an epsilon. Sensory feedback is perceived position, which is assumed to be computed via integration of optic flow. This model predicts a response gain of unity, a strong dependence of error on time constant (slope similar to Fig. 3) or of response gain on time constant (Eqn. 4.1) with regression coefficients of 0.8 and 0.05 (cf. Fig. 3D), and a modest correlation between movement duration and time constant (r approximately 0.2, similar to Fig. 3A). Thus, a feedback model uninformed about actual motion dynamics and without any attempt to estimate them can explain most features of the data. Modifications (velocity uncertainty, delayed perception, noise on the stopping criterion, etc.) do not change the main features of the simulation results.

Accordingly, since simple feedback control seems to be an alternative to estimating control dynamics in this experiment, the authors' conclusion in the abstract "that people need an accurate internal model of control dynamics when navigating in volatile environments" is not supported by the current results.

2) Modelling: the main rationale of the model (line 173 ff: "From a normative standpoint, ...") is correct, but an accurate estimate of the dynamics is only required if the uncertainty of the velocity estimate based on the efference copy is not too large. Otherwise, velocity estimation should rely predominantly on sensory input. In my opinion that's what happens here: due to the trial-by-trial variation in dynamics, estimates based on efference copy are very unreliable (the same command generates a different sensory feedback in each trial), and participants resort to sensory input for velocity estimation. This results in feedback control, which, as mentioned above, seems to be compatible with the results.

3) Motion cueing: Motion cueing can, in the best case, approximate the vestibular cues that would be present during real motion. Furthermore, it is not clear whether the applied tilt is really perceived as linear acceleration, or whether the induced semicircular canal stimulus is too strong so that subjects experience tilt. Participants might have used the tilt as indicator for onset or offset of translational motion, specifically because it is self-generated, but the contribution of the vestibular cues found in the present experiment might be completely different from what would happen during real movement. Therefore, conclusions about vestibular contributions are not warranted here and cannot solve the questions around "conflicting findings" mentioned in the introduction.

4) Methods: I was not able to find an important piece of information: how many trials were performed in each condition? Without this information, the statistical results are incomplete. It was also not possible to compute the maximal velocity allowed by joystick control, since for Eqn. 1.9 not just the displacement x and the time constant is required, but also the trial duration T, which is not reported. One can only guess from Fig. 1D that vmax is about 50 cm/s for tau=0.6 s and therefore the average T is assumed to be around 8.5 s.

5) Results: information that would be useful is not reported. On page 6 it is mentioned that the "effect of control dynamics must be due to either differences in travel duration or velocity profiles", it is then stated that both are "unlikely", but no results are given. It turns out that in the supplementary Figure 4A the correlation between time constant and duration/velocity is shown, and apparently the correlation with duration is significant (but small) in the majority of cases. Why is that not discussed in the results section? Other results are also not reported, for example, what was the slope of the dependence between time constant and error? Why is the actual control signal, the joystick command, not shown and analyzed?

Reviewer #3:

This is an outstanding work from the lab of Dr. Stains establishing rapid post-translational regulation of sclerostin, a robust inhibitor of bone formation. They carefully and clearly establish that sclerostin is rapidly degraded by lysosomes in response to mechanical loading, and further link lysosomal abnormalities, using Gaucher iPSCs, to sclerostin levels.

Reviewer #3:

In this work, Feilong and colleagues use Human Connectome Project fMRI data to investigate the degree to which the strength of functional connectivity is predictive of general intelligence, and the degree to which that predictive power is improved using the hyperalignment procedures their lab has previously developed. I am broadly very supportive of the goals of improving prediction of individual behavioral differences via improved, functionally-based cross-subject registration, and I have always felt that the hyperalignment procedure is one of the most promising approaches for improving cross-subject functional registration. Overall I feel that this paper is an important next step in the development and maturation of the hyperalignment technique.

However, I do have two significant concerns with the predictive modeling presented in this work. I note that I am not an expert in these techniques, so these concerns may be due to my own ignorance; however, I would like to see the authors at least better explain these issues to non-experts like myself.

First, the authors employed a leave-one-family-out cross-validation scheme for their predictive modeling. My understanding is that the field has generally moved away from leave-one-out or leave-few-out cross-validation, as that approach consistently overestimates the predictive power of generated models. The HCP is a large dataset. Can the authors employ a more robust approach of using fully split halves?

Second, the authors make the claim that fine-grained (vertex-wise) connectivity has substantially better predictive power than coarse-grained (parcel-wise) connectivity, based on the variance in intelligence explained by the predictive models. However, the models based on fine-grained connectivity also have many, many more variables being used to make the prediction. Is this not a confound?

Reviewer #3:

The manuscript "High-quality carnivore genomes from roadkill samples enable species delimitation in aardwolf and bat-eared fox" is mostly well written and demonstrates an interesting and useful method for sequencing genomes from low-quality samples. They also provide a comprehensive overview of the state of genomics across the Carnivora clade, with some improved species/subspecies designations. I think the work is of broad interest. The analyses are mostly clear and I think a few additional analyses and small improvements could be made prior to publication, but otherwise have no issues.

The additional analyses/clarification I would recommend regards the Genetic differentiation estimate: This is a really interesting statistic! For some of the species you have multiple individuals it seems? Can you explain this a little more in the text. I am just not entirely convinced that the statistic is robust, but I think it would be with a few more analyses. My concern is primarily due to having only two individuals in some of your comparisons, because of population structure/relatedness the random regions you sample could have correlated histories. I think this could be addressed by varying window sizes and replicates across comparisons where you have multiple individuals for both the intraspecific and interspecific calculations.

Reviewer #3:

In the manuscript by Kim et al., show that, beyond its roles of preventing somatic differentiation in the germline of embryos, Zn-finger protein PIE-1 also functions in the adult germline, where it is both SUMOylated as well as interacts with the SUMO conjugating machinery and promotes SUMOylation of protein targets. They identify HDA-1 as a target of PIE-1-induced SUMOylation. Here too, I find the claims interesting, however data is sometimes missing or does not fully support the claims.

Main concerns:

1) A key claim of novelty over previously proposed "glue" functions of SUMO is based on the fact that they find that temporally regulated SUMOylation of a very specific residue in a specific protein is affecting protein activity: The observation that "SUMOylation of HDA-1 only appears to regulate its functions in the adult germline" and not in the embryo together with the finding that "other co-factors such as MEP-1 are SUMOylated more broadly, these findings imply that SUMOylation in the context of these chromatin remodeling complexes, does not merely function as a SUMO-glue (Matunis et al., 2006) but rather has specificity depending on which components of the complex are modified and/or when."

I find this claim poorly supported by the data. In fact, I find that the data supports that multiple SUMOylations contribute to formation of larger complexes: The His-SUMO IP (Fig 2B) brings down far more un-SUMOylated HDA-1 than SUMOylated. This argues for the presence of large complexes with different factors being SUMOylated and many bringing down unmodified HDA-1. The chromatography experiments (Fig 3B-C) also provide hits that are in complex and not direct interactors. Finally, HDA-1 SUMOylation is indicated to regulate MEP-1 interaction with numerous factors (Fig 3D). If all these factors are in one complex, it is hard to imagine how a single SUMO residue would mediate all of these simultaneously. It is quite likely (and not tested) that loss of HDA-1 SUMOylation leads to (partial?) dissociation of a large complex, rather than loss of individual interactions with the SUMO residue of HDA-1. Unlike claimed by the authors, there is no evidence that the "activity" of HDA-1 is regulated by SUMO modification.

2) Based on loss of MEP-1/HDA-1 interaction upon pie-1 RNAi and smo-1 RNAi (Fig 4B), the authors conclude that "SUMOylation of PIE-1 promotes the interaction of HDA-1 with MEP-1 in the adult germline".

The evidence that it is PEI-1 SUMOylation that is affecting MEP-1/HDA-1 interaction is fairly weak. In fact, based on Fig 4A, MEP-1 and HDA-1 interact without expression of PIE-1, and in PIE-1 K68R (sumoylation-deficient), although due to poor labeling of the panel it is not clear whether lane 1 and 4 refer to the WT pie-1 locus without tag or lack of pie-1.

In 4B the HDA-1 band that is present in L4440 but not in pie-1 or smo-1 RNAi is very faint, and in our experience such weak signal is not linear i.e., bands can disappear or appear depending on the exposure. Importantly, according to the data, seemingly unmodified HDA-1 immunoprecipitated with MEP-1 (Fig 4B). This data contradicts the authors' claim that "These findings suggest that in the adult germline only a small fraction of the HDA-1 protein pool, likely only those molecules that are SUMOylated, can be recruited by MEP-1 for the assembly of a functional NURD complex".

Furthermore, the fact that pie-1 and smo-1 depletion eliminate the interaction between HDA-1/MEP1 doesn't mean that the SUMOylation of pie-1 specifically is required for the interaction: perhaps un-SUMOylated pie1, and SUMOylation of something else, are both necessary for the interaction. The authors show that MEP-1 is also SUMOylated (Fig3C). When IP-ing GFP-MEP-1, they precipitate all its modified forms and associated factors. One alternative possibility for why smo-1 RNAi abolishes MEP-1/HDA-1 interaction is that MEP-1 SUMOylation is needed for interaction with HDA-1 (independently of pie-1). (On a side note, why are the authors not including MEP-1 SUMOylation in the model?)

3) On page 13 the authors write: "These findings suggest that SUMOylation of PIE-1 on K68 enhances its ability to activate HDA-1 in the adult germline" and "We have shown that PIE-1 is also expressed in the adult germline where it engages the Krüppel-type zinc finger protein MEP-1 and the SUMO-conjugating machinery and functions to promote the SUMOylation and activation of the type 1 HDAC, HDA-1 (Figure 6)". Activation of HDA-1 is misleading and was never tested. If not performing in vitro assays for HDAC activity, the authors at least need to look at whether pie loss (degron) leads to acetylation of genomic HDA-1 targets and whether it affects HDA-1 (and/or MEP-1) recruitment to these sites. This could be done by ChIP-seq of HDA-1 and H3K9ac in WT and pie-1 degron animals.

Reviewer #3:

This manuscript by Kim et al. describes a role of SUMOylation in Argonaute-directed transcriptional silencing in C. elegans. The authors found that SUMOylation of the histone deacetylase HDA-1 promotes its interaction with both the Argonaute target recognition complex as well as the chromatin remodeling NuRD complex. This enables initiation of target silencing. Impaired SUMOylation of HDA-1 leads to loss of interactions with several protein complexes, reduced silencing of piRNA targets, and reduced brood size. While the findings and claims are interesting, some of the novelty is overemphasized and some of the claims are not fully supported by the data.

Main concerns:

1) The importance of HDA-1 SUMOylation for transcriptional repression. The title "HDAC1 SUMOylation promotes Argonaute directed transcriptional silencing in C. elegans" implies a central role of SUMOylation in piRNA-mediated transcriptional silencing. The Argonaute HRDE-1/WAGO-9 targets countless transposons as shown previously and also in this manuscript (Fig S3), and so do the HDA-1 degron and Ubc9 mutant, indicating that histone deacetylation and protein SUMOylation are essential processes in TE silencing. However, the HDA-1 SUMOylation mutant (KKRR) only slightly affects 6 TE families (Fig S3), indicating that SUMOylation of HDA-1 might not be a key mediator of this process. Furthermore, the authors write that "Our findings suggest how SUMOylation of HDAC1 promotes the recruitment and assembly of an Argonaute-guided chromatin remodeling complex to orchestrate de novo gene silencing in the C. elegans germline.", but then they also state that "Comparison with mRNA sequencing data from auxin-treated degron::hda-1 animals revealed an even more extensive overlap with Piwi pathway mutants (Figure S2B), indicating that HDA-1 also promotes target silencing independently of HDA-1 SUMOylation." Based on their results and their own interpretations, I find that the importance of HDA-1 SUMOylation in piRNA-dependent transcriptional silencing is overemphasized.

Additionally, the model (Fig 7) implies that for initiation of silencing WAGO recruits HDA-1 to targets. This should be tested by analyzing HDA-1 distribution over WAGO targets in WT and upon loss of WAGO.

2) The mechanistic role of HDA-1 SUMOylation. On page 17 (amongst other places) the authors claim that "The SUMOylation of HDA-1 promotes its activity, while also promoting physical interactions with other components of a germline nucleosome-remodeling histone deacetylase (NuRD) complex, as well as the nuclear Argonaute HRDE-1/WAGO-9 and the heterochromatin protein HPL-2 (HP1)".

-Regarding activity: Loss of deacetylation/silencing in the SUMO mutant might be due to loss of enzymatic activity, but it might also be due to defects in recruitment/complex formation. There is no data that proves altered enzymatic activity. In fact, Fig 6 indicates SUMO-dependent interaction of WAGO-9 with HDA-1, implying that recruitment is affected. To distinguish between activity and recruitment, at the very least, the authors would need to show that HDA-1 localization to its genomic targets is unaltered upon mutating its SUMOylation site (ChIP-seq of wt and KKRR mutant), while H3K9ac is increased (K9ac ChIP-seq in wt and KKRR mutant) in the mutant. This, in combination with HDA-1 localization in wt and WAGO-9 loss would imply whether complex formation to recruit HDA-1 or HDA-1 enzymatic activity is mostly affected by SUMOylation.

-Regarding physical interactions: Fig 3D shows that if we fuse a SUMO residue to HDA-1, it will interact with MEP-1, while SUMOylation deficient HDA-1 mutant doesn't interact. However, for the WT HDA-1 control, we only see unSUMOylated protein interacting with MEP-1. Furthermore, in the MEP-1 IPs of samples that should contain SUMO-fused HDA-1, the authors detect a lot of "cleaved", unSUMOylated HDA-1. Unless cleavage happened after IP, during elution (unlikely, and there is "cleaved" HDA-1 in the inputs), these findings argue that the interaction with MEP-1 is not mediated by HDA-1 SUMOylation. An interaction between MEP-1 and unmodified HDA-1 is also shown in the accompanying manuscript, which appears to be dependent on Pie-1 SUMOylation. Thus, SUMOylation of HDA-1 alone seems unlikely to be the major factor necessary for silencing complex assembly. (as a side question: Does the protease inhibitor cocktail used inhibit de-SUMOylation enzymes? I am concerned that deSUMOylating enzymes might compromise some result interpretations.)

-Regarding functional relevance of HDA-1 acetylation: On pages 12/13 authors claim that because "HDA-1(KKRR) animals and mep-1-depleted worms revealed dramatically higher levels of H3K9Ac compared to wild-type" and "HDA-1, LET-418/Mi-2, and MEP-1 bind heterochromatic", "SUMOylation of HDA-1 appears to drive formation or maintenance of germline heterochromatin regions of the genome." These correlations do not prove function. The authors have performed H3K9me2 (although not H3K9-ac) ChIP-seq in WT, KKRR mutant and HDA-1 degron worms, yet do not analyze globally whether acetylation is lost on genes that are affected (change in RNA-seq vs. change in K9me2 or acetyl). To support the claim that SUMOylation of HDA-1 drives deacetylation and heterochromatin formation, it would be important to show changes in H3K9Ac levels (or other acetyl marks) and potentially NuRD component occupancy between control and HDA-1 SUMOylation-deficient animals at specific targets (i.e. genes derepressed upon loss of SUMOylation identified in RNA-seq, and the reporter locus).

3) The authors claim (p17) that "initiation of transcriptional silencing requires SUMOylation of conserved C-terminal lysine residues in the type-1 histone deacetylase HDA-1". I do not see any supporting data that has separately looked at formation/initiation and maintenance of silencing (a technically challenging experiment).

4) The authors repeatedly claim that gei-17 does not play a role in piRNA target silencing, based on loss of gei-17 not affecting the piRNA reporter (Fig 1B). At the same time, they claim that pie-1 plays a role, even though it likewise does not affect the piRNA reporter (it affects the reporter only in F3; data on gei-17 effect in F3 is not present). In the accompanying paper, the authors show that while gei-17 loss by itself causes only moderate effect on extra intestine cells, combined with Pie-1 loss the effect is more severe than when Pie-1 loss is combined with Ubc9 or smo loss. This to me indicates an important role of gei-17 in inhibiting differentiation of germline stem cells to somatic tissues, but these effects are likely synergistic and thus masked by Pie-1. Individually neither Gei-17 nor Pie-1 show an effect on piRNA reporter in P0, but to confirm lack of synergy, their effects should be tested together. Although possible, the present data is insufficient to rule out gei-17 involvement.

Reviewer #3:

In this manuscript, Soucy et al. describe a new technique that involves a 3D co-culture system that allows the analysis of the regulation of the sympathetic adrenomedullary system. The data demonstrate the advantage of such compartmentalized 3D systems relative to the 2 D system for long-term studies. The findings also show the usefulness of this system to understand the control by preganglionic sympathetic neurons of catecholamines released by the adrenal gland cells.

The main concern with the work relates to the uncertain physiological relevance of the co-culture system developed by the authors. Although I appreciate the utility of such reductionist techniques to understand how preganglionic sympathetic neurons regulate catecholamines released by the adrenal gland cells, this is too removed from a physiological setting.

1) It is difficult to judge the level of novelty of the MPS technique reported in this manuscript relative to what is in the previous paper (Ref 36) which is not available.

2) The innervation of tissues including heart and adrenal gland is highly specific. In addition to the circulating catecholamines secreted by the adrenal glands, cardiomyocytes are tightly controlled by direct innervation. Thus, whether co-culturing PNS with other cells mimic what happens in vivo is not clear.

3) The number of AMMCs displayed in figure 2B seems minimal as only very few cells were stained with cardiomyocyte markers. It would be interesting to know how many of these AMMCs receive innervation (Fig. 3E).

4) It is not clear how primary cardiomyocytes were exposed to the catecholamines emanating from the AMMCs? Were these co-cultured or were the cardiomyocytes exposed to the media of AMMCs?

5) Do the "n" in each figure represent cells or experiments (repeats)?

6) There is no description of the method used to quantify the immunofluorescent signal.

7) The Introduction is too long. It can easily be shortened to focus on the literature related to the topic.

Reviewer #3:

Lee and Daunizeau formulate a model of the effects of mental effort on the precision and mode of value representations during value-based decision-making. The model describes how optimal levels of effort can be determined from initial estimates of precision and relative value difference between competing alternatives, accounting for the subjective cost of incremental effort investment, as well as its impact on precision and value differences. This relatively simple model is impressive in its apparent ability to reproduce qualitative patterns across diverse data including choices, RTs, choice confidence ratings, subjective effort, and choice-induced changes in relative preferences successfully. The model also appears well-motivated, well-reasoned, and well-formulated.

I have two sets of concerns, my first set relates to model fitting and validation. The model appears to do fairly well in predicting aggregate, group-level data, but does it predict subject-level data? Or, does it sometimes make unrealistic predictions when fitting to individual subjects? The Authors should provide evidence of whether it can or cannot describe subject level choices, confidence ratings, subjective effort, etc.

Also, I think the Authors should do more to demonstrate that their model is an advance on simpler variants. The closest thing to model comparison is an exercise where the authors show that, relative to when their model is fit to random data, their model explains more variance in dependent variables when fit to real data. This exercise uses a straw man as a baseline because almost any model which systematically relates independent variables to dependent variables would explain more variance when fit to real data than to data for which, by definition, independent and dependent variables do not share variance. It would be more useful to know whether (and if so, how much) their model explains data better, than, e.g. a model with where effort only affects precision (beta efficacy), or a model in which effort only impacts value mode (gamma efficacy). Since the Authors pit their model against evidence accumulation models, it would be yet more useful to ask whether their data predicts these diverse data better than a standard evidence accumulation model variants.

My second set of concerns are regarding the assumed effect of mental effort on the mode of subjective values. First, is it reasonable to assume that variance would increase as a linear function of resource allocation? It seems to me that variance might increase initially, but then each increment of resources would add diminishing variance to the mode since, e.g., new mnesic evidence should tend to follow old mnesic evidence. How sensitive are model predictions to this assumption? What about if each increment of resources added to variance in an exponentially decreasing fashion? Also, what about anchoring biases? Because anchoring biases suggest that we estimate things with reference to other value cues, should we always expect that additional resources increase the expected value difference, or might additional effort actually yield smaller value differences over time? If we relax this assumption, how does this impact model predictions?

Reviewer #3:

The results of this study suggest that maternal loss alters the HPA stress axis in wild chimpanzees, but these effects are transient and are not evident later in life.

Overall the study is the result of much careful fieldwork. The number of cortisol samples is impressive and these are robustly analysed. The conclusions are carefully and thoroughly discussed.

I have very few comments, in part because I am not a specialist in stress hormones and so cannot fully assess the laboratory analysis or interpretation, but in part because my view is that this is a high-quality thorough study and a well-written manuscript.

My only major point is that I am aware that measurement of cortisol is difficult in the wild. It is possible to inadvertently measure metabolites other than cortisol, and the most robust way to measure cortisol is using a challenge and subsequent measurements. While I cannot adequately assess this aspect of the manuscript, I think it is important that the other reviewers/editor ensure the hormone measurements are appropriate.

Reviewer #3:

General assessment:

This paper applies a sophisticated psychophysical paradigm to assess the effect of prior choices on perceptual decisions in a group of 17 high functioning (but not mild cases) children and teenagers (8-17 years) with ASD. Using a model that is assumed to dissociate the contribution of prior stimuli and choices, the study found a strong effect of prior choices not stimuli, which is stronger in ASD than controls. Similar results from another data set are also reported. There was no convincing evidence found for a correlation between the effect of the priors and the ASD severity.

Overall, this is an impressive study with a sophisticated paradigm, elaborate data analysis, ASD participants who were tested on a large battery, in-depth analysis of the literature with interesting insights, convincing results (but see below) and a well written manuscript.

Major issues:

1) The finding from the model that the prior stimuli did not have a positive impact (and even negative) on the decision bias is counter-intuitive and needs explanation (I apologize if there is one and I missed it). There were typically 5 prior trials, ~4 of them on one side, e.g. right, resulting in a higher rate of right presses on the test (because the test was unbiased, and the results showed a bias). Assuming the prior trials were mostly replied correctly, there should be a correlation between the stimuli and the choices. I see 2 possible reasons why the model produced negative weights - one is that indeed the choices were different from the stimuli, in which case we need to know the performance of the participants on the prior trials (which would be useful anyway). The other possibility is that the choices for the model were binary and the stimuli were continuous. If the stimuli had been coded as binary, it would have been difficult to dissociate between the stimuli and the choices. In this case, the conclusion should be that the prior stimulus laterality could have impacted the test choices, but not their magnitude. This issue should be explained in the text.

2) The performance on the test trials staircase procedure is not reported, only the PSE difference. It would be useful to know if the groups differed on this, as the example psychometric curves shown seem shallower in ASD. Biases are likely to push the staircase procedure to higher laterality discrimination thresholds. I suspect (but without proof) that worse performance (more errors) on the staircase procedure may amplify (but not create) the bias. It would be useful to show the performance data and discuss this issue.

3) The paradigm used is quite complex and complex paradigms are more difficult to fully understand, so I wonder about the justification for it. Why is it better or different from testing SDT shift of criterion by change in target probability? For example, in a Yes/No experiment for contrast detection set around 70% correct, the criterion may shift when there are more Yes or No trials. What would the authors expect in such an experiment? It would be useful to discuss this for the wondering reader.

4) About the interpretation: the word "perseveration", i.e. a tendency to repeat the last key or recent keys is not mentioned. The authors conducted a "response invariant" experiment which showed significant but much smaller biases (Figure 7). Are these significantly smaller than the 1st experiment (as seems from the plots)? If so, one cannot rule out a major contribution of repeating the recent keys, i.e. perseveration. It would be useful to see the raw data in this case, e.g. what is the %trials of pressing right when the priors were biased to the right. My understanding is that it must be high given that the staircase was symmetric (50/50 trials on left and right) and that a bias emerged from the data.

5) I wonder if the data could be analyzed to reveal the different contribution of preceding trials, i.e. the details of the serial dependency. Currently, all previous trials are treated equal in the model, but their contribution is not necessarily equal.

Reviewer #3:

In this paper the authors have developed a system to simultaneously generate two-, three- and four-photon fluorescence excitation from a single laser line and then proceed to apply this system to a number of turbid biological imaging applications to highlight its capabilities. Using a customised commercial La Vision BioTec Trimscope, they have incorporated a high powered fiber laser source with an Optical parametric amplifier and dispersion compensation to generate a either 1330nm or 1650nm laser lines with high peak pulse energies at low pulse repetition rates. They then compare the relative capabilities of each laser line in terms of number of fluorescence emission channels measured (skin tumour xenografts), fluorescence bleaching analysis and functional toxicity thresholds and fluorescence signal attenuation (excised murine bone).

Whilst the paper is well written, the concept of utilising high laser peak powers and at low repetition rates to generate 3PE and 4PE at spectral excitations at 1300nm and ~1650nm is not new and has been presented previously (Cheng et al. 2014), as referenced by the authors. The authors have however gone into more detail and presented a number of comparative excitation approaches to compare and contrast low-duty-cycle high pulse-energy infrared with the more common high-duty-cycle low pulse energy near-infrared alternative. The benefits of higher order multiphoton microscopy when combined with higher wavelength excitation allows deeper imaging and more localised fluorescence excitation with reduced phototoxic and photobleaching effects per excitation pulse. One of the major issues associated with generating 4PE is that since higher pulse energy is required, this further reduces the repetition rate of the laser source, in order to reduce the average laser power in order to avoid sample heating effects. This in turn leads to much longer acquisitions and is limited by the fluorophore saturation particularly since they are using single beam excitation.

Major comments:

1) It seems as though when you take into consideration duty cycles, fluorescence saturation, water absorption effects and longer acquisition times, which lead to greater phototoxicity, 4-PE at 1700nm excitation is not appropriate for most dynamic biological applications where acquisition speed and/or continued image acquisitions are the key factors. Could the authors comment on this?

2) How long does it take to acquire a single frame with four-photon excitation at 1700nm? In none of the data sets was frame time mentioned in particular when acquired 3D data sets. Can the authors ensure that these times are mentioned both in the main text and the figures containing images.

3) In line 131 and figure 3d the authors present data showing relative axial resolution measurements. Are these features measured diffraction limited and how do they know? They are clearly not measuring like for like structures (different fluorescent species) so do not think this can be used as a measure of resolution. Can the author provide other resolution measurements?

4) In line 140 - 142 the authors present data showing the advantages of THG at 1650nm over other excitation lines. Aside from the excitation wavelength could this data be explained by the greater absorption and scattering at the emission wavelengths generated at these laser lines?

5) In figure 3A and 3C the SNR for 1650nm increases whilst for 1300nm and 1180 excitation this decreases. Is this simply due to more of the exciting fluorophore species residing deeper into the tissue?

Reviewer #3:

General Assessment:

The manuscript is well written and the methods are sound. The strengths of this manuscript are that this study is the first to systematically perform detailed electrophysiological measurements on inhibitory interneurons (INTs), in particular RC and non-RC INTs using the SOD1 mouse model for ALS. It is very interesting that they showed a dichotomy between reduced excitability in RC neurons (which could lead to an indirect increase in overall excitability of MNs) and non-RC INTs, which actually showed an increase in excitability which would have the opposite effect on MNs.

Main comments:

1) Most electrophysiological studies have focused on motor neurons and showed that they become hyperexcitable at very young ages, although there is controversy as to whether the hyperexcitability persists and is causative or compensatory to disease progression.

2) The dichotomy observed between RC and non-RC Inhibitory neurons is interesting. Given that many of the glycinergic non-RC interneurons are Ia-inhibitory interneurons responsible for reciprocal inhibition, their effects on the target motor neurons have opposite effects on MN excitability. At this point it is mere speculation as to how these changes actually exacerbate the progression of the disease and effects circuit function.

3) This paper is mainly descriptive with no specific hypothesis other that what has been discuss often in the literature: Motor neuron hyperexcitability occurs from intrinsic alterations in MN ion channels, increased excitatory synaptic activity, or a decrease in inhibitory activity or all of the above. Although the authors are most likely the first to demonstrate changes in inhibitory interneuron excitability with direct electrophysiological recordings, it is unlikely that these findings will significantly move the field forward presently. The authors suggest that biomarkers could be developed, this is just a broad statement without concrete proposal for implementation. It would be useful to show a specific target that could be modified pharmacologically in animals over time to see if this changes the progression/survivability of the ALS animals.

4) Furthermore, the functional significance of early hyperexcitability as either a cause or compensation of ALS is controversial at present. Numerous studies have addressed hyperexcitability but yet we are still far from understanding the bases for this disease and one cannot help question whether this avenue of investigation is fruitful.

5) Does this change in interneuron excitability and the dichotomy between RC and non-RC demonstrated persist over the course of the disease? How relevant are these changes to disease progression?

6) It will be necessary to use other animal models available for comparison since SOD1, although historically a well-studied mouse model, is an ectopic over expresser, and is not the predominate mechanism for ALS in humans. There are others probably more pertinent models, ie. C9ORF72. Whether such changes in inhibitory interneurons occur in those other models and in humans remains to be determined.

Reviewer #3:

The authors are to be commended for the effort put into careful experimental design and clear presentation of methods and results.

My main concern with the manuscript is that the claim about their specific polymerase gene being "ultraconserved" is not backed up with their own data or by citations from the literature. If the gene sequence was ultra-conserved, I wouldn't have expected the authors to be able to do so much recoding of the gene without fitness consequences. Furthermore, it is clear that homozyogous-viable NHEJ mutations did develop in the experiment. Without explanation, this seems to be a fatal flaw in the design.

This manuscript describes a modification of the general homing gene drive concept by use of a split drive system that increases the frequency of a recoded polymerase gene that replaces a cleavage susceptible, naturally occurring, haplosufficient, conserved polymerase gene. This approach is taken in order to limit the evolution of cleavage resistance in the naturally occurring gene.

I am not convinced that the research presented achieves the intended goals. I did a quick look for literature on the "ultraconserved" polymerase pol-y35 gene and could find none. I am not sure if the conservation is at the DNA sequence level or at the amino acid level. If at the amino acid level, then it makes sense that resistance alleles can form at the DNA level that don't impact the protein at all. Figure 2a shows the 22 and 27 recoded nucleotides for the two guide RNA sites. The authors say that these changes to the sequences didn't seem to impede fitness. Did the authors try many other recodings and finally decide on these because all others caused loss of fitness, or is it just that this gene is robust to substitutions even though the protein is conserved.

Figure 4C shows that the frequency of flies with at least one copy of the pol-y35home R1 increased from about 25% to about 50% between the parental and F0 generation when there was no Cas9 present. As long as the transgenic males were competitive with the wild flies this makes sense because the released flies were homozygous for that allele and the offspring should all have inherited one copy of the gene. What doesn't make sense is that when the work was done with all flies harboring the Cas9, the pol-y35home R1 increased less than in the former case, from the parental to generation F0, the frequency of flies with the pol-y35home R1. In some replicates the frequency of such flies didn't increase at all. It should be noted that the parents were always homozygous. This certainly indicates a fitness cost to the flies with a combination of Cas9 and the homing construct.

In this same figure, results from the model are plotted. It seems like the model assumes no fitness cost because it shows an exact increase from 25% to 50% flies carrying at least one copy of the pol-y35home R1 theoretical construct. In later generations the experimental results outperform the model. Presumably, this model is used to construct figure 6. This mismatch needs to be addressed in the manuscript.

The fact that in all three replicates of the experiment without Cas9, the F0 is above 50% indicates that something else may be going on that is unrelated to gene drive. It could be due to heterosis between the two slightly different strains of flies. When wildtype males mate with wildtype females, the offspring are more inbred than when a transgenic male mates with a wildtype female. Just a hypothesis.

Reviewer #3

This manuscript by Beier et al. has used an impressive array of genetically modified mouse lines to study, which retinal circuits are responsible for driving the pupillary light reflex (PLR). These mouse lines are validated by direct electrophysiological recordings from rods, to rod bipolar cells, to ON and OFF cone bipolar cells. The manuscript makes two key conclusions based on measurements of PLR from darkness to 100 lux and 1 lux light steps: 1) the ON but not the OFF pathways drive PLR, 2) PLR relies on the most sensitive rod pathway - the primary rod pathway. My main concern is that the data shown in the paper does not uniquely support these two key conclusions. There are many issues, some of which may be fixed by better explanations, some of which may require more complete measurements. I outline my main concerns below:

1) The manuscript uses an incoherent terminology of the retinal pathways. For example, the beginning of the second paragraph of the introduction states that the ON and OFF pathways split in the first synapse, which is not true, for example, for the primary rod pathway (rod bipolar pathway). The latter segments of the same paragraph lay out more clearly the conventional definition of the primary, secondary and tertiary rod pathways. In short, it would be important to use a coherent and conventional terminology of the retinal pathways and relate the experiments and conclusions to these. It would also be important to correlate the used stimuli to the light levels defined to drive signals across different retinal pathways in image forming vision (see Grimes et al. 2014 & Grimes et al. 2018). Now that the light levels for physiological studies are expressed in R / rod (see Supplementary Table), whereas lux are used as units for PLR. Comparison to the previous literature would require a unified intensity space (preferentially Rs or both luxes and Rs). It would also be important to relate the sensitivity of the primary rod pathway (as the authors claim is driving the PLR) to the signaling levels (extremely low light levels, <10 R/rod/sec) where this pathway is supposedly driving image forming vision (Murphy & Rieke, 2006). It seems that the current PLR experiments probe much higher light levels than these papers in relation to the primary rod pathway. A wider stimulus space should be tested and/or at least a clear explanation would be needed for the choices made.

2) One of the two main conclusions of the paper is that the retinal ON pathway drives the PLR and the OFF pathways do not contribute to the PLR. The authors state (see abstract): "The OFF pathway, which mirrors the ON pathway in image forming vision, plays no role in the PLR". The data in Figs. 2A & B and 3 A & B indeed give strong support for the notion that light steps from darkness to 100 lux and 1 lux drive light responses through the ON pathway. However, this finding is not in conflict with the image forming vision. In fact, both the classic papers (Schiller, 1982, photopic ) as well as more recent results (Smeds et al. 2019; scotopic) support the notion that light increments are coded by the ON pathway. Now the circuits controlling PLR seem to fall exactly in this picture. However, the classic papers based on image forming vision (see e.g. Schiller, 1992) propose that the OFF pathways would drive light decrement stimuli. To justify the conclusion that "OFF pathways do not contribute to PLR" the authors should test a wider stimulus space including light decrements across scotopic and photopic light levels or limit their conclusions to light increments and in line with current notion for image forming vision. The reason that OFF pathways do not play a role may just reflect a limitation in the stimulus space probed.

3) The authors appear to ignore that the division into ON and OFF pathways occurs only after the AII cells along the primary rod pathway. The fact that Cx36 KO mice exhibit a normal PLR thus seems to invalidate the main claim of the paper that the primary ON pathway drives the PLR. The authors state: "These results imply that either the rod to rod bipolar cell pathway, independent of the AII ON pathway, is capable of driving pupil constriction or that cones are playing a role". Both of these conclusions are in contradiction with the main conclusion that the primary rod pathway as defined conventionally would be the underlying mechanism. If indeed cones are driving the PLR in Cx36 KO mice, that would be in contradiction with the previous literature (Keenan et al. 2016). It would be important to test this perhaps by using a different mouse line allowing to eliminate the cone contribution. Alternatively, showing data on Cx36 KO mice at lower light levels could help but this dataset is missing from the Fig. 3. Similarly, the Cone Cx36 KO dataset seems too sparse (n = 3) to justify the current conclusions in Fig. 3D and for some reason, the corresponding data trace is missing completely from Fig. 3C. In fact, the authors as they speculate might have uncovered (see Discussion) an entirely novel mechanism controlling the PLR. However, this now has been left untested even if it could be the most interesting new discovery if properly tested/shown.

Reviewer #3:

The manuscript by Shi and colleagues delineates an approach for labeling newly synthesized lipids thereby providing a method to examine how lipids move throughout the cell. The premise of this technical approach is that fluorescently labeled fatty acids are fed to a cell in the presence of another lipid which will incorporate the fluorescent acyl tail using the endogenous cellular acyltransferases. Cellular imaging is paired with this approach to show the subcellular accumulation of the lipid. As presented, the data are intriguing, but there are some concerns and questions about the technique that limits the interpretation of the data and could impact the overall utility of this approach. The authors should provide the additional requested data, and resolve the issues raised below to increase confidence that this labeling approach allows for the monitoring of physiologic lipid trafficking pathways.

Specific concerns and questions are delineated below.

1) The authors initially exploit the remodeling of PLs as described in figure 1a. This involves the addition of lyso-PL and NBD-labeled palmitoyl-CoA. The authors imply from their schematic in Fig 1a that they are using lyso-PLs that are being remodeled at the sn1 position by NBD-labeled palmitoyl-CoA. Unless I am missing something, lyso-PA and other related lyso-PLs are generally remodeled at the sn2 position. Additionally, there is specificity for PUFAs acylation to the lyso-PL. So I am a bit confused about the enzymes that are working in this system. I tried to determine which lyso-PLs that the authors are using, but the methods did not specify if they are using 1- or 2-lyso PLs. This should be clarified so that we can understand the enzymes the authors think are underlying the labeling reaction. On a minor, but related note, the lyso-PL in Figure 1a is missing an -OH group at the sn1 position.

2) The authors use a cell system where the cells are starved of lipids and other metabolites for 1 hour and then fed a large bolus of lipids as substrates. It appears that the cells can remodel and label some PLs under these conditions, but it is not clear to me that this represents physiologic labeling that can be used to track the de novo labeling and trafficking into subcellular compartments. Nor can it be used to draw strong conclusions about required trafficking or enzymatic pathways under normal conditions. What happens if labeling occurs in complete media or defined media? This might help to resolve this.

3) The labeling looks non-uniform in mitochondria as evidenced by the images in figure 2a. Why is the labeling only at the outer edge of the mito in these cells in this figure? What happens if labeling goes longer? Similarly, the authors quantify "30 cell images" or the like in the figures for Pearson correlations. How were the 30 cells selected, and since labeling across the mitochondria is not uniform, how were images selected? A much larger number of images scanned in an unbiased manner would increase confidence.

4) Likewise, what happens if the labeling is allowed to proceed beyond 15 min. Can the authors provide a 30 min and 1 hr image?

5) There are a number of conclusions drawn about specific pathways required for the trafficking of accumulation of labeled lipids. I realize that some of these studies are used as a specific proof-of-concept for the approach. However, there are many studies that go beyond proof-of-concept and draw conclusions about biology. Many of the studies are somewhat superficial and the conclusions reached by the authors should be tempered given that they have not deeply investigated this new biology.

Reviewer #3:

In this manuscript, Icke and colleagues show that the secreted protein CexE/Aap from entergotoxigenic E. coli is acylated at an N-terminal glycine and suggest that acylation is required for secretion via a Type I Aat secretion system to the cell's surface or into the environment. The key findings is the identification of an N-acyltransferase (AatD) encoded nearby cexE/aap and demonstration that this enzyme is required for acylation.

There is a concern about the novelty of the findings. The publication by Belmont-Monroy et al. (PLoS Pathogens, August 2020) cited by the authors is very similar to the current manuscript. That publication demonstrated that N-acylation of Aap (a CexE homolog) occurs at its N-terminal glycine (made available after signal peptide cleavage), that acylation is dependent on the acyltransferase AatD, that acylation is required for Aap secretion, and that N-terminal residues are sufficient for acylation of a heterologous protein (though this was poorly analyzed in that paper). Almost all of those findings are shown in this current manuscript by Icke et al., independently confirming the acylation reaction.

This Icke et al. study is well done and convincing on the AatD-dependent acylation of CexE/Aap. Overall, the same conclusions are drawn as Belmont-Monroy et al., 2020. The major new advance (not previously described) is the observation that the N-terminal glycine is required for N-acylation by AatD.

As described in my comments (below), the manuscript could be improved in a few instances by including key controls to support the conclusions. In other instances, broad conclusions are made from narrowly focused data and the text should be revised.

Major comments:

1) "To our knowledge this is the first report of enzyme mediated N-palmitoylation in nature". This statement is not correct. The lipoprotein N-acyltransferase Lnt (used as a reference for AatD analysis in this manuscript) performs N-palmitoylation (C16:0) in E. coli and distantly related bacteria such as mycobacteria/corynebacteria. See Jackowski & Rock 1986 (JBC 261,11328-11333), Hillman et al. 2011 (JBC 86, 27936-27946), Brulle et al. 2013 (BMC Microbiology 13, 223).

2) The conclusion that "we reveal a new function for acylation - protein secretion" is not fully supported. The authors do not directly show that the secreted CexE is acylated (Fig 2A) or that acylation is required for secretion. The use of 17 ODYA is innovative and could be used to show that secreted supernatant CexE is acylated. The CexE N-terminal substitution mutants that are not acylated (Fig 7C) could be used to test if acylation is required for secretion.

3) If the secreted CexE is acylated, some discussion is needed. How is the acylated form sometimes secreted into the aqueous environment but sometimes embedded in the outer membrane as shown in the model?

4) Can the authors show/detect CexE acylation in the native system that doesn't rely on overproduction of the CfaD transcription factor? Is the observed acylation physiological or a consequence of strong overexpression?

5) Claims of novelty in text should be altered following Belmont-Monroy et al., 2020.

Reviewer #3:

The manuscript named "Ex vivo observation of granulocyte activity during thrombus formation "submitted by Morozova and colleagues try to demonstrate the implication of deux different types of granulocytes in thrombus formation. Author study thrombus formation in anticoagulated whole blood from healthy and Wiskott-Aldrich patients in parallel-plate flow under collagen type I and low shear rate (100 s-1). They identified a CD66/CD11 cell population defined as granulocytes able to interact with growing thrombus. Two types of granulocytes were observed and differentiated with their fluorescent patterns: type A (uniform DiOC6 staining) and type B (cluster-like DiOc6 staining). Authors studied granulocytes behavior under several kinds of inflammation mediator. The manuscript should be improved, please see my following comments.

1) Authors should clarify the technical part of the manuscript and the figure 1, essentially the use of anticoagulant to perform follow chamber. It is not obvious which anticoagulant was used to performed flow chamber: citrate, heparin, hirudin. Does recalcification was performed in all experiments?

2) The authors should explain why the figure 1 demonstrates that granulocytes need free calcium ions to adhere to the growing thrombus. This is not the conclusion of figure 1. Moreover, all the growing thrombi seem different (more compact in citrate than with hirudin, w/o granulocyte in citrate and with granulocytes in hirudin) the authors should discuss this point.

3) This following sentence is confusing (last sentence of 3.1): “Hirudin- and heparin-anticoagulated blood was used in all further experiments because citrated blood recalcification causes local fibrin formation and platelet activation.” Platelets activation is essential to growing thrombus.

4) Author hypothesized that type B are more activated than type A essentially based on crawling and velocity cells. Could they do supplemental experiments to prove this point (increased of CD11 active form) and to differentiate neutrophils from eosinophils and basophils?

5) It will be great to perform a competition experiment to prove that platelets are interacting with granulocytes through CD11.

6) Did authors find NETs in this setting?

7) In all pictures platelets seem not well represented, only two and three platelets in figure 2. How the authors could be sure that granulocytes interact with platelets and not collagen?

8) Some platelets seem inactivated (round form) and annexin V positive. Could the authors discuss this point?

9) Concerning the last figure, it will be great to use healthy platelets and WAS granulocytes to conclude that crawling is altered.

Reviewer #3:

In this manuscript, Dempster et al. analysed the predictability of cell viability from baseline genomics and transcriptomics based features. They did a comprehensive analysis across feature and perturbation types, which gives a valuable contribution to the field. The main findings of the paper (gene expression based features outperform genomics based ones) are not necessarily new, but the authors also show the interpretability of gene expression based features, which clearly helps to place these machine learning (ML) models into biological context . This is especially important for the possible translatability, as small (low number of features), interpretable models are generally preferred over large, "black box" models.

The study is very nicely constructed both from machine learning and cancer biology perspective. My only major comments are regarding some (potential confounding) factors related to tissue-type and feature filtering.

Major comments:

1) A well known phenomenon on the field is the tissue-type specificity of drug sensitivity, which is a major confounding factor in several ML-based studies. The authors, absolutely correctly, use tissue-type as features in their models to overcome this problem. However, as RF models (individual trees) do not use all features at the same time, so it is possible that some genomics based models are not using information about tissue-type, even if tissue-type was selected in the 1,000 features. On the other side, for gene expression based models (based on the "tissue specificity of gene expression"), tissue-type information is probably always available. This could (partially) cause the better performance of gene expression features. Could the authors do some additional controls (e.g.: providing "multiple copies" of tissue-type features for genomics based models) to overcome this potential confounding factor?

2) The authors use a Pearson correlation filter (mainly) to decrease computational time. In Figure 4 (and also inFigure 2 - supplement 3) they show that in case of "combined" features, the features sets including gene expression based features had the best performance. When did they use the Pearson filter in case of combined features, before or after combining them? I.e. in case of expression + mutation, they selected the top 1,000 expression and top 1,000 mutation features, combined them and trained RF models with 2,000 features, or combined expression and mutation features, selected the top 1,000 features, and trained the models with them? If the later, it would be important to see how much of the different feature classes (e.g.: mutation and expression in my example) are included in the top 1,000 features. This is especially important, as Pearson correlation as a filter is probably more suitable for continuous (expression) than binary (mutation) features, so it is possible that the combined features use mostly expression based features. In this case, it is not so surprising that the performance of combined feature models are more close to expression based models.

Reviewer #3:

Three different anti-asprosin mAbs were produced and tested in different metabolic syndrome animal models. Beneficial effects were noted on body weight, food intake and blood glucose and insulin levels. The effects were modest, but seemed to be relevant to elevated aprosin levels, as the AB blocked the effects of adenoviral overexpression of the hormone. Some issues require attention:

1) Additional characterization of the aprosin neutralizing effect of the AB is required.. It will be helpful to show the endogenous free asprosin levels at different time points after a single or repeated mAb injection. This result is also important to tell whether this mAb will cause other immune responses and side effects that might confound interpretation of the results.

2) In Figure 3 (a, e, j) and Figure 4 (a, e, I, m). please show body weight to rule out the stress or side effects caused by virus injection. For DIO mice, 14 days IgG injection also caused weight loss; for db/db mice, IgG injection increased body weight. Please discuss.

3) Although adenovirus and AAV are widely used for in vivo protein overexpression, it is important to show here that endogenous asprosin levels were increased after virus injection and decreased after antibody neutralization.

4) In Figure 5, more data on liver weight, histology, etc. is required to support their conclusion on liver health. The current data from three different mice models are very contradictory, this can be caused by the side effect or off-target effect of this mAb.

5) In Figure 6, it is important to demonstrate the neutralizing effect of the mAbs.

Reviewer #3:

This paper shows that during a second-order conditioning (SOC) task, the representation of a conditioned outcome is represented in the lateral orbitofrontal cortex (lOFC). The BOLD signal in this region shows increased functional coupling with the amygdala for second-order conditioned stimuli that indirectly predict a negative outcome. The authors suggest these findings reflect a mechanism by which value is conferred to stimuli that were never paired with reinforcement.

The paper tackles an interesting question concerning the neural mechanisms that support second order conditioning. The task design includes relevant controls and, on the whole, the findings support the claims made by the authors. I have a few questions about interpretation of the data, but my main suggestion would be to revise the framing of the article. There are many previous studies that have investigated the mechanisms that support second order conditioning which are not always given due credit. I believe this paper would benefit from placing the hypotheses and findings more firmly within the context of previous literature.

Comments:

1) The authors test the hypothesis that CS2 is directly paired with a neural representation of the US. They state that this hypothesis 'has never been tested to date'. However, a number of studies have shown evidence for and against this hypothesis (for example: Wimmer and Shohamy 2012; Wang et al., 2020; Barron et al., 2020). Can the authors clarify how the hypothesis tested here differs from those investigated previously? In addition, it is not clear to me how the four potential mechanisms they propose are really distinct from each other?

2) Relatedly, given the authors use an SOC paradigm that differs from sensory preconditioning studies used by many previous authors, does the difference in task paradigm provide new insight? Do the authors expect the neural mechanism to be the same or different between their version of SOC and sensory preconditioning?

3) Why is the behavioural data in Figure 1F bimodal for CS1 and CS2? i.e. what does choice probability of 0 for CS2+ vs CS2- mean for a given subject?

4) To test the author's hypothesis, is it not necessary to assess evidence for US in response to CS2? They instead report reactivation of US in response to CS1 and for the PPI it is not clear to me how the authors distinguish between CS1 and CS2 given the temporal proximity in their presentation (Figure 1D).

5) For the PPI, is there a main effect of CS- and CS+ versus CSn in lOFC? If not, how does this affect interpretation of the PPI? On a separate note, is the effect reported in Figure 3 really in the hippocampus? Does it survive small volume correction using a hippocampal mask?

6) The following is stated as a premise: "To form an associative link between CS2 and US, the reinstated US patterns need to be projected from their cortical storage site to regions like amygdala and hippocampus, allowing for convergence of US and CS2 information." This potentially seems fair for the hippocampus, with added reference to relevant literature (e.g. publications from Shohamy and Preston labs), but in my opinion the jury is still out on this one. It is not clear to me why we necessarily expect amygdala here.

7) There are various strong statements that in my opinion need to be toned down in light of existing literature. For example, the paper claims this study is the first to show evidence for implicit inference. However, as far as I'm aware, Wimmer & Shohamy 2012 also found no evidence for explicit memory of stimulus-stimulus associations with no relationship between measures of explicit memory and decision bias. Similarly, the authors claim this paper is 'the only report so far of behavioral evidence for associative transfer of motivational value during human second-order conditioning', overlooking a large number of other studies that have shown similar behavioural effects.

Reviewer #3:

This manuscript examines data from the Young Adult Human Connectome Project's 900-subject release to compare both structural and functional connections between iso-eccentricity bands in striate cortex and the fronto-parietal, cingulo-opercular, and default mode networks. The authors find that central vision is most strongly connected to the fronto-parietal network, which is associated with attention, while the far periphery is more strongly connected to the default mode network. The questions asked in this manuscript are of considerable interest to the field, and this study has the potential to be impactful. However, substantial work is needed to make the methods and results sufficiently clear and reproducible to the reader.

Major Comments:

A major problem throughout this paper is that the authors have not been very careful in documenting their methods, what they are plotting, or how they are supporting their assertions. This is a major shortcoming of the work. I do not believe there is sufficient detail in this paper as is to reproduce the methods, nor was I able to understand what precisely was calculated in the statistical tests reported.

The amount of work that has been put into this project's quality control (at minimum, visual inspection and filtering of 900 MR images) is very impressive! This information should really be shared with the broader research community in order to make this manuscript more reproducible and in order to ensure that other researchers can simply use and cite the authors' efforts rather than repeating them. This could be as simple as a supplemental table or text-file that includes the subject IDs of those HCP subjects that were included in all analyses.

It should be crystal-clear from the Methods section whether the manuscript's data were collected or reanalyzed by the authors. My understanding is that all of this manuscript's analyzed data are from the HCP database. However, had I read only the "Data Acquisition" section I would have been left with the strong impression that the authors collected the data themselves using the same kind of scanner and the same analysis pipelines as the HCP. Unless this is the case, the opening sentence of this section should probably be something like "All data were acquired and preprocessed by the Human Connectome Project (Van Essen et al., 2013)" [10.1016/j.neuroimage.2012.02.018]. It may also be wise to reference the HCP in the Acknowledgements section. Further information: https://www.humanconnectome.org/study/hcp-young-adult/document/hcp-citations. This should apply equally to the data and the preprocessing methods-i.e., if the quality control mentioned in the above comment was performed by the HCP and not the authors, that should have been explicit.

P3, ❡6. This paragraph is critical to the methods but is not at all clear. In particular, the paragraph eventually describes seven eccentricity segments per subject, yet it does not explain what the eccentricity boundaries of these segments are, nor does Figure 2 show these segments. It isn't clear from the manuscript if these are ever used (rather than the 3 central/mid-peripheral/far-peripheral segments) or exclusively used.

In looking at Figure 4, my first and strongest impression is that the central connectivity is very similar to the far-peripheral connectivity, and the z-score differences are incredibly small. Additionally, the legend does not make the quantities plotted very clear (these are based on the averaged z-scores across subjects?) so I'm left wondering how to assess any sort of significance. I have a similar reaction to Figure 5. More help is needed to understand these results.

Given that this paper consists of a large analysis of a large existing dataset, it would be especially nice if the authors would make their source code and intermediate analysis files publicly available. Having access to the source code directly is virtually a requirement of making this kind of study reproducible and would mediate many of my concerns about the ambiguities of the methods.

Reviewer #3:

General assessment:

Antitermination (AT) is a widespread mechanism to regulate transcription and can be mediated by ANTAR domains which prevent the formation of the terminator hairpin by binding to and stabilising a dual hexaloop motif in the nascent RNA. In the submitted manuscript Walshe and coworkers address the molecular basis of this AT mechanism which is largely unknown. They report two crystal structures of the dimeric ANTAR protein EutV from E. faecialis, one of EutV alone and one in the presence of a 51 nt long RNA containing the dual hexaloop motif, and combine this structural data with biochemical and biophysical data.

The study

-Reveals structural rearrangements that occur upon RNA binding and provides molecular insights into the RNA binding mode

-Shows for the first time that a Met residue is obligatory for RNA binding

-Redefines the minimal ANTAR domain binding motif

-Suggests a new model for ANTAR-mediated AT

Thus, the study is a comprehensive work, the experiments are performed thoroughly, and the conclusions are supported by the data. The results are of interest to a broad audience, ranging from the field of transcription in all domains of life to protein:nucleic acid interactions in general.

However, the authors should address the following concerns:

1) p 5, lines 15-17: The interactions should be described more clearly, i.e. are the hydrogen bonds between main chain atoms or between side chains? Which atoms/functional groups are involved (e.g. carboxy group of sidechain of Glu161)

2) p 8, line 1-2: The SEC-MALS data indicates that the sample is not homogeneous and the authors suggest that this might be a concentration-dependent effect. This hypothesis is, however, not supported by the data. First, there is no information provided about the concentration used in the SEC run . Second, the SEC run was carried out on a S200 column. The experiment should be repeated on a S75 column which has a better resolution in the range of interest. Furthermore, the SEC runs should be performed with different concentrations to check if the oligomerization is indeed concentration-dependent and it could be used to check if the oligomerization is reversible (i.e. by collecting the "dimeric" form and re-run the solution and see if there is an equilibrium). Finally, as the authors discuss the dimerization behavior/mechanism, they might check if/how phosphorylation influences the oligomerization. These tests are important as this sample was used for the SPR experiments. If the sample, however, is not homogeneous, interpretation of the data might be compromised due to a mixture of different oligomeric states so that concentrations are not correct or a 1:1 binding model cannot be sued (most probably, the concentration of EutV is higher in the SPR experiments than in the SEC run and if there is concentration-dependent oligomerization this might be a significant issue).

3) p 8: the chronology of Fig. 2 does not correspond to the chronology of the panels mentioned in the text.

4) p 11, line 20: the authors state that G4 makes the only base specific interaction between the protein and the RNA hairpins. However, the details of the interactions are discussed only later in the manuscript so that this conclusion cannot be drawn at this stage. Thus, the author should present the interaction analysis earlier or adapt their argumentation (maybe by pointing to Fig. 3).

5) Fig. 3: The interaction network between RNA (bases) and the protein is a very important point in the manuscript. In order to emphasize that only one of the bases, G4, makes base-specific contacts is, most probably, thus responsible for sequence-specific read-out, a 2D representation of the interaction network should be provided as Figure Supplement. (e.g. using LigPlot)

6) p. 14: alanine mutagenesis. In order to confirm the importance of G4 the authors might substitute the base by another base and repeat the SPR measurements. Moreover, the quality of the protein samples should be checked (and data should ideally be provided as supplemental material), i.e. is the samples homogeneous (see comment on SEC runs) and are the samples free of nucleic acid contamination (how is the A260/A280?)

7) p. 14: EutV binding to P1 and P2 RNA tested by SPR: was the sample homogeneous ? (see comment above on SEC runs).

8) p 14: The authors should comment on the differences in the CD spectra in the region around 220 nm.

9) p 20, ,lines 14-23. G4 plays a critical role in sequence-specific recognition. This recognition mode is reminiscent of the mechanism an operon-specific transcription factor, RfaH, uses. Here, RNA polymerase pauses at a pause site and exposes the nontemplate strand, which forms a hairpin. This hairpin stabilizes the flipping-out of a base in the loop region and allows sequence-specific read-out. Similar to EutV, sequence-specific recognition relies on very few base-specific interaction. However, RfaH binds to DNA. Moreover, also the sigma factor uses a flipped-out residue for recognition, although applying a different mode of stabilization. Thus, a comparison of these recognition modes might be of interest.

10) p. 22: revised AT mechanism: The proposed model is reasonable and fully supported by the data. Is there a possibility to check the role of the two hairpins in vivo? I.e. if there is a possibility/assay to distinguish between recruitment and AT efficiency, the proposed model could be tested.

Reviewer #3:

This study shows how well mixed populations of yeast cells initially expressing both an anticompetitor toxin and resistance to it, first lose toxin production (because there is a cost but no benefit to toxin production when all cells are resistant) and then lose resistance (because there is a cost but no benefit to resistance when no cells produce toxin). Consequently, these evolved sensitive populations have lower fitness than their own toxin-producing (resurrected) ancestors, but only if the toxic ancestors are introduced at a high enough frequency, that is, there is positive frequency dependent selection. These results are quite intuitive and satisfying, and are well supported by rigorous experiments determining the causal mutations and their selective advantages both within intra-cellular populations of the virus, and between cells in the evolving populations. This was really nice, thorough, and interesting work. However the overall result is not really surprising, as much similar work has been done before (and is properly cited) in which three types of competitors show non-transitive pairwise fitness relationships.

The main claim to originality is that the three types here are generated sequentially by two rounds of mutation, natural selection, and replacement/fixation: that is, there is genealogical nontransitivity between ancestors and descendants, rather than just ecological nontransitivity between contemporary co-existing variants. This demonstrates an important principle: that natural selection can produce a decline in overall relative fitness in a lineage over multiple rounds of mutation and fixation. The only other reported example of this in experimental evolution is the work of Paquin and Adams (1983), but the authors here argue convincingly that the Paquin and Adams, lacking the benefit of sequencing to identify mutations and their frequencies, inadvertently competed ecological types that were co-exising in their evolving populations and had not fixed.

My only criticism, then, is that the example of non-transitivity demonstrated here is rather "obvious"; the result is entirely predictable, given the amount of previous work in similar microbial systems. However, this is countered by the fundamental nature of the question for evolutionary biology, and the lack of specific experimental examples, apart from the very old Paquin & Adams. Overall, then, I am satisfied that this paper is a significant step forward. I found it well written, interesting, and the conclusions were well supported by careful and thorough experiments.

Reviewer #3:

The manuscript by Morcom et al., describes mechanisms of Corpus callosum Diysgenesis in mice and how they relate to humans. It will be of interest to the field. It explains the spectrums of disorders of the corpus callosum in humans. It is an important study that sets the focus on midline populations and away from axonal navigation as the main source of corpus callosum dysgenesis.

The authors found that a mutation in Draxin carried by certain mouse strains is responsible for the heterogenicity of corpus callosum phenotypes found in these mice. Draxin mutations interrupt the normal remodeling (closing) of interhemispheric fissure necessary for callosal axons to cross. The phenotypes in the mouse are very similar to what is found in humans, and also variable, perhaps related to stochasticity on the mechanisms involved, or to the dependency on other allelic variants. The findings are important to understand what mutations cause CCD in humans and how, mechanistically, it occurs. The authors found that Draxin mutation misregulates astroglial and leptomeningeal proliferation. Mechanistically, how this more precisely affects interhemispheric remodeling is still unclear. This is a point that may reinforce the work.

Major concerns:

1) The authors have done an excellent job identifying the mutation and characterizing and comparing in detail the phenotypes in mice and humans. They also provide very interesting hints about how Draxin regulates the remodeling of the interhemispheric fissure. But mechanistically, their findings only offer an incomplete view. In my opinion, the findings would be reinforced by a deeper digging into how, cellularly or molecularly, Draxin makes glial and leptomeningeal cells remodel the interhemispheric fissure. Proliferation by itself does not seem to explain the phenotypes. It is not fully clear the model that they are proposing. Does it affect cell-cell adhesion, cell-cell signaling, membrane processes, metalloproteinase activity? Perhaps they could characterize some more the morphology and junctions of the affected cells or perform some studies in acute models or in vitro.

Minor comments:

Fig 4C-the expression patterns of mRNA Draxin in C57 or BTBR does not seem so similar as it is mentioned in the description of the results.

Fig 4D-The full versión of western-blots shown in supplementary showing all forms is more informative than the cuts shown in principal Figure. Please indicate molecular weights.

Reviewer #3:

This work by Katada and colleagues uses M4 and 5B transgenic lines to express ChR2 in starburst amacrine cells (SACs) and retinal ganglion cells (RGCs). It finds that ChR2 activation in SACs improves the ChR2 response in RGCs. Thus, in a gene therapy strategy that expresses optogenetic proteins in RGCs, SACs may be considered as a helpful additional target. The rationale of the manuscript basically regards RGCs as a uniform population and disregards all amacrine cells except SACs. If differences in RGC and amacrine subtypes are taken into consideration, some conclusions of this manuscript should be revised.

Major comments:

1) This manuscript makes one assumption: that the RGCs in M4-ChR2 and 5B-ChR2 have comparable ChR2 evoked response if activated alone, thus the difference between their ChR2 responses is entirely attributed to the activation of extra SACs in the M4 line. Yet there is no experimental evidence to support this assumption. Both M4-YC and 5B-YC label ~35% of the RGC consisting of multiple subtypes, the subtype compositions of the two populations are not shown. ChR2 response properties of a neuron may be influenced by its own ion channel composition that differ between cell types. The authors need to either a) show the 2 mouse lines label identical subsets of RGCs (unlikely, given FigS6E), or b) compare M4 line with or without coactivation of SACs to single out the effect of SACs.

2) The experiment results using rAAV (Fig4) are hard to interpret:

a) CAG promoter directs expression in most cell types. So other amacrine (Fig4D) and RGC cell types in addition to SACs and M4/5B RGCs are also infected. Comparison between rAAV/M4/5B retinas cannot provide clean insight into the effect of SAC.

b) The manuscript makes comparisons within the rAAV experiments (Fig4I-K FigS8F-H), trying to link induction efficiency into SACs with visual restoration. However, it is a given that higher infection in RGCs also leads to better visual restoration. So SAC effect cannot be separated from RGCs (Fig4J-K FigS8G-H).

c) The one exception shown in Fig4I and FigS8F, where SAC infection rate is linked to maintained/peak ratio, while RGC infection is not, has two caveat: First, the authors acknowledge that higher maintained response may not causally link to better restoration (line 235). Second, the same correlational analysis for other AC types is missing.

d) At this stage, a simpler interpretation of the results is equally plausible: that higher infection in all retinal neurons (regardless of type) is correlated with better restoration.

3) M4-ChR2 retina has very weak OFF response to regular light stimulus, but 5B has normal ON/OFF ratio. The authors speculate that SACs are responsible for this difference. But one observes that M4 labels mostly OFF RGCs while 5B labels equal amount of ON and OFF RGCs (S3 and S6E, lamination patterns of M4 and 5B), so there is a simpler explanation: RGCs that express tet-ON ChR2 are no longer very responsive to regular light stimuli. If that is true, that these cells are very unhealthy, then comparison of their ChR2 responses becomes less meaningful. The authors need to address the cell health problem caused by tet-ON ChR2 expression.

4) Only a few RGC subtypes form synaptic connections with SACs in the rodent retina. Thus, the effect of SACs would be limited. In the case of primate retina, ChAT positive neurons are much fewer, so their effect in ChR2 gene therapy are likely even more limited.

5) Lines 154-155: an equally likely explanation: M4 contains ON and ON-OFF DSGCs, which are known to be important for OKR, whereas 5B does not. This possibility needs to be considered.

Reviewer #3:

In this manuscript, Santos and Sirota demonstrated that the in vivo fast choline dynamics detected using choline-oxidase based biosensors is strongly correlated with, and likely caused by, phasic oxygen dynamics in vivo. The authors developed a novel tetrode-based amperometric choline oxidase (ChOx) sensor that can simultaneously measure ChOx and O2 levels within the same tetrode, which enabled the authors to observe strong correlations between ChOx and O2 levels in vivo (in behaving rats and mice, and under several distinct behavioral contexts). To dissect the causal relationship and determine the role of phasic O2 transients, the authors further combined in vivo as well as in vitro perturbation experiments to demonstrate that that phasic fluctuations in O2 concentration can lead to fluctuations in ChOx measurements. Moreover, mathematical modeling recapitulates the systemic relationship between ChOx and O2, suggesting the source of this coupling stems from non-steady-state enzyme kinetics. Together, these findings challenge the long-held belief that ChOx sensors can measure sub-second temporal dynamics of choline concentrations in vivo, and also calls for critical re-evaluation of all oxidase-based biosensors literature to determine the contribution of phasic O2 dynamics in vivo.

The study provides extensive evidence to support their claim: correlational, causal, analytical and modeling. The authors employed multiple levels of approaches, from the development of novel biosensors that leads to the observed correlation, to careful in vivo and in vitro perturbation experiments to demonstrate causal relationship. The data is carefully analyzed, and elegantly matched with modeling results. The results of this study have broad implications beyond the ChOx literature and in fact challenge the entire literature on oxidase-based biosensors.

Reviewer #3:

This manuscript attempts to address a timely question about animal social networks - what is their functional resilience to human-induced disturbance? The authors use association data from savanna elephants to construct empirical and virtual networks and assess how these change after virtual removal of individuals based on their age or network position (to simulate poaching events as real-world data were not available). Simulation studies require clear statements of caveats for interpreting the results as they only predict potential direct responses of a network and cannot account for the dynamic and indirect responses that are more likely to occur in nature. Here various network metrics are used to infer functionality, but critically, these are not supported by field data or citations (either from elephants or other study systems), and furthermore the relevance of the metrics to address structure vs. function is unclear to readers less familiar with SNA. Secondly, the motivation for the study is deeply embedded in elephant biology and would benefit a broader audience with a clear introduction to structural vs. functional resilience.

1) Applicability of simulation studies

The study sets out to test the functional resilience of elephant networks after simulated poaching events because real-world data were not available (to the authors). There are many caveats for applying the results of network simulations to real-world data because they rarely can take indirect and dynamic responses into account (unless these data are used to inform the simulation), see Shizuka & Johnson Behav Ecol 2020 for a nice review of this point. The authors allude to this in the discussion when they discuss the need for more dynamic models, but conclude by stating the need to work more collaboratively - this is a good point and I'm sure it's true, but there really needs to be a clear statement about the applicability of these simulated results in the introduction and upfront in the discussion. This is essential to avoid inadvertently misleading readers less familiar with these methods.

2) Network measures need greater empirical support and explanation

As this is a simulation exercise, it is essential that the network metrics are meaningful in this context. This is especially important given recent discussion of metric hacking in social network analysis studies (e.g. Webber et al. Anim Behav 2020). At present, some of the metrics are presented in a paragraph in the Introduction with vague support e.g. line 281 - "Each of these heuristics... SHOULD change drastically...", and all 7 are in table 1 but there are no references (either from elephants or even broadly-speaking from studies on networks) to support the major assumptions of the study. Refs are given in the table caption but it is unclear what these relate to. There have been some very interesting experimental studies on functional resilience which might help in this regard. E.g. Maldonado-Chaparro et al. 2018 PRSB used captive zebra finches to experimentally test foraging efficiency (i.e. functionality) of social groups after repeated disturbances to their networks, and as here, focused on functional change immediately after disturbance (e.g. line 172-73).

More importantly, it is unclear which of the 7 metrics are supposed to inform us explicitly about structure vs. function or whether these can even be unambiguously disentangled - e.g. is clustering coefficient structure or function? It is used in both this study and by Goldenberg et al. 2016 that is introduced here as focusing only on structural resilience. It would be very helpful to have clear statements about the metrics and predictions regarding structural vs. functional resilience. At the moment they vary throughout the manuscript, e.g. referred to as metrics of social competence in the discussion (line 543). Sorry for my confusion, but there are so many different ways that we can derive metrics from networks that justifying these clearly is critical for the conclusions of the study.

1. More succinct presentation of the knowledge gap and its broader implications beyond elephant biology.

At present, the study is presented with elephant biology and conservation as the core motivation, yet the concept of functional resilience is fundamental for studies of any species where social connections influence the flow of information (and presumably fitness of individuals). The introduction is extremely long (10 paragraphs over 6.5 pages) and functional resilience is not introduced and defined until the end of the Introduction's 4th paragraph and its link to broader literature is confusing . Focusing the introduction on how/why structural and functional resilience may vary in networks (and how this can be inferred from network metrics), and then using elephant biology as an example for why this is relevant to study, might make it much easier to follow.

Reviewer #3:

Quiroga et al. studied the molecular function of mechanosensitive ion channel protein Piezo1 during mouse primary myoblast differentiation in culture condition. The authors measured myoblast proliferation and differentiation after either knockdown of Piezo1 or chemical activation of Piezo1 protein. In overall, the study is significant given its conclusion directly contradicts with a recent study by Masaki Tsuchiya et al. Nature Communications (2018) by which knockout of Piezo1 produced opposite effects. However, major concerns were identified and need to be addressed to strengthen their claim.

1) It is unfortunate that the authors have confused "fusion index" with "differentiation index". By the description in Method, they actually measured differentiation index though claimed as "fusion index". The commonly used fusion index is the ratio of nuclei in myocytes with {greater than or equal to} 3 nuclei normalized with total number of nuclei in MyHC+ myocytes. Therefore, it appears that what the author claimed about "fusion defect" was actually a differentiation defect. These errors need to be corrected.

2) Following comment 1, the authors need to evaluate whether or not the differentiation is affected when Piezo1 is knocked-down or activated. It is suggested to run a panel of qPCR assay for myogenic markers including myosin genes (Myh3, Myh8). Western blots of myosin by MF20 antibody will also need to be performed and quantified.

3) The author discussed the potential off-target effects for siRNA from the previous study. Although it is comparatively more convincing that this manuscript tested 4 siRNA, for the scientific rigor, the authors still need to clarify whether the study by Tsuchiya et al is reproducible. As such, the authors should measure myoblast fusion by using the same siRNAs as listed in Tsuchiya et al. In addition, the authors should also characterize the myoblast fusion phenotype of Piezo1 gene-KO from CRISPR treatment of primary myoblast.

4) To rule out any off-target effects of the chemical activator of Piezo1, the authors should test whether this drug's effect on myoblast fusion /differentiation can be negated when Piezo1 is knocked down.

5) Concerning the role of myomixer gene in Piezo1 KD phenotype, the authors should use another set of primers for qPCR. The current forward primer only detects a predicted longer transcript isoform of Mymx but not its predominant isoform (NM_001177468).

6) For Fig.6, the details of experiment procedure, e.g. the timing of drug treatment in relation to differentiation timing, needs to be provided.

7) The authors should cite the correct references as being consistent with their description. For instance, line# 528, 1011. In addition, the writing needs to be improved for better readability.

Reviewer #3:

In this manuscript, Naetar et al. investigate the role of LAP2α binding to A-type lamins in the nucleoplasm. LAP2α was already thought to be important for maintaining the nucleoplasmic pool of soluble A-type lamins, because knockout of LAP2α has previously been shown to reduce nucleoplasmic signal from an antibody that recognizes the lamin-A/C amino terminus. However, by directly tagging A-type lamins with fluorescent proteins and by using an alternative antibody to stain them, Naetar et al. find that the presence of LAP2α does not appreciably affect the pool of soluble lamins in the nucleoplasm. Instead, they find that LAP2α affects the assembly state of soluble lamins within the nucleoplasm, preventing formation of higher order A-type lamin structures that impede the mobility of telomeres within the nucleus.

There is a lot to like about this paper. I admire the author's mechanistic approach to studying lamin assembly state. The complementary cell biology/microscopy approaches paired with the biochemical approaches in figure 5 lead to an overall convincing story. And finally, I appreciate the efforts the authors made to "show their work," including their genome editing quality control measures.

Major comments:

1) Although I appreciate the transparency of the authors in demonstrating their workflow and quality control measures (see above), some of the terminology makes the manuscript difficult to read. At times it feels more like reading a lab notebook than reading a manuscript. For example, The manuscript would be easier to understand if cell lines were given descriptive names (eg: LAP2α KO, or mEos3.2-lmna instead of "WT#21") rather than continuing to refer to them by the small guide RNA that was used to generate them. A second example: it is nice to show biological replicate data as in figure 1, but it took me a while to figure out that the second and third columns in panels A and B were biological replicates; I spent some time trying to determine which experimental condition was different. Perhaps one biological replicate could be displayed in the main text and the second could be moved to the supplement, especially considering that it appears that only one of the clones was used for the quantifications shown in the bottom panels.

2) Why was the choice made to disrupt LAP2α at the beginning of exon 4? How large are exons 1 and 2, which are not shown in the schematic in the supplemental figures? What percentage of the LAP2α peptide primary sequence is affected by a frameshift mutation at the start of exon 4? Why was this approach preferable to introducing a frameshift mutation closer to the 5' end of the gene? I am concerned that the "LAP2α KO" cells used in the experiments may have some partially functional truncated LAP2α protein.

3) On page 16, the authors describe a set of experiments that are meant to demonstrate that their failure to see a difference in nucleoplasmic A-type lamins in LAP2α mutants is not due to the fluorescent protein tag used, however, instead of looking at untagged lamins, they elect to look at a cell line that has all lmna alleles tagged. Wouldn't it be better to use the LAP2α KO cells from figure 1 and stain with both the 3A6 antibody and the N18 antibody to determine whether untagged lamins behave the same way as tagged lamins? Perhaps this experiment could be added along with the current data, as it would be nice to compare directly between a cell line with all lmna alleles tagged and a cell line with no lmna alleles tagged.

This experiment would also give the authors a chance to compare morphology and overall fitness of cells with all untagged lmna with cells with all tagged lmna, to determine whether the tagged proteins are fully functional. Even if the tagged protein is fully functional, it would be appropriate to add a brief discussion of the possibility that fluorescent tags do perturb lamin-A/C function. After all, many lamin mutations do not cause obvious phenotypes in tissue culture cells, but defects can still emerge during development and aging in the context of an animal.

4) The authors build a convincing case that binding to A-type lamins by LAP2α influences their ability to assemble. But how do cells leverage this relationship for biological functions? Do cells tune the amount of fully soluble vs. partially assembled A-type lamins in the nucleoplasm in order to control nuclear structure or function in response to certain stimuli? Have the A-type lamins in the nucleoplasm been found to be in a different assembly state in different cell types? As the study is currently written, it presents an interesting molecular mechanism but no biological mechanism.

Reviewer #3:

In the current manuscript (De novo learning and adaptation of continuous control in a manual tracking task), Yang et al. aim to demonstrate that motor adaptation to a mirror reversal perturbation to visual feedback is de-novo learning of a movement controller in contrast to the adaptation of an existing controller with rotation to visual feedback. The authors examine two different experimental paradigms (1) continuous tracking of a cursor (trajectories generated by different sum-of-sinusoid functions) and (2) point to point movements under these two different visual manipulations of the cursor feedback: a 90 deg rotation and mirror reversal. Importantly, the authors set the motion of the cursor under the continuous tracking case as a sum of sinusoidal trajectories in order to perform frequency analysis of the motion tracking. The authors then examine the behavior in the time domain, and dissect the responses at individual frequencies in the frequency domain to determine the response of learning observed in each condition to the fast and slow changing components of the perturbation. There are two major reported results: (1) Participants learn both mirror reversal and rotation learning, but mirror reversal learning shows little to no aftereffect, whereas rotation learning shows an ~25º aftereffect from ~70º of learning. The authors argue that this suggests that mirror-reversal learning arises from a de-novo controller that is not engaged during baseline or washout (Lines 199-200) (2) Learning in the continuous tracking task shows a gradation in performance over frequencies (i.e., higher frequencies demonstrate lower learning). These are interesting experiments, with a well-defined motivation/question and (mostly) clear presentation of results. The figures and results largely support the hypothesis. My specific comments are shown below:

1) In the abstract, the last line says 'Our results demonstrate that people can rapidly build a new continuous controller de novo and can flexibly integrate this process with adaptation of an existing controller'. It's not clear if the authors have shown the latter definitively. What is the reasoning for this statement, "flexibly integrate this process with adaptation of an existing controller"? It would seem you would need the same subjects to perform both experimental tasks (mirror reversal and VMR) concurrently to make this claim.

2) It would be helpful if the authors could provide more background/context on their view of de novo learning and explanations on the relationship between de novo learning and the adapted controller model. For example, why does the lack of aftereffects under the mirror-reversal imply that the participants did not counter this perturbation via adaptation and instead engaged the learning by forming a de novo controller (Line 199)? Is the reasoning purely behavioral observations, or is there a physiological basis for this assertion?

3) Details about frequency analysis are buried deep in the methods (around line 711), especially how the hand-target coherence (shown in 4B) is calculated. It would be helpful to include some of these details in the main text. For example, it is currently very difficult to understand the relationship when from moving from Figure 4A to 4B.

4) Lines 197-199: The reason for the lack of after-effects in the mean-squared error analysis is a little vague. It took a few tries to understand the reasoning. It would be good to spell this out a little more clearly.

5) Lines 223-225: The logic behind why coupling across axes is not nonlinear behavior seems to be missing. It's quite unclear and currently difficult to understand. It would be very helpful to spell this out too.

6) Surprisingly, there is no measurement of aiming in the learning to VMR. Several motor learning studies (several the authors cite) show that learning in VMR is a combination of implicit and explicit. I understand that this is not possible in the continuous tracking task, but can certainly be done in the point to point task. Is there a reason this was not done? Wouldn't this have further supported the author's claim of an existing controller?

7) Figure 2C: the data for mirror-reversal seems to have a weird uptick in the error. Why would that be? Is there an explanation for this?

8) Lines 339-342: the results show that mirror-reversal learning is low at high frequencies (Fig 5B). The authors interpret this as reason to believe that this is actually de-novo learning and not adaptation of an existing controller. This seems somewhat unfounded. Could it be that de novo learning performs well at low frequency, through 'catch-up' movements, but not at high frequencies? Do the authors have a counter argument for this explanation?

9) Lines 343 - 350: The authors ascribe the difference between after-effects and end of learning to be due to de-novo learning even in the rotation group. However, that difference would likely be due to the use of explicit strategy during learning and its disengagement afterwards, or perhaps a temporally labile learning. Can the authors rule these possibilities out? What were the instructions given at the end of the block and how much time elapsed?

10) Lines 787: Outlier rejection based on some subjects who had greatly magnified or attenuated data seems like it might be biasing the data. Also, the outlier rejection criteria used (>1.5 IQR) seems very stringent. Furthermore, it appears there was no outlier rejection on the main experiment. It would be good to be consistent across experiments.

11) Figure 4: The authors show the tracking strategies participants applied by investigating the relationship between hand and target movement. The linear relationship would suggest that participants tracked the target using continuous movements. In contrast, a nonlinear relationship would suggest that participants used an alternative tracking strategy. The authors only state this relationship is based on figure 4 but it seems do not provide any proof of the linearity. It would be more convincing to provide an analysis to show that the relationship is indeed linear or nonlinear.

Reviewer #3:

This manuscript is a detailed analysis of the molecular mechanism for ISW2 recruitment in yeast and delineates not only the binding interface between ISW2 and the transcription factor Ume6, but also finds similar interactions between ISW2 and Swi6. The authors take a systematic and rigorous approach in finding that a 27 amino acid region of Ume6 and the WAC domain of Itc1, accessory subunit in ISW2, are responsible for recruiting ISW2 to Ume6 binding sites. The strength of this paper is that they focus on examining these interactions in vivo and using MNase-seq to show changes in nucleosome positioning upon mutation of Itc1, Ume6 and Swi6. The data is well supported and the conclusions are compelling. In addition, they use the Spytag approach to show these regions alone are capable of recruiting Isw2 to genomic target sites. They also show that amino acids 1-73 of Itc1 alone are sufficient for binding to the correct genomics sites and is compelling evidence of their specificity. The authors, by comparing the sequence composition of the WAC domain in ISW2 orthologs from flies to humans, are able to explain a contradiction that has been in this field for a long time about the apparent different role of yeast ISW2 and its Drosophila homolog ACF/ISWI. The Drosophila ISWI complex appears to have a more global role in chromatin organization; whereas yeast ISW2 is more specialized or targeted. The WAC domain in ISWI is defective for recruitment by such transcription factors like Ume6 and Swi6, unlike that observed for ISW2. The other interesting finding or correlation that is derived from their findings is that the recruitment of ISW2 by Ume6 and Swi6 may not only work to recruit ISW2 but may also regulate ISW2 activity as the same region of Itc1 shown to bind to these transcription factors is also shown to regulate the activating function of the H4 tail on Isw2. The paper is well written, clear and nicely organized. I did have one question for the authors, as it seems that this type of recruitment may not be universal as there are only a subset of Ume6 sites that behave as expected in their mutational analysis. Do the authors have any idea why that is the case and what makes this subset of sites behave differently?

Reviewer #3:

The authors report results of an MEG analysis deploying a cognitive paradigm in which participants engage in a source memory task characterized by the appearance of three images in succession and are then tested via a cue (the first of the three images) followed by a choice of responses for a two dimensional pattern and then a choice (out of three images) of a photographic scene.

The principal finding is that (via MEG sensor level data) there is a widespread 8-15 Hz power decrease that is correlated with the number of recalled items (from 0 to 2) on a given trial. In the hippocampus (via MEG source reconstruction), the magnitude of phase amplitude coupling observed as participants are told to associate the items is correlated with memory performance. The 8-15 Hz power decrease/memory correlation (as estimated by beta coefficients in a model described in Figure 1) is larger (across individuals) during moments when subjects are viewing the stimulus items as opposed to during the "associate" period. The novelty in the result is related to the experimental task that attempts to dissociate memory-related effects related to perception from those related to binding which putatively occurs when subjects are given the "associate" instruction.

My main conceptual concern is related to the design of the experimental task. I am not sure that the perception/binding framing is appropriate, since there is no reason to think that subjects are not associating/binding items during the periods when the items are being shown on the screen. I suppose this may partly explain the lack of a significant difference in PAC/memory beta coefficients observed in the hippocampus when contrasting these two epochs (Figure 4). But the corollary is that the alpha power-related beta coefficients are observed while binding is likely also occurring within the paradigm (esp since each image is shown for 1.5 seconds it would seem). Is the alpha power effect seen in the hippocampus? The plots in 3a suggest there is an oscillation present in the relevant frequency range, and the time course of alpha power differences seen in Figure 2 suggests that they occur relatively late after onset of the images, which may fit better with some contribution for this pattern to the forming of associations rather than perception.

I understand that the paradigm was constructed in an attempt to temporally dissociate memory effects attributable to perception versus those attributable to binding. But given the temporal resolution available using EEG, I would imagine that the authors could differentiate an earlier perception-related effect from a later PAC binding effect in the time series if the associated images were presented in conjunction. Is it correct to frame the alpha results as related to "perception?" The beta coefficients used for analysis reflect a "memory related effect observed when visual stimuli are present on the screen," but not necessarily improved memory predicated on more accurate perception to my interpretation. I would think that a perception/binding distinction requires operationalizing perception as activity that doesn't vary with later associative memory success, and binding as activity that does. The notion of perception used by the authors here seems slightly different. The authors can perhaps comment on this concern.

The authors report PAC results for other regions on page 6, but claiming that PAC is a hippocampal-specific effect would require showing that the PAC-related beta coefficients are significantly greater than the other regions, rather than simply the absence of a significant effect in these regions. The authors should also clarify if they combined locally measured PAC over several ROIs into an average for these other regions? It seems unlikely to detect PAC if a single theta/gamma time series were extracted over such a large area of cortex.

The interaction effect reported at the end of the results (ANOVA model) is interpreted such that the cortical alpha effect is stronger when the visual items are presented, while the hippocampal PAC effect is stronger when no items appear on the screen, but these recordings are made in different regions (hippocampus versus the entire cortex). If my understanding is correct, a result in line with the model the authors suggest (cortical alpha power decrease/hippocampal PAC) would show a region (hipp v cortex) x task (images on screen vs "associate" command) x metric (PAC vs alpha) interaction. Can the authors clarify if the cortical data entered into this model includes only those regions that showed a significant effect initially, or just all the sensors? The former would seem to introduce bias.

Similarly, the different visual classes are always presented in the same order, which may give rise to the strong disparity in recall fraction between the pattern and scene images. I understand the linear model incorporates predictor variables for scene/pattern recall, but given that scene recall is driving a significant amount of the overall recall number observed as the main variable of interest, I would wonder if the alpha/beta power effects are related to the relative complexity of the scene images as compared to the patterns. Given the analysis schematic the authors report, I assume the authors have analyzed whether the same effects occur when contrasting scene versus no recollection and pattern vs no recollection. If the same effects are observed regardless of type of image (when compared with no recollection) this may help address this concern.

My second conceptual question is related to MEG data. It appears to me that the authors use MEG sensor-level data for the alpha-related effect in the cortex (Figure 2), but MEG beamformer reconstructed data (localized to the hippocampus) for the PAC effect. Is there a reason the authors did not use MEG data localized to specific cortical regions rather than sensor data? This may reflect confusion on my part, but I don't understand why they would use qualitatively different types of data for these two aspects of the analysis that are then combined (in the ANOVA, for example).

The authors should also engage with concerns regarding the validity of localizing MEG signals (especially for an analysis such as PAC) to deep mesial temporal structures such as the hippocampus. I understand that MEG systems with greater than 300 sensors are more reliable for this purpose, but I think a number of readers would still have doubts about MTL localization of signal. Also, my understanding is that such deep source localization requires around 100 trials per class, which I think fits with what the subjects completed, but the authors may include references related to this issue.

I think the signal processing steps are overall quite reasonable. I would ask the authors to clarify if they limited their analysis of cortical alpha/beta oscillations to those in which a peak exceeded the 1/f background, as they report for the PAC analysis on page 5. Also, it would be helpful to show that the magnitude of the MI values in the hippocampus exceed those observed by chance (using a shuffle procedure) in addition to showing that there is a memory-related association reflected in the beta coefficients.

Reviewer #3:

This is a very thorough study giving new insight into a non-cell autonomous mechanism for DCC in axon guidance in midline fusion important for corpus callosum axon guidance.

I have no substantive concerns.

Reviewer #3:

Substantive concerns:

1) Regarding hypothesis 4, the authors test whether or not desiccating species have lower TE loads than non-desiccating species, but in my opinion the logic outlined in lines 114-124 suggests that the relationship between desiccation and TE load may be more nuanced than overall TE load. It could be possible that DSB repair associated with desiccation removes only recent insertions if homologous pairing is involved, or high-copy TEs if ectopic recombination has occurred. The authors already test recent TE activity elsewhere in the manuscript, so they could compare signatures of recent activity in desiccating vs non-desiccating species to see if there are fewer recently active TEs in desiccation species. Similar comparisons could easily be made for abundance of high-copy TEs (regardless of length).

2) Additionally, regarding the signatures of recent transposition, the authors have done a thorough job comparing TE divergences and LTR insertions, but since transcriptomes for some species are available, presence of transcribed TEs could provide further support for recent and ongoing TE activity.

Reviewer #3:

This paper compares two methods for assessing the effect of luminance on visual processing speed. One method represents conventional methodology, using a forced choice button push approach to assess the Pulfrich effect (whereby delayed processing of horizontal motion in one eye creates a percept of motion in depth). The other, more novel method uses a continuous (monocular) tracking task to assess relative delays in signal processing caused by luminance changes. The authors show that the two approaches yield remarkably close agreement (to within a few milliseconds) in their estimates of the relative processing delays caused by luminance differences across eyes. The authors go on to establish Pulfrich-like effects in a binocular tracking task.

The paper is very clearly written, and the experiments and analyses have been meticulously conducted. The technical quality of the work is excellent. Scientifically, the paper does not really contribute any novel insights about the nature of perceptual processing. Rather, the paper represents more of a methodological manifesto advocating for the power of tracking-based psychophysics approaches. The experiments serve as a powerful illustration of how well tracking tasks can work in practice, validated by more conventional approaches. The paper makes a compelling case that tracking tasks are able to reproduce existing findings, and can do so significantly more efficiently (i.e. in much less time).

The novelty of the approach is a bit overstated. On the first page, the authors suggest that continuous target tracking is "a new stimulus-response data collection technique". This is a bit much. People have been doing manual tracking tasks for decades, in many cases with quite sophisticated analysis and an emphasis on elucidating perceptual processing, in a similar spirit to this paper. Studies of eye movement and postural control have also employed related approaches. See, for example, the work of John Jeka, Tim Kiemel, Chris Miall, Otmar Bock, Noah Cowan - as well as the likes of Jex and McRuer in the 70s. Perhaps the authors were not aware of this substantial body of work. It seems appropriate to offer some acknowledgement and discussion of this prior work that has also recognized the power of such methods and employed them very effectively.

A significant weakness of the paper is the small number of participants who performed the tasks - only five, two of which were the authors of the paper. While the within-participant comparisons are compelling, the broader agenda of advocating for wide adoption of these tracking tasks for scientific and potentially clinical applications will need more extensive validation on much broader populations. I do share the authors' optimism about the use of tracking tasks, but broad adoption for probing perceptual processing will require demonstrations that these approaches can be robust across much larger cohorts.

Reviewer #3:

Whole genome sequence data from a geographically large set of 86 Brachypodium distachyon samples is presented and combined with previous data. In addition, flowering time collected from both field and controlled conditions are presented. Overall, the manuscript has many interesting aspects and ideas but overall, the main agenda is not clear. They mention selfing, seed dispersal, coalescence theory, microevolution, plasticity and frequency dependent selection in the abstract but none of those topics are explored in-depth in the manuscript. There were multiple points e.g. in the methods that needed clarification. The manuscript would benefit from focusing on one or two aspects and making strong cases for them.

Main comments:

1) It is an overstatement to claim that this dataset covers the region from Iberia to Iraq, when already previous datasets covered Iberia and Iraq. Here French and Italian samples are added to previous data.

2) The connection between the heterozygosity, structural variation and assembly issues due to paralogy should be more clearly presented. For example, in r. 130-134,it is not obvious what does mapping against BdTR7a to itself and identifying less heterozygous sites prove? In addition, the procedure for masking the fake heterozygosity should be more explicitly described. Inspection by IGB, or defining thresholds by "trial and error" are not reproducible methods. Also, wouldn't one want to take into account the overall level of diversity in a given region instead of putting a threshold as "ten or more SNPs along a distance of at least 300 bp".

3) Sympatry issue: The different lineages are described to be sympatric thus it would be important to be really specific about the sampling locations. How close are the closest sympatric samples representing different lineages? Is that truly a sympatric setting? Further in r. 176-181, how does plotting ancestry components in the map prove that there has not been gene flow between sympatric lineages? There seems to be shared ancestry but it is a known issue that shared ancestry and admixture are not easy to separate. This aspect is central to the paper and would need more rigorous analysis with e.g. forward or coalescence simulations. The reasoning continues in rows 344-352, but is not really backed up by any analysis other than plotting ancestry components on the map. Or if it is, it should be more precisely expressed.

4) R. 301-303 this statement sounds like the authors are suggesting that selfing and dispersal are actively (or as a result of selection) interacting and maintaining the diversity. I did not see convincing evidence that the distribution of lineages is not just a combination of drift, selfing and random dispersal events. Maybe this is what the authors mean, but should be more clearly stated.

Reviewer #3:

This manuscript investigated the interactions of SARS-CoV-2 S protein and its RBD domain with ACE2 protein of host cells using mainly the HDX-MS approach. The results revealed the dynamics information about the interactions and how ACE2 binding at the RBD domain primes enhanced proteolytic processing at the S1/S2 site of S protein, and are potentially useful for the relevant research, e.g., therapeutic development. This is a rather straightforward study, without further biological validation of the major conclusions. Detailed comparison and integration of the HDX-MS results with those from cryo-EM were not provided in the manuscript as well. Some details of the manuscript also need further clarification.

Major comments:

1) Fig. S1: The SDS-PAGE showed around 90 kDa for the molecular weight of RBDisolated, which should be around 25 kDa based on its sequence (318-547). Please check and clarify.

2) It is confusing about the existing forms of the S protein and ACE2 and their binding stoichiometry, regarding the statements such as "we measured dynamics of a trimer of this near-full length S protein..." (Page 4, line 87), "we performed HDXMS experiments of monomeric ACE2..." (Page 10, line 220-222), "......were pre-incubated at 37{degree sign}C for 30 min in a molar ratio of 1:1 to achieve >90% binding......" (Page S2, line 65-66). Please confirm whether the expressed ACE2 is dimeric and S protein is trimeric or not, and their binding stoichiometry is 1:1 or 2:3. Please also provide the concentration and calculation details for ensuring the >90% binding. If only one ACE2 in the ACE dimer and one S protein in the S protein trimer are involved in the binding, how sensitive and accurate could the HDX-MS results reflect the binding, since no HDX difference would be observed for the other ACE2 and other 2 S proteins?

3) Page 2, line 33-35: Other studies (e.g., Ref. 11) have shown that ACE2 binding can enhance S1/S2 cleavage by furin and S1/S2 cleavage site could be possible targets for small molecule inhibitor/antibody development. It would be helpful if further evidence could be provided to support that the stalk hinge regions could also be the targets for that.

Reviewer #3:

Thank you for inviting me to review this manuscript by Guell and colleagues, in which the authors conduct an interesting study into the hemispheric symmetry (or lack thereof) between low-dimensional resting state functional connectivity gradients in key structures within the subcortex. In a large cohort of individuals, the authors demonstrate interesting asymmetries in the thalamus and pallidum, along with the cerebellum and striatum. They then survey a broad anatomical literature in search of a parsimonious explanation for their observed results.

Overall, I found the manuscript to be interesting, well-documented and well-reasoned. I have only minor comments that I hope will help the manuscript.

• My only slightly major concern is in the section titled 'Projection of subcortical functional gradients to cerebral cortex'. Specifically, I'm worried that multiplying each subcortical voxel by the absolute value of its eigenvalue may remove the effects of interest. For instance, in the raw eigenvalue, there is an interpretable (and important) difference between loadings of +1 and -1, however these two scores would be equivalent when the absolute value is taken. The authors mention that "Absolute functional gradient values were used in order to specifically observe the relationship between subcortical regions with strong IHFaS as indexed by asymmetric functional gradients and cerebral cortical connectivity", but I don't see how this follows.

• Is it perhaps surprising that there is strong IHFaS between first order thalamic regions but not between the cortical regions providing modulatory inputs to those regions?

• Do the authors predict that these patterns will be similar for task-based data analyses?

• The thalamic patterns appear to overlap with Ted Jones' concept of 'core' and 'matrix' thalamic nuclei (doi: 10.1016/s0166-2236(00)01922-6). Although these terms loosely overlap with 'first-order' and 'higher-order' thalamus, they are defined by the mode of thalamic projection to the cerebral cortex (targeted, granular vs. diffuse, supragranular, respectively), rather than the projection from cortex (as in the case of first- and higher-order).

• I couldn't find any information about whether the resting state fMRI data were filtered prior to the calculation of voxelwise cosine similarity. It could be interesting to determine whether the observed patterns are associated with broad-band patterns or more specific frequencies.

• The large sample size is a strength of the approach, but I did not see this leveraged anywhere in the manuscript. For instance, was there strong split-half reliability, or were some patterns more variable across subjects?

Reviewer #3:

This work started from the notion that Alzheimer's disease (AD) pathology spreads through connected regions, and investigated whether the level of AD pathology in specific regions relates to the integrity of the fiber bundles connecting them, in 126 elderly with normal cognition at risk of AD. Specifically, AD pathology was quantified by beta-amyloid (Aβ) and tau protein levels from positron emission tomography (PET). Three fiber bundles, the cingulum, the fornix, and the uncinate fasciculus, were a priori selected, and six measures were derived from free-water corrected diffusion tensor imaging. The authors hypothesized that Aβ levels would relate to the integrity of (i) the (anterior) cingulum, and (ii) the uncinate, and (iii) that tau levels would relate to fornix integrity. The direction of the relations was not specified. The authors find support for particularly the second hypothesis (Aβ levels and the uncinate), but also for the first (Aβ levels and anterior cingulum). They also find relations between tau levels and uncinate integrity, and Aβ levels and right fornix integrity. The relations were consistently in a direction the authors refer to as "unanticipated", that is, more restricted diffusion with the presence of pathology. The authors conclude that the result "suggests more restricted diffusion in bundles vulnerable to preclinical AD pathology”.

The work addresses important topics (early detection and spreading of AD pathology) of great interest to people from several disciplines. The sample is interesting with both regional Aβ and tau measurements, and the imaging processing methods used are advanced. The paper is clearly written and nicely illustrated.

My main concern relates to the main conclusion of "more restricted diffusion in bundles vulnerable to preclinical AD pathology". Although this result is discussed as "unanticipated", I think the centrality of this point makes more scrutiny warranted.

1) Direction of relationship. The authors state that "[..]the directionality of the observed pattern of association opposes the classical pattern of degeneration. The classical degeneration pattern accompanying disease progression is characterized by lower anisotropy and higher diffusivity, representing loss of coherence in the white matter microstructure with AD progression", and further: "[..] more restricted diffusion with the presence of pathology was unanticipated [..]".

Indeed, their results were unanticipated based on the literature, as highlighted by the authors. As this is the central point of the work, I believe it is important to do additional analyses to try and enlighten the results and the suggestion of a biphasic relation. I understand that the authors have done a lot of work already, but here are some fairly simple and not too time-consuming suggestions which might be informative (please feel free to ignore these suggestions and instead follow other paths to show the reader more results to evaluate the unexpected direction of the relations):

(i) A simple start could be to assess the relationship with age, how strong this relationship is, and what the residuals look like when regressing out age (and bundle volume).

(ii) As the authors mention, a reduction in crossing fibers might lead to "more restricted diffusion" but be a sign of deterioration. Analyses undertaken to assess this point would be valuable. For instance, one could test if the relations are similar in regions of the bundles where there are little crossing fibers and in regions with more crossing fibers.

(iii) The authors state that "[...] we estimated that 20% of the participants would be considered Aβ-positive". Were a majority of these also tau-positive? If so (or if participants exist in the larger PREVENT-AD sample that were not "cognitively normal at the time they underwent diffusion-weighted MRI»), creating a group of high AD pathology, is the relations between Aβ/tau and diffusivity similar in this group of high Aβ and tau compared to a similar-sized (and, if possible) age-matched group with (very) low Aβ and tau levels?

2) Hypotheses. As mentioned, the authors state in the Discussion that directionality of the observed pattern of association was unanticipated. I was therefore somewhat surprised that the directionally of the hypothesized relations were not included in the hypotheses presented in the Introduction. I think it would increase the readability of the Results section if this point was made explicit earlier in the text, and the non-expected direction mentioned in the Results.

3) Number of tests. The author state that "Associations with a p-value < 0.05 were considered significant, but we also report associations that would survive false-discovery rate (FDR) correction for each bundle with q-value of 0.05, accounting for 6 tests (i.e. the number of diffusion measures assessed per bundle).". I find this somewhat problematic (at least without further justification). First, I think the authors should only consider corrected p-values significant. Second, these 6 measures are tested per hemisphere, and across at least 3 fiber bundles (for cingulum, it seems the authors have done separate analyses for the anterior and posterior part), making the total number of tests higher. Correcting for the number of diffusion measures per bundle might be too strict, but I think the total number to correct for should be higher than 6. Whether any correction has been applied is also difficult to grasp while reading the Result section, as it seems like p-values are not FDR-corrected in Tables 2 and 3 (mentioned only in Table 4). I think the total number of bundles assessed, and the correction should be made explicit when introducing Figure 2 and Table 2.

Reviewer #3:

Carreño-Muñoz et. al. describe an piezoelectric sensor based approach to quantify rodent behavior. Piezoelectric sensors convert pressure, acceleration, strain, and even temperature and sound into an electoral charge. They are exquisitely sensitive and have a wide range of functionalities. The paper describes an open field arena that sits on top of three sensors on an air table that is able to detect animal movement. The authors use several behavioral paradigms and genetic models to validate their system. Overall, the piezo and pressure/force/vibration based systems have been well established for rodent behavior. Some examples of commercial systems are the Laboras (Metris BV) and PeizoSleep (Signal solutions), along with many papers that describe similar systems. The advantage of the system described in this paper (Phenotypix) is that it encompasses a large open field which allows the mouse to carry out naturalistic behavior. It also sits on top of an air table which allows more sensitive measurements. Although the system described has some advantages, the manuscript does not describe a system that leads to a significant enough advance. The manuscript does not offer a thorough solution for any one problem in biology and does not make a convincing case for adaptation of this platform. The figures and experimental description are also lacking leading to unclear interpretation of data.

One of the major issues with this paper is that it does not adequately describe the Phenotypix platform to allow for replication. This may be fine if the platform is commercially available, which seems to be the goal, but when I searched for the "Phenotypix, Roddata", I did not find a commercial supplier. Thus, it is unclear how this data can be replicated. Another major issue is that it is never clear if behavior state determination based on mechanoelectrical signal, video data, or both. Ideally, one would use the video data to train classifiers that only use the mechanoelectrical data. However, it is not clear that this was done in most of the experiments. Without the hardware specifications and classifiers for the behaviors, replicability is an issue. The fact that the apparatus needs to be place on a 250kg air table brings its practical utility and scalability into question. Systems such as Laboras can be obtained with readily available classifiers for numerous behaviors (https://www.metris.nl/en/products/laboras/laboras_specs/) and allow for long term monitoring in home cage environment and questions the claim of "A novel device for behavioural phenotyping of freely moving laboratory animals (rats and mice) now allows to detect behavioural components out of reach of existing systems."

One issue that is not addressed for the various behaviors - how does body weight affect the spectral properties of behaviors. How can we compare the same behavior between two animals of differing sizes? Since this is a pressure sensor, this is important.

Reviewer #3:

The work by Münch et al addresses an important problem of modeling data that originates from multiple channels (100s-1000s) by establishing a Bayesian inference-based framework to extend an existing Kalman filter-based method. They convincingly demonstrate that their approach is much more accurate at quantifying channels using previous, and is impressively able to combine multiple experimental modalities. Most importantly, as a Bayesian method, this approach allows the incorporation of prior information such as the diffusion limit or previous experiments, and also allows one to perform model selection to select the best kinetic model of the data (although this aspect is less developed). In particular, the Bayesian approach of this work is an important advance in the field.

1) The manuscript needs line editing and proofreading (e.g., on line 494, "Roa" should be "Rao"; missing an equals sign in equation 13). Additionally, in many paragraphs, several of the sentences are tangential and distract from communicating the message of the paper (e.g., line 55). Removing them will help to streamline the text, which is quite long.

2) Even more emphasis on the approximation of n(t) as being distributed according to a multivariate normal, and thus being continuous, should be placed in the main text. To my understanding, this limits the applicability of the method to data with > ~100s of channels; although the point is not investigated that I could find. In Fig. 3, it seems the method is only benchmarked to a lower limit of ~500 channels. Although an investigation of performance below that point would be interesting, it is only necessary to discuss the approximate lower bound cutoff.

3) The methods section should include information concerning the parameter initialization choices, HMC parameters (e.g. number of steps) and any burn-in period used in the analyses used in Figs. 3-6

4) In the section on priors, the entire part concerning the use of a beta distribution should be removed or replaced, because it is a probabilistic misrepresentation of the actual prior information that the authors claim to have in the manuscript text. The max-entropy prior derived for the situation described in the text (i.e., an unknown magnitude where you don't know any moments but do have upper and lower bounds; the latter could be from the length from the experiment) is actually P(x) = (ln(x{max}) - ln(x{min}))^{-1} * x^{-1}. I'm happy to discuss more with the authors.

5) Achieving the ability to rigorously perform model selection is a very impressive aspect of this work and a large contribution to the field. However, the manuscript offers too many solutions to performing that model selection itself along with a long discussion of the field (for instance, line 376-395 could be completely cut). Since probabilistic model selection is an entire area of study by itself, the authors do not need to present underdeveloped investigations of each of them in a paper on modeling channel data (e.g., of course WAIC out performs AIC. Why not cover BIC and WBIC?). The authors should pick one, and maybe write a second paper on the others instead of presenting non-rigorous comparisons (e.g., one kinetic scheme and set of parameters). As a side note, it is strange that the authors did not consider obtaining evidences or Bayes factors to directly perform Bayesian model selection - for instance, they could have used thermodynamic integration since they used MC to obtain posteriors anyway (c.f., Computing Bayes Factors Using Thermodynamic Integration by Lartillot and Philippe, Systematic Biology, 2006, 55(2), 195-207. DOI: 10.1080/10635150500433722)

Reviewer #3:

In this manuscript, Robert et al. demonstrated that medial SuM sends glutamatergic projections to the hippocampal CA2 region, and stimulation of these projections exert mixed excitatory and inhibitory responses in CA2 pyramidal neurons. Furthermore, they showed that SuM-CA2 circuits recruit local PV basket cells to provide feedforward inhibition to CA2 pyramidal cells, which increases the precision of action potential firing in conditions of low and high cholinergic tone. Finally, they performed in vivo electrophysiology recording to show that stimulation of SuM-CA2 projections can influence CA1 activity. Overall, this is a well-designed study, and the quality of the data is high. The authors performed an impressive amount of electrophysiology recording in acute slices and provided detailed information on how long-distance SuM projection neurons regulate CA2 pyramidal cell activity. These findings provide insights into how SuM activity directly acts on the local hippocampal circuit to modulate social memory encoding. However, there are some concerns that need to be addressed.

1) The authors performed CAV-based retrograde tracing and demonstrated that medial SuM sends glutamatergic projections to CA2. These results are in contrast to a recent study (Li et al, Elife 2020) showing that lateral SuM neurons send dense projections to both CA2 and DG, and the SuM-DG projections release both glutamate and GABA to dentate granule cells. Based on the results from this study and the study from Li et al. does that mean medial SuM neurons are different from lateral SuM neurons in terms of the neurotransmitters they release? The authors need to clarify this point and provide additional ephys data to show that pyramidal cells do not receive direct GABAergic inputs upon stimulation of SuM-CA2 projections using high-chloride internal solution to reveal the IPSCs.

2) The authors claim that SuM-CA2 circuits recruit local PV basket cells to provide feedforward inhibition to CA2 pyramidal cells. While the data presented are supportive, they are not entirely convincing. Specifically, MOR agonist DAMGO is not specific to PV BCs. Though DAMGO has a preferential effect on PV cells over CCK cells, other interneuron types have been shown to be sensitive to DAMGO manipulation. Therefore, these results are subject to alternative interpretation that other types of CA2 local interneurons may be involved. To show whether PV BCs is the sole interneuron subtype involved, the authors may use a P/Q type calcium channel blocker, ω-agatoxin-TK, as P/Q Ca2+ channels are unique to PV BCs. In addition, chemogenetic inhibition of PV BCs was used, but light-evoked IPSCs are not completely blocked. The authors claimed this could be due to partial silencing of PV BCs. However, there is no evidence showing the efficacy of 10µM CNO application in suppressing CA2 PV basket cell activity. These data should be provided in order to draw such conclusions.

3) CCK basket cells are known to excite PV basket cells (Lee et al 2011) via a pertussin-toxin sensitive pathway. Is it possible that SuM-CA2 mediated excitation of PV basket cells includes a CCK intermediary? This point should be discussed.

4) The in vivo recording data showed that SuM-CA2 circuit stimulation decreases the firing rate of CA1 pyramidal cells followed by increased firing rate in these cells. Then the authors performed slice recording and showed that the reduced firing rate of CA1 neurons in vivo is likely caused by increased inhibitory inputs onto CA1 pyramidal cells. Figure 7G-H seems to explain the reduced events in the first phase of the tetrode recordings, but not the rebound part. Is there some circuit component that is lost when making slices? Furthermore, what does SuM-CA2 circuit stimulation do to theta/gamma rhythms in CA1? These data should be available in the tetrode recordings.

Reviewer #3:

The paper titled: "Auditory detection is modulated by theta phase of silent lip movements" the authors investigate visual entrainment to lip movement using behavioral (exp1) and non-invasive physiology (EEG; exp2).

In the first experiment participants engage in the detection of a brief tone embedded in noise. Critically, the tone appears whilst subjects are viewing a silent movie clip. Tones are critically timed with respect to the phase of the theta rhythm prevalent in the lip action trajectory (and its relation to the original audio track). Each trial includes 0, 1 or 2 tones and subjects provide a speeded response when the tone is detected. Tones are also critically presented either during the first half of the clip or the second half of the clip (or both or neither). This latter timing parameter is designed to probe the possibility of an increasing degree of entrainment to visual lip movement as the clip evolves. In the second experiment the findings demonstrated in the exp 1 are met with an analysis of visual entrainment and its impact on auditory sources using EEG and source estimation on data obtained while observers viewed the same silent movie clips passively. The paper is well written, the premise is clear and the findings are interesting and timely. In what follows I outline some questions and concerns that come to mind when assessing the validity of the interpretation of the findings. Those span the experimental and stimulus design as well as the analysis choices made.

1) The behavioral procedure suggests that the tones were pseudo-randomly positioned w/ respect to the quantified theta phase of the lip movement. It would be interesting to understand whether any care was taken to exhaustively sample different phases of the phase of interest in the lip movement. It might be important, therefore to demonstrate that phases were equivalently sampled by chance in the first and second half trials and over the different clips. An inset in figure 1 would make for a good spot to demonstrate the descriptive statistics of target positioning (as a function of phase).

2) Second and somewhat related, wouldn't it make more sense to quantify accuracy based on phase bins? This way no division to subpopulation would be required since each individual could be aligned to their best phase. The methods leave it somewhat unclear whether this was a possibility in terms of the stimulus design (i.e., were there enough phases to accomplish this in the stimulus/tone timing; see previous point).

In addition the subject mean phase of the correctly detected target provides little insight as to the periodic nature of performance. Analyzing whether there is a periodic modulation of the pattern of responses over phase would provide richer, more nuanced evidence for the claims.

3) It would be important and interesting to learn whether the first and second part of the trial has the same MI profile at theta b/w lip movement and audio track. Currently, The characterization of MI was done on the whole movie clips. This is crucial for both Experiment 1 and Experiment 2 interpretation.

4) The distinction b/w the first and second half -- indicating that entrainment takes time to build up is somewhat overstated in the context of this paper seeing that the literature suggests that by 0.5 s entrainment is fully arrived at (among others -- the authors themselves say so in the TINs piece). Other processes such as calibration to a given speaker might take longer, and those might justify (or account for?) the result showing that early vs. late targets differ in the degree to which the phase of the lip action affects performance.

Important details over the stimuli need to be clarified:

5) Did every clip introduce a new speaker to the subject? Thus, time on cl cip also amounts to degree of familiarity with the speaker?

6) Did each clip have the same degree of MI b/w audio and lip movement or were there better (more pronounced) lip clips than others when considering their link to the audio? Would it make sense to add these measures as covariates in the analysis?

7) Is the same target timing used for the same clip for all subjects? Or are the tones truly randomly placed and matched onto clips such that a given clip could appear w/ tones at different times for different subjects?

At the risk of somewhat repeating point #2 above -- within the analysis the following should be considered:

8) The authors establish that in the second half performance there are, in fact, two subpopulations in the sample. Wouldn't this post hoc grouping factor, which isn't obviously motivated be better described by properly delineating performance as a function of phase? I can readily understand that the authors might not have a clear hypothesis over what might be the better phase for performing on an irrelevant tone probe. Nonetheless, if a periodic process is entraining performance once a best phase is identified adjacent phase bins should demonstrate this circular relationship. This would allow for a direct quantification of ALL data together after aligning performance to the best phase bin, per subject.

Finally, the following points pertain for most for the contextualization of this work and the discussion:

9) While the authors discuss at least two mechanisms relating to how entertainment affects growth by the second part of the clip, it would be nice to relate the concrete reading of this effect to cognitive processes that may evolve within these timescales. In other words, learning that tracking takes 0.5 s or learning that visual inputs to frontal cortex take a given time scale to exert impact on auditory sensory regions is another description of the finding. What might these time scales buy me as a speaker and as a listener? What processes might be reflected by arriving at these states of synchrony and top-down control for speech comprehension?

10) The post hoc description of the subpopulations preferred phases is interesting and could relate interestingly to the entertainment literature (from Spaak 2014 in vision through Hickok 2015 in audition and others). Might the authors speculate on what part of speech is characterized by one phase vs. another?

11) The author's conjecture in the discussion of this topic - an additional one - there are recent papers by Assaneo et al. (Poeppel as PI, Nat Neurosci, 2019) that show bi-modal behavior in a spontaneous synchronization task (motor to auditory), which was found to be related to morphological differences in frontal-to-auditory white matter pathways, functional differences AND better learning in a statistical learning paradigm. How do the two sets of bi-modal populations interact? The author's discussion of the motor cortex suggests they would.

Methods section:

The paper by and large is well written. An exception to this would be the methods section. Currently, the methods do not comply with best practices that would generate the work reproducible by others.

Reviewer #3:

In this manuscript, the authors test the long-standing and long overdue "evolution-on-demand" hypothesis of integrons. Using a combination of genetic construction work, experimental evolution, and WGS the authors present a convincing body of work favoring the presented hypothesis. The paper is clear, well written and the authors should be given credit for including experimental data from an integron containing clinical plasmid including resistance cassettes to the last resort antibiotics carbapenems. This is largely missing in the field.

My overall assessment of the manuscript is very positive. The "evolutionary ramp" approach is an elegant way to test the "evolution on demand" hypothesis and the authors provide compelling evidence favoring the evolutionary effects of an active class 1 integrase. However, reading through the manuscript I have three major questions/comments regarding the mechanistic aspects and conclusions of the paper. Regarding the last two points, I believe a slightly more balanced discussion including other possible explanations (such as experimental conditions) would add more balance to the Conclusion chapter and improve the manuscript.

Major Comments:

1) Based on WGS the authors characterize evolved populations and claim to demonstrate extensive integrase driven rearrangements in combination with chromosomal mutations underpinning the adaptations towards both constant sub-MIC and 2- fold increments of gentamicin concentrations.

My first concern regards the crucial control in Figure S2 where control PCRs confirm data from Illumina short read sequencing on whole populations. It is hard for me to follow and understand this figure. I suggest that a schematic figure of each combination of cassettes, primer positions, and expected band length combined with proper lane descriptions should be prepared.

2) Surprisingly, and contrasting integron structures from environmental and clinical samples, the authors provide evidence for a strong predominance of "copy and paste" as opposed to the emblematic "cut and paste" insertions of the gentamicin resistance cassette during experimental evolution. They argue that their data suggest that intI1 has a bias towards "copy and paste" cassette rearrangements.

First, I find the term "copy and paste" somewhat confusing. I cannot see that the underlying mechanism of cassette excision differs between the two outcomes in integron structure. The cassette is in both cases excised (cut) from the ancestral integron before it is inserted (paste) into either arrays. I may have missed something here- but why "copy" and how is this novel?

Second, I am not convinced that the presented evidence provides sufficient support for the proposed "copy and paste" bias of IntI1. As the authors discuss thoroughly, the presence of multiple copies of the ancestral structure provides more "ancestral" integration targets for the excised cassettes. The authors exclude the alternative hypothesis that a second copy of aadB increased fitness as compared to a single copy (as expected from copy and paste). Fitness effects of different arrays are discussed solely on the basis of retrospective analyses of populations that did not go extinct. I would have been more convinced if this was backed by some measure of fitness, for example MIC values of integron arrays containing two aadB cassettes. From Fig 1C it is not unlikely that it could be increased.

3) The authors highlight in the abstract and in the Conclusion section that they found no evidence of deleterious off-target integrase effects. They suggest that integrase activity, rather purge deleterious chromosomal mutations and enable more targeted beneficial adaptive responses.

The authors present cases where likely beneficial off target recombination events occurred. To what extent do the authors think the absence of deleterious off target effects is due to the experimental conditions (continuous increments in gentamicin concentrations combined with strong bottlenecks)?

Reviewer #3:

The authors showcase results from an experimental pipeline aiming at demonstrating how evolution of in vitro cancer models can be exploited to identify somatic genomic and structural variants associated with the emergence of drug resistance.

To this aim the authors unbiasedly selected 5 widely used chemotherapeutic agents via systematically treating the HAP-1 cell line with 16 different drugs then chose those yielding clinically compatible half-maximal effective concentrations. After generating stably resistant clones ) of the HAP-1 parental cell line, across a number of replicates (by culturing in sublethal doses of the selected compounds), the authors whole-exome/whole-genome sequenced their models and compared variants observed in the resistant clones versus those present in the parental line.

In this way the authors identified recurrent loss of function variants across replicates in the drug resistant clones per each drug and were able to reproduce the increase in drug resistance of the parental line by knocking out the genes found altered in the drug resistant clones or they were able to reproduce the same finding by pharmacologically inhibiting genes found to host gain-of-function mutations in the resistant clones. Thus highlighting a new potential target for combinatorial cancer therapy and chemosensitization.

Briefly, this is a nice piece of work showing for the first time that exploiting in vitro evolution paired with whole genome analysis for identifying targets for combinatorial therapy and elucidate the mechanisms involved in the emergence of drug resistance is practically feasible.

The experimental pipeline and the followup validation experiments are well thought and designed and outcomes convincingly support the authors' final claim. There are no arbitrary nor unjustified choices and the showcased platform seems to be robust enough.

I would like to see the following few points addressed/answered:

1) The authors focused only on chemotherapeutics while composing their initial search basin. Would considering also few targeted therapies worthy? or it is known that no effects would be exerted on HAP-1? This should be briefly mentioned.

2) The title of the manuscript can be improved: the authors are deconvolving genomic alterations whose acquisition is linked to the development of drug resistance, thus potential chemosensitising targets or targets for combinatorial therapies. This could be better reflected by the title. As it is now it reads like the main aim is to identify 'innate/intrinsic' targets/cancer-dependencies.

3) Mutagenesis experiments to identify mutations that are linked to the emergence of drug resistance might be mentioned in the introduction, and the following work cited: PMID: 28179366.

4) When mentioning the 'Genomics of Drug Sensitivity in Cancer' portal (www.cancerrxgene.org) the following two works (describing the online resource) should be cited: PMID: 23180760 and PMID: 27397505

5) Figure 1 nicely describes the experimental pipeline presented in this manuscript however it should be completed with a final panel or a couple of panels illustrating the genomic comparison between parental and drug resistant clones to identify SNV and CNV associated with drug resistance.

6) It is not clear what the numbers in the 'fennel' in figure S3A refer to. Resistant clones within an individual tested drug? individual resistant clone or overall cases? This should be specified.

7) As it is presented, Table 1 is not very informative/clear, I would replace it with a barplot.

Reviewer #3:

This work by Kilroy et al., is a nice study on the role of inactivity on DMD zebrafish and the beneficial impacts of neuromuscular electrical stimulation on muscle structure and function in these fish. The clinical presentation of muscular dystrophies is often variable which makes it difficult to predict the disease severity and progression. The key points of this work are (1) Same genetic defect could lead to phenotypic and functional variability (2) Inactivity in DMD deficiency worsens the disease progression in zebrafish (3) Neuromuscular electrical stimulation improves muscle structure and function. While this study summarizes these key points in a detailed manner, many of the mechanistic details leading to these observations are missing.

1) There have been many published natural history studies as well as longitudinal imaging studies performed in human DMD patients. How does phenotypic data in zebrafish compare with longitudinal phenotypic studies in human patients?

2) For data presented in figure 1: authors describe the birefringence phenotype in mild mutants as increased degeneration for three days and then increased regeneration. Could they provide any experimental evidence of "muscle regeneration" mentioned in this statement?. Similarly, they mention severe dmd mutant regenerated throughout this study, however, no experimental data is provided to support this statement. As myotome contains both normal and degenerating myofibers, could improvement in birefringence be a consequence of the growth of those normal myofibers vs regeneration of sick myofibers? The term regeneration has also been used later in NEMS studies and needs to be supplemented with the experimental evidence of regeneration.

3) DMD is caused by damage in sarcolemma and subsequent myofiber detachment. The authors didn't observe any effect on myofiber structure but still found reduced velocity in mutants that were subjected to intermittent inactivity. Could this be due to a slight increase in sarcolemma damage (not examined here) and/or changes in the calcium in muscle fibers? Similarly, what are the effects of extended inactivity on MTJ structure? While authors make good observations with their animal model (as also seen in human and other animal models previously), mechanistic details underlying these changes are lacking.

4) Authors show few transcripts in figure 10C that were restored to WT level in MT on eNMES treatment. What is the role of these genes in DMD pathology or muscle function? Why do authors think a change in these 5-6 genes out of several hundred genes is important?

5) While authors demonstrate proposed ECM modeling in response to eNMES, it will be helpful to present changes in ECM structure in response to eNMES treatment (EM or IF).

6) Previous studies in humans in other animal models have also shown that physical exertion or mild forms of exercise exacerbates the decline in muscle function in DMD deficiency. How are these results comparable to the previously published studies?

Reviewer #3:

Obstructive sleep apnea (OSA) is a common disease associated with intermittent hypoxia (IH) and is linked to health complications. The lung is the first organ to experience the IH and in this study Wu et al uses a mouse model of OSA to identify transcriptional changes in the lung as a whole organ. The authors then also use single cell RNA sequencing (scRNAseq) to further identify transcriptional changes in different cellular populations of the lung. The authors found changes in circadian and immune pathways and that endothelial cells in the lung specifically showed the greatest transcriptional changes. The data will be useful as a reference for the field in understanding transcriptional responses in lung cells exposed to IH.

scRNASeq is an exciting technique that has the potential to identify how different cell populations respond to a stimulus (in this case intermittent hypoxia). However, it provides an enormous amount of data which requires significant processing and interpretation. This paper contains a huge amount of data generated by scRNASeq, yet the actual data section is very short. Given the complexity of information obtained, I think it warrants a more detailed analysis in the results section and discussion. It would be helpful to me if the authors could distil the very large volumes of information into a more extensive discussion of their findings (particularly discussing the figures in more detail). Is the summary finding of this paper that early changes in hypoxia and circadian gene expression drive later disease in the lungs of OSA patients? The abstract seems to focus on hypoxia, circadian and immune changes but the data text section focuses very little on these pathways. More details on the figures shown and tying the figures to the results text would improve this paper and enable further interpretation by readers.

Reviewer #3:

The manuscript by Dr. Vlachos group has demonstrated many important features as well as mechanisms of RA-induced synaptic plasticity. For example, they demonstrated that RA-induced plasticity happens in human neurons as well as in rodent neurons in vivo; discovery that synapodin as a critical mediator of RA plasticity as well as RA effect on the size of spine head, synaptopodin cluster and spine apparatus. Moreover, the effect of RA on in vivo LTP plasticity is very interesting. The data looks solid and supports the authors' conclusions.

However the manuscript can be significantly improved by discussion of their results, in the context with literature data as well as explaining the possible mechanism of their results.

1) RA effect on AMPAR upregulation has been reported to not share the same SNARE mechanisms as electrical LTP (Synt1/7 independent vs dependent). How does RA have the extra effect on the LTP amplitude? Moreover, RA plasticity is recognized as a form of homeostatic synaptic plasticity, i.e., the effect takes hours to develop as shown by the authors of RA incubation of many hours in their experiment on human neurons. How does this compare with their RA manipulations in LTP exp (Is TA injected shortly before LTP stimulus? What do the author think that LTP stimulus does to RA signaling?)?

What about metaplasticity involves RA? any connections to the present study?

2) The authors conclude that RA have effects on spines with or without spine apparatus, however, the authors' data suggest that RA-plasticity is blocked when spine apparatus is eliminated (with synaptopodin KO). Moreover, there is significant overlap of spine size for spines with or without spine apparatus... How do the authors interpret their results here? Is spine apparatus dynamic? can floating between spines quickly? Any literature on this? The authors need to discuss more on the possible ways, with supporting literature data, of how this spine apparatus can affect RA function.

In short, a discussion of the above points will add significance to the study.

Reviewer #3:

In this manuscript, Sachella et al examine the contributions of the lateral habenula (LHb) to fear conditioning. They use 3 different paradigms: (1) a contextual fear conditioning paradigm, (2) a cued fear conditioning paradigm, (3) a combination paradigm where both context and cues can predict shocks. They also manipulate the LHb in several ways: (1) using muscimol, (2) using inhibitory optogenetics, (3) using excitatory optogenetics. The results are thought-provoking and would represent a novel contribution to the field, but I am left confused about some of the major points. My suggestions for improvement/clarification of the manuscript are as follows:

Major Comments:

1) Some important points need to be brought up in the introduction in order to frame the problem the authors are addressing and motivate the study. First, the introduction needs more background on separate circuits controlling cued vs contextual fear conditioning (hippocampus, amygdala). This only comes up in the discussion. Readers also need more background on connections between known structures for fear conditioning and the LHb. There should also be explicit discussion of the well characterized connections between LHb and dopamine neurons, including how LHb inputs help generate reward prediction errors that may be important for fear conditioning. The idea that prediction errors contribute to the authors' observations could be foreshadowed here.

2) In general, the muscimol experiments are nicely done. However, muscimol is always administered during training. I am left wondering whether LHb activity is required during the initial learning of the association or for consolidation later. It would be ideal to also include a test of muscimol infusion immediately following the FC training, during a memory consolidation period. This is important because the authors at times seem to argue that the LHb is important specifically for memory consolidation, but later in the discussion claim that activity during the training (related to prediction errors) is an explanation for their results.

3) I'm struggling with the interpretation of the experiments in Figures 3 + 4 using the cue + context FC paradigm and talking about "reconsolidation." These are really key to the paper so making sure the experiments are clear is a must. From the cue + context test, it seems that having both cues + contexts available for memory provides a much stronger memory. I am uncertain about why the authors think this is so and whether the effect is independent of the LHb? For the "reconsolidation" experiment, I can't figure out what's new. The no-reconsolidation group should look like Figure 2 muscimol group, and it mostly does. The reconsolidation group should look like the Figure 3 muscimol group, and it mostly does. So this looks to me more like a replication of Figures 2+3 (with no vehicle control) than anything else. What did we learn that could not be learned from the experiments in Figures 1-3? The suggestion is that "FC training under inactivation of the LHb creates a cued memory whose retrieval depends on contextual information." (lines 154-155). I don't disagree with this interpretation necessarily but it seems vague, and there is no circuit-level insight as to the mechanism.

4) The ArchT experiments, as the authors already recognize, are problematic because of potential heating and other artifacts. 25s of continuous 10mW green light is a lot. I am not left with much confidence in interpreting these experiments and therefore I am not sure why they are included in the paper. There are other methods of optogenetic inhibition that would be better suited perhaps, or the results could be replicated with chemogenetics, where the authors could ensure DREADD viruses did not spread into the medial habenula.

5) The oChIEF experiments are interesting, but again very difficult to interpret. There is no data showing what the stimulation does to LHb firing, which is a concern given the very long light stimulation (through the whole experiment). Therefore, it is unclear whether the authors' hypothesis that the light stimulation interferes with normal function is correct. The design here also does not take advantage of the temporal precision of optogenetics.

Reviewer #3:

Verhelst and colleagues presented an interesting work about fibre-specific laterality of white matter in left and right language dominant people. A new fixel-based approach was used. Two main results were reported. First, extensive areas of significant lateralization were found in white matter, and second, a cluster of fixels in the forceps minor showed significant differences between people with the left and right language dominance, but no differences were found in other white matter tracts, including the arcuate fasciculus, which is sometimes considered to be relevant to the language lateralization.

The authors suggest that the lateralization of language functioning and the arcuate fasciculus are driven by independent biases, and that the relationship between forceps minor asymmetry and language dominance could be of interest.

1) Arguments against traditional fiber tractography and DTI-derived metrics. I agree with the authors that it is a great advantage of the fixel-based approach to investigate fiber-specific effects. But some arguments in the current paper seem to be misleading, and are not very convincing. For example, The authors wrote that "it has been established that streamline counts from fibre tractography do not represent an appropriate metric to quantify white matter connectivity (Jones et al., 2013)." In some rare cases, this could be correct, but I don't know robust evidence that could support this absolute statement. No empirical data was found in either the present paper or the cited paper, and relevant discussions were mainly on the usage of the term e.g., 'streamline count' and data interpretation. It may be still fair to assume a monotonic relationship between 'streamline counts' and the actual white matter connectivity. The authors may want to further clarify this point.

A similar problem exists for the argument against DTI-derived metrics. It reads like that we should never use DTI-derived metrics in future studies as 'crossing fibers' widely exist in the brain, and that the DTI model could not provide (as) 'reliable and informative results' (as the fixel-based method). My understanding is that these different approaches/metrics could reflect complementary aspects of white matter fibers. I didn't find relevant data or discussions e.g., about the relationship between DTI-derived metrics and the three metrics in the fixel-based analysis (i.e., FD, FC, and FDC). Actually, if the DTI-derived metrics could reflect unique aspects of white matter, the non-significant results in FD, FC and FDC (e.g., in the arcuate fasciculus) could not simply suggest that no differences in every aspect of one white matter tract. Let alone that there are many other metrics that describe regional properties of white matter. Even so, the authors suggested independent biases repeatedly in the text based on the non-significant results in the arcuate fasciculus.

In addition, it reads strange that, while traditional approaches were simply considered not useful in the Introduction, in the Discussion the consistency with previous results based on these traditional approaches was used to support the current findings. This makes me curious what unique information we could get from the fixel-based approach. Each metric has its own advantages and limitations. I agree that the fixel-based approach could provide great advantage in describing fiber-specific effects. A fair discussion is better for readers to understand the results.

2) Arguments against traditional laterality index. The authors spent several paragraphs to support their proposed log-ratio laterality index. Their main point against the traditional laterality index is that the traditional index lacks additivity property. While I agree that the log-ratio is a potential approach for laterality studies, it seems that such an additivity property is not necessary for the laterality index. The main reference cited is an old paper from Tornqvist et al., (1985), which focused on relative changes, rather than laterality. In this reference, a relative change index H is considered as additive if and only if H(z/x) = H(y/x)+H(z/y) in a two-stage change: x-->y-->z. But for laterality study, it seems not to be in this case. Only left (i.e., x) and right (i.e., y) quantities are used for characterizing laterality, but without the third quantity (i.e., z). The additivity property seems to be meaningless in the context of laterality calculation. Further clarification is needed.

In addition, the authors mentioned that the traditional laterality index is 'bounded and therefore lacks the additivity property'. The authors may want to further explain the reasoning behind this statement.

Finally, although a non-linear relationship between the log-ratio index and the traditional index was showed in the Appendix X, but within the commonly observed range of laterality effect size (i.e., from -0.5 to 0.5 based on the results from this paper), the relationship is almost linear (see Figure 5). Particularly for the most widely used formula (R-L)/((R+L)/2), the results are almost identical to the log-ratio values. Based on this, I guess that if the authors used this traditional laterality index, they would get exactly the same results.

The traditional laterality index e.g., (R-L)/((R+L)/2) is widely used, which also makes results comparable across studies. This further makes me doubt the necessity of promoting a new laterality index while it does not provide additional information. Back to the beginning, my comments were based on the assumption that the additivity issue is not a problem for laterality studies. The authors may want to clarify.

Reviewer #3:

This manuscript presents data in support of a model whereby neurons harboring a YAC bearing 128 CAG repeats of the Huntingtin protein show disrupted Ca2+ handling via the endoplasmic reticulum in axons and nerve terminals. Unfortunately, my enthusiasm for the manuscript is relatively low for the following reasons:

1) It is unclear at this point whether YAC-based models are really appropriate since they lack the appropriate genomic control of transcription. This may be why for example one of the stronger phenotypes, the increase in mEPSC frequency, is greatest at DIV14 and diminishes some by DIV18 and is absent by Div21. This of course is not the same trajectory of the disease impairment itself. The authors speculate that the reversal of the phenomenology with older cultures may be from degeneration but there is no data to back up this claim. There seems little reason at this point in time not to use HD knockin mice.

2) The analysis for synapse "density" (Supplement) was only carried out at Div18, a time point where the impact of the YAC is already diminished. Unfortunately, the high degree of variability associated with measuring all possible puncta on a dendrite is not likely to easily uncover what amounts to a ~30% change in mEPSC frequency. I am not convinced therefore that the data in figure 1 cannot be explained in part by synapse density.

3) The underlying physiological perturbations driven by the YAC are deciphered almost entirely using pharmacological approaches, many of which are in themselves ambiguous in interpretation. Ryanodine is a complex drug as it potentiates receptors at low doses and blocks at higher doses. Confounding all of this is the fact that the literature has incubation times that span tens of minutes to hours (and not specified in this manuscript). I was disappointed that the authors did not at least repeat the pharmacology experiments with different aged neurons (DIV14, 18, 21). If disrupted ER Ca or RyR function lies at the basis for the change in spontaneous exocytosis, the pharmacology experiments should at the very least track this phenomenology. Similarly high/inhibiting doses of ryanodine should presumably lead to opposite effects, and this at the very minimum should have been done in the control and YAC neurons.

4) The reported changes in resting Ca2+ are highly suspect. The use of ionomycin should drive the sensor to saturation, and then from the saturated value and knowledge of the dynamic range of the probe, affinity constant, and the Hill coefficient, one can extrapolate back to what the resting concentration is. This has been done with GCaMPs in the past and predicts resting values in the 100-150 nM range (in broad agreement with many previous Ca measurements in live cells). In the experiments here the ionomycin never convincingly reaches saturation, as the response merely rises and recovers making the data uninterpretable.

5) The central problem with the approach here is that there is a lot of inference with what happens to ER Ca2+ in the YAC cells but no direct measurements were made. There are a number of genetically-encoded probes that have been used in the last 5 years to examine the ER Ca in neurons (CEPA1ER, ER-GCCaMP-150, D1ER), and experiments using one of these probes should be done to inform the science here.

6) The experiments claiming suppression of AP-evoked release are very difficult to interpret as there is no control over the stimulus itself. The authors simply rely on removing TTX to let APs fire randomly, something that will be driven significantly by network density, synaptic connectivity, and the balance of excitatory versus inhibitory drive in the cultures. The authors should simply study evoked release by stimulating the neurons expressing physin-GCaMP6m directly and examining the response sizes in YAC versus control neurons.

7) iGlusnFr is a potentially powerful tool to assess glutamate release, but to be interpretable it too needs to be treated in a quantitative fashion. The size of the signal will be proportional to the fraction of GlusnFr present on the cell surface and the amount of glutamate released. If for some reason expression of the CAG repeat led to a smaller fraction of expressed sensor reaching the surface of the neuron, this would artificially lead to changes in apparent DF/F. In order to use this probe in an interpretable fashion the authors need to carry out experiments whereby they correct for the surface fraction of the probe across experiments.

As it stands, this manuscript reports largely hard to interpret phenomenology owing to the narrow tool kit they have applied to the problem (mostly pharmacology and inference).

Other important details:

• There is no mention in the methods (or anywhere else) regarding the temperature of the experiments.
• A more meaningful graphical representation would be showing median +/- IQR rather than mean +/- SD.
• It would be helpful to show the effects of inhibition of RyR on WT (confirm ability to decrease mEPSC by inhibiting RyR) and YAC128 (additional proof that RyR contributes to YAC128 pathology).
• The data on single bouton physin-GCaMP6m need to be extracted for all boutons and then reported as fraction of boutons showing the fluctuations. As it stands, it is unclear if there is a selection bias.
• What was the percentage decrease in iGluSnFr signal at the last time point?

Reviewer #3:

The authors have conducted a very challenging study. The paper is clearly written and the topic of neural function under anesthesia is interesting. However, a significant limitation is that many of the analyses presented here do not provide clear insights into the processes the authors are studying.

-A key issue is that the authors aim to predict who is more or less sensitive to general anesthesia. However, each individual subject was given a different target plasma concentration of propofol, based on clinical scoring. So any difference in behavior may reflect different dosing rather than different behavioral sensitivity to a particular drug concentration.

-The interpretation of increased functional connectivity is challenging in the context of anesthesia, which modulates vessel dilation and systemic physiology. These analyses would benefit from additional information about the fMRI signal characteristics, e.g. amplitude and physiological signals.

-Fig. 3 is used to portray comparisons of wakefulness vs. sedation, implied in the text, but does not include direct statistical tests of the difference between the two conditions, and contrasting p<0.05 with p>0.05 does not indicate a significant difference. The suggestion of reduced cortical responses to auditory stimuli makes sense given that the participants are sedated, but the analysis does not seem to provide information about which aspect of auditory processing is modulated by sedation.

-The statements about response time not being mediated by age may reflect an underpowered study, as age is a strong modulator of anesthetic sensitivity and one group has an n=6.

-While many interesting MRI studies can be done with quite small n, depending on the question being asked (e.g. Midnight Scan Club, high-resolution individual studies), this study aims to conduct structure-based predictions of individual differences in behavior. This type of analysis requires more than the n=6 slow responders used for Fig. 5, as there are many other features that likely vary in a group this small. I appreciate that the authors have conducted a very challenging study, and it is not easy to collect more data, but while many interesting analyses can be done on this type of data, this is not an appropriate sample size for assessing GMV-individual differences associations. Larger samples sizes or within-subjects analyses are needed for robust GMV effects.

-Cluster correction method in 'Analyses of fMRI data' should be specified (and checked, Eklund et al.). The precise statistical method used to assess FDR corrected activity correlations with individual subject response times is not clear; it seems that the ANOVA resulted in non-significant results that are nevertheless being reported as differences using Hedges d?

-The presented evidence does not sufficiently support the authors' conclusion that they "provided very strong evidence that individual differences in responsiveness under moderate anaesthesia related to inherent differences in brain function and structure within the executive control network, which can be predicted prior to sedation.". I would commend the authors on their interesting and challenging experiment, and recommend refocusing the analyses.

Reviewer #3:

Jack and colleagues report that SARS-CoV-2 interacts with RNA to form phase-separated liquid compartments, similar to P bodies and nucleoli, shown here as blobs. The authors then perturbed the system in numerous ways, showing that: i) different nucleic acids give rise to different blobs; ii) that protein cross-linking and mass spec suggests that the phase-separated N is in a different tertiary or quaternary conformation than the soluble N; iii) that some N domains (e.g., PLD, R2) are important for blob formation, particularly when the protein is phosphorylated (by an unknown kinase); and iv) some small molecules can affect the number and size of the blobs. Overall, this story is at a very early stage phenomenology and lacks clear demonstration of physiological relevance. Certainly, the claim that "nilotinib disrupts the association of the N protein into higher order structures in vivo and could serve as a potential drug candidate against packaging of SARS-CoV-2 virus [sic] in host cells" ought to be tested - it would be easy enough to do, though I don't think this would complete the story.

Major comments:

1) Figure 1 is difficult to interpret with the information provided. In panel A, the colors seem to be important, but readers are not given a clue as to what. In panel B, how were the Y axes calculated? What are we really looking at in Figs. 1C and D? Were these on glass slides? Plastic? Was the surface coated, passivized, or otherwise derivatized in any way? What kind of microscope was used? What do the white signals (blobs) come from? Is there a fluorescent label involved? Is this phase contrast? In panel D, please include a buffer only control (no protein) to demonstrate blobs are not simply a buffer artefact. Finally, what N:RNA molar ratios were used in this Figure?

2) For the polymeric RNAs, what were the average chain lengths?

3) In describing Figure 1, the authors state "The shapes of these asymmetric structures were consistent with remodeling of vRNPs into 'beads on a string', as observed by cryoEM." This is wishful thinking. I see blobs of different shapes, but there is no way to know whether these represent N protein "beads" on RNA "strings." Reference 6 cited in the manuscript and showing "beads on a string" model has a scale bar of 50 nm = 0.05 µm, and even there, the N:RNA complex is very obscure.

4) My greatest concern of this work is that no information was provided about the N protein that was used for the in vitro studies. How pure was it? What steps were taken to remove co-purifying nucleic acids? Was it monodisperse? Aggregated? Please include DLS data and show silver stained SDS-PAGE.

5) Similarly, how did the mutant forms of N (Fig. 3A) behave? Were they properly folded? Did the authors check them by CD or SEC? And what concentrations of mutant proteins were used? Without these data, the rest of Fig. 3 is uninterpretable.

1. B. Could the authors please explain what the numbers on the Y axis are and how they were calculated. Also, their disorder prediction predicts dimerization regions to be highly disordered, would they consider a problem with the prediction method?

7) C, D, E what is the N: RNA molar ratio?

8) Could the authors please explain the calculation method used to calculate the % surface area covered by droplets?

9) Fig, 4A and B. Why is [N] so low? In other experiments the authors usually used 18.5 µM, whereas here the concentration was 7.8 µM, almost invisible blobs as observed in other figures provided by the authors (and below ksat, or very close to it).

10) Fig, 4C. What is 1.5 M N RNA? [N] is set to 57.6 µM, much higher than in Fig. 4 A-B assays. Is there a reason?

11) Fig. 4D is missing control cells transfected with GFP only (no N).

Reviewer #3:

The Aizenman lab has previously demonstrated the utility of Xenopus tectum as a model to examine neuronal, circuit and behavioral manifestations of VPA treatment, a teratogen associated with autism spectrum disorder in humans. In Gore et al., they demonstrate that the deficits induced by VPA treatment, including enhanced spontaneous and evoked neuronal activity, are blocked by pharmacological or morpholino based inhibition of MMP9. Inhibition of MMP9 also reverses the effects of VPA treatment on seizure susceptibility and the startle habituation response. Over-expression of MMP9 pheno-copies the effect of VPA, and inhibition of MMP9 in single tectal neuronal blocks the expression of experience-dependent structural plasticity. The results are convincing and add mechanistic insight into circuit and behavioral dysfunction induced by VPA signaling, as well as an expansion of the repertoire of plasticity mediated by MMP9 signaling.

Minor points:

-The time course for the introduction of VPA and MMP9 inhibitors should be reiterated in the results section.

-Fig 1 Please report the number (or %) of tectal neurons in which MMP9 was over-expressed following whole-brain electroporation.

-Does MMP9 transfection change the E/I ratio, as previously reported for VPA?

-Does VPA or MMP9 inhibition change the initial large amplitude/short latency evoked response?

Figure 2: please report statistics for total number of barrages or barrage distribution across experimental groups (latter also for Fig 3).

Figs 3 and 5: The presentation of the immunoblots should clarify if raw or normalized (to Ponceau Blue) data were quantified.

Fig 4: Please report a post hoc comparison following the repeated measures ANOVA

Fig 5: Total growth and growth rates could also be included in the results section.

Minor comments: -The discussion considers a broad range of potential targets of MMP9, including cell surface receptors, growth factors, adhesive proteins, and extracellular matrix components, many of these are left out of the abstract and introduction.

-The statement of page 6 "Increased synaptic transmission observed in MMP9 over-expression tectal neurons is consistent with dysfunctional synaptic pruning" appears at odds with a body of literature in mouse hippocampus, included many papers cited in the discussion, demonstrating the role of MMP9 in spine elongation, synaptic potentiation and synapse maturation.

Reviewer #3:

Lang and col. used mouse models to address the impact of the light and dark cycle and of myeloid conditional knockout of BMAL1 and CLOCK in susceptibility to endotoxemia. As expected, mortality rate increased in animals housed in constant darkness (DD). The mortality rate remains dependent on the circadian time in DD mice and, more intriguingly, independent on myeloid BMAL1 and CLOCK, with persistent circadian cytokine expression but loss of circadian leukocyte count fluctuations. The study is mainly descriptive without mechanistic explanation, which leaves the reader a bit frustrated.

1) Please revise the result section and the legends (for example legends of Figures 3 and 5) to explicitly mention whether experiments with conditional knockouts were performed with LD or DD mice.

2) Line 15 and 80. Saying that DD mice show a "three-fold increased susceptibility to LPS" is true for very specific conditions only, and should not be used as a general statement.

3) Line 99-. Please be more precise in describing cytokine levels (for example, in LD, TNF peaks at ZT10, IL-18 at ZT14 or ZT22 but not ZT18, and IL-10 but not IL-12 peaks at ZT14).

4) Line 105-106. Referring to Figure 1E, it is not straightforward for the reader to understand what is meant by "free-running and entrained" conditions.

5) Figure 2C and 3G. There is a substantial decreased mortality in LysM-Cre+/+ versus WT mice. Any explanation?

6) Figure 5 depicts a protocol with LD and DD mice. Yet, it seems that only DD mice were analyzed. Is that correct? LD mice should be analyzed in parallel as controls.

7) Figure 5 and Sup Figure 5. There are huge differences in leukocytes counts between LysM-Cre+/+ and WT mice. Without being exhaustive, LysM-Cre+/+ display much more macrophages in bone marrow, spleen and lymph nodes, DCs in lymph nodes, NK cells in spleen and lymph nodes at both CT8 and CT20. This is very puzzling and questions about the pertinence of these "control" mice. Additionally, one might expect from these observations that LysM-Cre+/+ mice are more sensitive to endotoxemia, which is not the case (point 5).

8) Line 257. The effect of IL-18 is not totally surprising, since both detrimental and protective effects of the cytokine have been reported in the literature. This could be briefly mentioned.

9) Sup Figure 5A. The gating strategy has to be shown for each organ, separately.

10) Sup Figure 5D. The peritoneal cavity contains not only different macrophage populations with different inflammatory properties, but also different B cell populations including anti-inflammatory B-1a cells (plus NK cells, DCs...). Considering that LPS is injected i.p., more thorough analyses of the peritoneal cavity should be performed to properly interpret results of cytokine and mortality.

11) It is not clear whether endotoxemia was addressed with BMAL1 and CLOCK myeloid conditional knockout mice kept LD. Since time-of-day dependent differences in mortality were much less in DD mice (line 74), we probably expect only marginal differences in DD mice.

Reviewer #3:

This work provides a computational model to explain the change of grid cell firing field structure due to changes in environmental features. It starts from a framework in which self-motion information and those related to external sensory cues are integrated for position estimation. To implement this theoretical modeling framework, it examines grid cell firing as a position estimate, which is derived from place cell firing representing sensory inputs and noisy, self-motion inputs. Then, it adapts this model to explain experimental findings in which the environment partially changed. For example, the rescaling of an environment leads to a disruption of this estimation because the sensory cue and self-motion information misalign. Accordingly, the model describes mechanisms through which the grid cell position estimate is updated when self-motion and hippocampal sensory inputs misalign in this situation. The work also suggests that coordinated replay between hippocampal place cells and entorhinal grid cells provide means to realign the sensory and self-motion cues for accurate position prediction. Probably the strongest achievement of this work is that it developed a biology-based Bayesian inference approach to optimally use both sensory and self-motion information for accurate position estimation. Accordingly, these findings could be useful in related machine learning fields.

Major comment:

The work seems to provide a significant advance in computational neuroscience with possible implications to machine learning using brain-derived principles. The major weakness, however, is that it is not written in a way that the majority of neuroscientists (who do not work in this immediate computational field) could benefit from. It often does not explain why/how it came to some conclusions or what those conclusions actually mean - for example, right in the introduction, "This process can also be viewed as an embedding of sensory experience within a low-dimensional manifold (in this case, 2D space), as observed of place cells during sleep". It also does not provide a sufficiently detailed qualitative explanation of the mathematical formulations or what the model actually does at a given condition. So my recommendation would be to carefully rewrite the work to make it readable for a wider audience. I also fear that the work also assumes significant a priori neuroscience information, so people in machine learning fields would not benefit from this work in its current form either.

It is not clear why place cell input was chosen as sensory input. Place cells also alter their firing with geometry, sensory and contextual changes. Although grid cells require place cell input, place cell firing represents more than just sensory inputs. In fact, they may be more sensitive to non-sensory behavioral, contextual changes than grid cells. Moreover, like grid cells, they are sensitive to self-motion inputs, e.g., speed-sensitivity and, at least in virtual environments, head-direction sensitivity. This point would deserve a detailed discussion.

Reviewer #3:

The authors combine minimal and detailed models of hippocampal theta rhythm generation to understand the underlying mechanisms at the cellular-network level. In their 3 steps approach, they extend previous minimal models, they compare these minimal models with more detailed models and they use a piece (segment) of the detailed model to compare it to the minimal models.

I have a number of methodological issues with the paper. First, both models should be validated against experimental evidence given that the experimental results exist. The validation of a "minimal" model with data from another model is circumstantial and useful to link two models, but in no way is a scientific validation, in my opinion. Second, the model reduction arguments are simply taken as a piece of a large model. This is in now way a systematic reduction, which the authors should provide. In the absence of that, the two models are simply two different models. Third, it is not clear what aspects of the mechanisms cannot be investigated using the larger models that require the reduced models, given that the models do not necessarily match. Fourth, the concept of a minimal model should be clearly explained. They used caricature (toy) models of (2D quadratic models, aka Izhikevich models) combined with biophysically plausible descriptions of synapses. The model parameters in 2D quadratic models are not biophysical as the authors acknowledge, but they can be related to biophysical parameters through the specific equations provided in Rotstein (JCNS, 2015) and Turquist & Rotstein (Encyclopedia of Computational Neuroscience, 2018). In fact, they can represent either h-currents or M-currents. I suggest the authors determine this from these references. In this framework, the dynamics would result from a combination of these currents and persistent sodium or fast (transient) sodium activation. Fifth, from the original paper (Ferguson et al., 2017) their minimal model has 500 PV and 10000 PYR cells (I couldn't find the number of PV cells in this paper, but I assumed they were as in the original paper). This is not what I would call a minimal model. It is minimal only in comparison with the more detailed model. While this is a matter of semantics, it should be clarified since there are other minimal model approaches in the literature (e.g., Kopell group, Erdi group). Related to these models, it is typically assumed that the relationship between PYR to PV is 5/1. This is certainly not holy, but seems to have been validated. Here it is 20/1. Is there any reason for that? Sixth, the networks are so big that it is very difficult to gain some profound insight. What is it about the large networks and their contribution to the generation of theta activity that cannot be learned from "more minimal" networks?

Because of these concerns and the development of the paper, I believe the paper is about the comparison between two existing models that the authors have constructed in the past and the parameter exploration of these models.

I find the paper extremely difficult to read. It is not about the narrative, but about the organization of the results and the lack (or scarcity) of clear statements. I can't seem to be able to easily extract the principles that emerge from the analysis. There are a big number of cases and data, but what do we get out of that? Perhaps creating "telling titles" for each section/subsection would help, where the main result is the title of the section/subsection. I also find an issue with the acronyms. One has to keep track of numbers, cases, acronyms (N, B), etc. All that gets in the way of the understanding. I believe figures would help.

Another confusing issue in the paper is the use of the concept of "building blocks". I am not opposed to the use of these words, on the contrary. But building blocks are typically associated with the model structure (e.g., currents in a neuron, neurons in a network). PIR, SFA and Rheo are a different type of building blocks, which I would call "functional building blocks". They are building blocks in a functional world of model behavior, but not in the world of modeling components. For example, PIR can be instantiated by different combinations of ionic currents receiving inhibitory inputs. Also, the definitions of the building blocks and how they are quantified should be clearly stated in a separate section or subsection.

I disagree with the authors' statement in lines 214-216, related to Fig. 4. They claim that "From them, we can say that the PYR cell firing does not speci1cally occur because of their IPSCs, as spiking can occur before or just after its IPSCs." Figure 4 (top, left panel) suggests the opposite, but instead of being a PIR mechanism, it is a "building-up" of the "adaptation" current in the PYR cell. (By "adaptation" current I mean the current corresponding to the second variable in the model. If this variable were the gating variable of the h-current, it would be the same type of mechanism suggested in Rotstein et al. (2005) and in the models presented in Stark et al. (2013).) The mechanism operates as follow: the first PV-spike (not shown in the figure) causes a rebound, which is not strong enough to produce a PYR spike before a new PV spike occurs (the first in the figure), this second PV-spike causes a stronger rebound (it is super clear in the figure), which is still not strong enough to produce a PYR-spike before the new PV-spike arrives, this third PV spike produces a still stronger rebound, which now causes a PYR spike. The fact that this PYR spike occurs before the PV spike is not indicative of the authors' conclusions, but quite the opposite.

The authors should check whether the mechanistic hypothesis I just described, which is consistent with Fig. 4 (top, left panel), is also consist with the rest of the panels and, more generally, with their modeling results and the experimental data and whether it is general and, if not, what are the conditions under which it is. If my hypothesis ends up not being proven, then they should come up with an alternative hypothesis. The condition the authors' state about the parameter "b" and PIR is not necessarily general. PIR and other phenomena are typically controlled by the combined effect of more than one parameter. As it stands, their basic assumption behind the PRC is not necessarily valid.

The subsequent hypothesis (about PYR bursting) is called to question in view of the previous comments. The experimental data should be able to provide an answer.

The authors' should provide a more detailed explanation and justification for the presence of an inhibitory "bolus". What would the timescale be? Again, the data should provide evidence of that. In their discussion about the PRC, the authors essentially conclude what they hypothesis, but this conclusion is based on the "bolus" idea. The validity of this should be revised.

The discussion about degeneracy of the theta rhythm generation is interesting. However, because of the size and complexity of the models, this degeneracy is expected. Their minimal modeling approach does not help in shedding any additional light. In addition, the authors' do not discuss the intrinsic sources of degeneracy and how they interact with the intrinsic ones.

The last two sections were difficult to follow and I found them anecdotal. I was expecting a deeper mechanistic analysis. However, I have to acknowledge that because of my difficulty in following the paper, I might have missed important issues.

The discussion is extensive, exhaustive and interesting. But it is not clear how the paper results are integrated in this big picture, except for a number of generic statements.

The proposal that the hippocampus has the circuitry to produce theta oscillations without the need of medial septum input has been proposed before by Gillies et. (2003) and the models in Rotstein et al. (2005) and Orban et al. (2005). But the idea from this work is not that the hippocampus (CA1) is a pacemaker, but rather what we now call a "resonator". To claim that the MS is simply an amplificatory of an existing oscillator is against the existing evidence.

Reviewer #3:

The study by Jackson et al. characterizes the progression of the degeneration of axons and dendrites, including metrics on density and dynamics of dendritic spines and terminaux boutons (TBs), in the rTg4510 transgenic mouse model. The authors describe a decrease in the density of both structures, spines and TBs, as well as degeneration of neurites. Repression of the expression of the mutated version of tau was able to partially mitigate some of the negative effects observed in the non-repressed condition. When degeneration of the neuronal process was observed, the loss of a dendritic branch was preceded by a sharp increase in the loss of dendritic spines, while axonal loss was preceded by a long-lasting and progressive loss of TBs. While the findings are interesting, there are several concerns that dampened the enthusiasm on the study:

1) The data obtained with the rTg4510 mouse model must be very carefully interpreted given that the disruption of the endogenous gene Fgf14 that occurs in this mouse model contributes significantly to the neurodegenerative phenotype (Gamache et al., 2019). While the authors acknowledge the possibility that genetic factors other than tau hyperphosphorylation may contribute to the rTg4510 pathology, the results must be put into the perspective of the mouse model rather than into the perspective of the tauopathy exclusively. In this sense, it would be recommended that the caveats of the mouse model be included in the introduction.

2) The authors do not either mention the sex of the animals used in the study or how many mice from each sex were included in each experimental group. This is an important matter because it has been described that the rTg4510 mouse model presents with sex differences in the degree of accumulation of tau (Yue et al., 2009; Song et al., 2015).

3) A big concern is the identity of the neurons labeled. The strategy to label cells is very unspecific and no details are given on their identity. Different subtypes of pyramidal neurons with different densities of dendritic spines and axon boutons may be mixed up in different proportions in each group and batch. In fact, the resilience of different neuron subtypes to the pathology may be different too. If the authors cannot pinpoint the identity of the neuron imaged, an elaboration on this issue must be included in the manuscript. In addition, the manuscript must include representative images of the cortex of both genotypes showing the labeling pattern obtained with their approach. It is recommended to the authors to add more information about the vector.

4) How did the authors estimate the point of divergence between genotypes? The authors mentioned the 30-35 wk and 50 wk as points of divergence - which should be interpreted as the first time points where the differences between groups are significantly different - in lines 180-183. While the Wald test and the Akaike information criterion indicate that genotype is the factor with the most influence on the model estimates, it does not compute statistical differences between phenotypes at a given time point. Regarding the GAMMs, some fits suggest that data at earlier points may be very different between groups (i.e., Fig 2E, 5C, 6C). Is the decrease in density of TBs over time in WT mice significant? How do the authors interpret those fits?

5) Looking at the data in Figures 1E and 2E, one would expect more negative growth values in figs 5E and 6E, indicating a larger decrease in density. They are flat. Are these analyses well powered? Are the data in Figures 5E and 6E not representative?

Reviewer #3:

This paper describes a novel technique for measuring several distinct subcortical components, using naturalistic speech instead of the more typical clicks and tone-pips. The benefits of using extended speech (e.g., stories) include simultaneous measurement of middle- and late-latency components automatically.

The technique is of great interest with many potential use cases. The manipulation of the acoustics is reasonable (replacing voiced speech with click trains of the same pitch), does not degrade intelligibility, and reduces sound quality only in minor ways. The manipulation is also described clearly for others to implement.

The authors also investigate several variations and generalizations of the technique, and their tradeoffs, inducing responses from specific tonotopic bands and ear-specific responses.

The reliability of the ABR wave I and V responses is remarkable (especially given the previous results of the senior author using unprocessed speech); wave III is less so. Being able to simultaneously record P0, Na, Pa, Nb, P1, N1, and P2 simultaneously shows promise for future clinical applications (and basic science). The practical importance of using a lower fundamental frequency (i.e., typical of male speakers), is clearly established.

The technique has some overlap with the Chirp spEECh of Miller et al., but with enough tangible additional benefits that it should be considered novel.

The writing is very clear.

Major Concerns:

"wave III was clearly identifiable in 16 of the 22 subjects": Figure 1 indicates that the word "clearly" may be somewhat generous. It would be worthwhile to discuss wave III and its identifiability in more detail (perhaps its identifiability/non-universality could be compared with that of another less prominent peak in traditionally obtained ABRs?).

Reviewer #3:

In this study, Higgs et al. apply a systematic and hierarchical approach to testing the enrichment of imprinted gene expression in (mostly) adult tissues, culminating in a survey at the single-cell and neuronal sub-type level, which the authors achieve by exploitation of now extensive single-cell gene expression datasets. Arguably, there are no great surprises in this analysis: it reinforces previous studies showing/suggesting an enrichment for imprinted genes in the brain, with functions in feeding, parental behaviour, etc. But, it is conducted in a rigorous manner and makes highly informed inferences about the expression domains and neuronal subtypes identified. This level of detail is beyond any previous survey, therefore, the study will provide an excellent resource (although the fine details of the specific neuronal sub-populations in which imprinted gene expression is enriched are likely to be of interest to specialists only). Having, at all levels of their analysis, access to two or more single-cell datasets provides an important level of confidence in the analysis and findings, although there are some discrepancies between the enrichments found in comparing any two datasets. Moreover, the findings will give more prominence to neuronal domains that have received less emphasis in functional studies, for example, the enrichment of imprinted genes within the suprachiasmatic nucleus implicating roles in circadian processes.

Imprinted expression covers a range of allelic biases and we are still some way from really understanding what an allelic skew means in comparison to absolute monoallelic expression: biased expression in all cells in a tissue or a mosaic of mono- and biallelically expressing cells. So finding an imprinted gene expressed in a given cell type without knowing whether its expression is actually imprinted in that cell type is a problem. And certainly a significant proportion of more recently discovered brain-expressed imprinted genes seem to fall into a category or paternal bias rather than full monoallelic expression. The authors do acknowledge this caveat in their discussion (lines 491-499). Is it possible to stratify the analysis according to degree of allelic bias? Ultimately, scRNA-seq using hybrid tissues will be important to resolve such issues. In this context, the authors will need to discuss findings in the very recently published paper from Laukoter et al. (Neuron, 2020), although that study focussed on cortical neurons in which Higgs and colleagues do not find imprinted gene enrichments.

Another issue that could cloud the analysis, and particularly inference of how PEGs and MEGs could be involved in separate functions, is the issue of complex transcription units. The authors allude to Grb10 in which there are maternally and paternally expressed isoforms largely arising from separate promoters, which also applies to Gnas. There are also cases in which there are imprinted and non-imprinted isoforms. A problem with short-read RNA-seq libraries will be that much of the expression data for a given transcription unit cannot discriminate such differentially imprinted isoforms, as most of the reads mapping to the locus will map to shared exons. This caveat probably also needs to be mentioned in the text.

The authors give some prominence to Peg3 as an example of the role of imprinted genes in maternal behaviours (e.g., line 508) as reported in the original knock-out (Li et al. 1999). However, this particular Peg3-knock-out associated phenotype has been questioned by a more recent Peg3 knock-out in which it was not observed (Denizot et al. 2016 PMID: 27187722), suggesting that the initial phenotype could be a consequence of the nature of the targeting insertion rather than Peg3 ablation.

While a general picture that emerges is of imprinted genes acting in concert to influence shared functions (e.g., feeding), the authors also point out cases in which a single imprinted gene contributes to a neuronal function (Ube3a in the case of hippocampal-related learning and memory; line 511-512) but for which they did not find enrichment of imprinted genes in the relevant neuronal population. This poses some problems, but it could indicate that that particular function of the gene is not the function for which imprinting was selected if the gene is active in other domains, but is rather 'tolerated'. Of course, many imprinted genes will have multiple physiological functions, so the convergence on specific functions probably provides the best (but by no means perfect) basis for discerning the evolutionary imperatives.