Reviewer #2:

This is a nice study that is clearly written and makes use of several datasets. The authors show that a gene signature associated with increased myelopoiesis in utero is associated with increased risk of pediatric asthma. Furthermore they show that cord blood serum PGLYRP -1 is associated with reduced risk of pediatric asthma and increased FEV1/FVC. Interestingly sIL6ra which is derived from neutrophils but not associated with neutrophil granules did not show any association with pulmonary outcomes. This suggests that it is the neutrophil granules rather than the neutrophils per se that are the problem association. The following should be addressed:

1) While the manuscript is clearly written, the message regarding PGLYRP-1 is at times confusing. The manuscript is clear that PGLYRP -1 is inversely associated with mid childhood asthma risk. The discussion however refers to animal models where PGLYRP -1 is proinflammatory and is associated with increased airway resistance and allergen sensitization. The apparent disparity should be clarified.

2) What is the proposed role of neutrophil degranulation in the pathogenesis or long term susceptibility to asthma?

3) While it was not the focus of the current study and maybe beyond the scope of the data it would be interesting to know if there is any association with the subsequent development of adult asthma.

Reviewer #2:

The paper submitted by Girard-Buttoz and colleagues asks whether and how early maternal loss affects cortisol levels and diurnal slopes among wild chimpanzees at Tai Forest, Côte d'Ivoire. The major claim of the paper is that, like humans, chimpanzees experience altered HPA functioning after maternal loss, including alterations to both diurnal slope and overall cortisol levels. However, their chimpanzee orphans exhibited patterns in diurnal slope that were opposite to their predictions (predicted blunted slopes, observed steeper slopes). The authors should be commended for their efforts in collecting a large number of samples for this analysis. However, I am not convinced that it is sufficient for investigating the hypotheses put forth here and, therefore I am also not convinced that their results are solid. I also have concerns about the theoretical grounding for the paper.

1) My principal concerns with this paper, as written, revolve around the methods/results. First and foremost, I am not convinced that the authors have the sufficient sample size to evaluate the predictions/hypotheses outlined in the introduction. While 849 urine samples is a large number, and again, their efforts here should be commended, the sample spread is actually quite thin once it is spliced up into appropriate categories, especially considering how many samples were collected per individual year, on average. As the authors indicate throughout and especially when describing their modeling approach, cortisol is inherently a very noisy hormone impacted by myriad factors- including age in at least one other densely-sampled chimpanzee community. I'm also surprised that time of day was modeled quadratically. It is my understanding that humans, other populations of chimpanzees, and other mammals follow a sigmoidal curve which should be modeled with a third-order term as well. For these reasons, it's difficult to tell whether model 1A is not significant because of insufficient sample or a true lack of predictive power. Additionally, I'm concerned that the paper seems to focus so much on the results from a single model term in a model that did not reach significance.

2) Despite acknowledging that the "significance of these predictors should be interpreted with caution" because model 1a did not reach significance, the authors make very strong claims about the results in the discussion- and also feature the finding of that model in the title of the paper. That seems problematic to me- especially because the insignificant model results (more intense diurnal slopes among immature orphans) diverge from the expectations set forth by other works in humans and non-humans. The finding that this is to do with higher-than-expected morning cortisol is puzzling given that evening levels are generally considered more responsive or plastic. However, this could also be an artefact of fitting the models without the third-order term for time.

3) The introduction needs refinement to help clarify and specify the authors' arguments.

(a) Does the biological embedding model always lead to negative fitness outcomes? Or is it possible that phenotypic adjustments might be adaptive, or even just making the best of a bad job (e.g. earlier death, but not death today)?

(b) Throughout the introduction it is unclear whether and where the authors refer to the human clinical literature as opposed to animal literature. It is also unclear how human patterns are similar versus different from those observed in animals. Further, I would recommend that the authors include a deeper review of the animal literature (e.g. early experimental work with macaques, cortisol at other chimpanzee field sites/captivity). It's also unclear whether and where the authors refer more broadly to early life adversity (and what this means for humans vs. animals) versus more specifically to maternal loss. Additionally, there should be further discussion specifically related early maternal loss (rather than "early life adversity" which can include a lot of different factors) focused on the nutritional and social obstacles associated with early maternal loss, how these related to HPA functioning, and how these effects are expected to change during development (Plasticity? Flexibility? The role of HPA in responding to changing environmental conditions?). What about the adaptive calibration model which posits that the HPA can readjust during particular periods of developmental reorganization?

4) It is difficult to assess the discussion without first dealing with the problems in the introduction/methods. However, despite their claims in the results section, it does not seem that the authors interpreted the results of model 1a with caution.

Reviewer #2:

The manuscript addresses an interesting question: whether genetic effects of common variants on educational attainment (EA) differ between individuals with and without psychiatric diagnoses. The dataset they use is ideally suited for such an analysis. The authors find evidence that the influence of common variants on EA is attenuated in individuals with a diagnosis of autism spectrum disorder (ASD) or ADHD.

My main concern with the paper is the statistical analyses used to support the authors' conclusions. The authors draw conclusions from dividing individuals into subgroups and comparing the R^2 of the EA PGS between those subgroups. This analysis is liable to bias due to range restriction: if the subgroups have been selected based on low/high education, then the R^2 of a predictor will tend to be lower in the subgroups than in the overall sample. Furthermore, here the selection into the subgroup (here diagnosis with ASD or ADHD) itself is related to both education and the EA PGS, which could be contributing to the differences in R^2 the authors observe between subgroups.

A more powerful and robust analysis would be to fit an interaction model in the full sample. The authors could regress individual's EA jointly onto their EA PGS, their diagnoses coded as binary variables, and the interactions between the EA PGS and the diagnoses codings. The authors could do this jointly for all diagnoses in the full sample, which would account for comorbidities between psychiatric disorders. If the influence of the EA PGS is truly weaker in ASD and ADHD cases, there should be a negative interaction effect between the EA PGS and ASD and ADHD diagnoses, which can be tested with a simple statistical test for a non-zero interaction effect.

It could also be worth first regressing the EA PGS onto the psychiatric diagnoses, and taking the residuals before assessing whether there are interactions between the EA PGS and ADHD/ASD diagnosis. It is possible that correlation between the EA PGS and ADHD/ASD diagnosis could generate a spurious interaction effect in the above analysis.

It is interesting that controlling for SES appears to mediate the (potential) interaction between EA PGS and ADHD diagnosis. However, I worry again that this could be a function of SES influencing ADHD diagnosis. SES and its interaction with both EA PGS and ADHD diagnosis could also be included in a full interaction model that could help interpret this finding.

The authors construct the PGS by using a pruning and thresholding approach. This is known to be suboptimal, which may explain why their R^2 is lower than in other studies. The authors could use LD-pred or other methods that account for linkage disequilibrium and non-infinitesimal genetic architectures. In the EA GWAS from which the score was constructed, the best R^2 was found by applying LD-pred to all variants without p-value thresholding.

The hypothesis that indirect genetic effects differ between psychiatric cases and controls is interesting. Do the authors have sufficient sibling data within their samples to test this?

Line 581: Closely related individuals were removed from the analysis. Why? How many were removed? Could inclusion of these help assess the hypothesis about indirect genetic effects and improve power? The authors could use a mixed model regression to control for relatedness without having to throw individuals out of their sample.

The grammar in the writing of the paper is a little odd at times. Often, definite or indefinite articles are omitted preceding nouns, such as in 'association of EA-PGS' in the abstract, which should be 'association of the EA-PGS'.

line 54: 'strongly influences', I think this is a little overconfident in its assignment of causality to highest level of education, perhaps 'strongly associated' would be better

Paragraph 3 of the introduction: the authors should mention population stratification and assortative mating as possible mediators of the association between EA PGS and EA, especially when referencing the drop in association strength in within-family designs

I found the decile based analyses a bit pointless. By arbitrarily dividing a continuous outcome into discrete subgroups, the authors are losing power and not gaining much compared to simply performing linear regression, which they already do. I would relegate these to supplementary figures.

Line 452: I think that the stated equivalence between low EA PGS and learning difficulties goes a bit too far here. I understand the point the authors are trying to make, but I think it should be phrased more carefully.

The authors used an MAF threshold of 5% for construction of the score. Typically, a threshold of 1% is used for construction of PGS from summary statistics by software such as LD-pred.

Line 580: the authors state that an EA PGS based on summary statistics from European samples cannot be used to predict EA in non-European samples. This is not true. It is true that the prediction accuracy is attenuated, but it is not zero.

Reviewer #2:

General assessment and major comments:

The study addresses a timely and important question of the role of potential modulations in perceptual decision-making in the atypicalities observed in perceptual processing of individuals diagnosed with autism. The manuscript is important, and the methods used are sound.

There are however some issues to consider:

Thresholds, or other indications of sensitivity and precision of performance in the task are not detailed (although judging by the individual psychometric functions presented in the figures, slopes seem less steep in ASD). Was sensitivity considered in any way in the analysis? wondering how the model fitting would look like and how it would interact with the biases. Bias magnitude could vary as a factor of noise or sensitivity.

Also, could larger consistency bias in the ASD group result from weaker performance, more lapses of attention etc.?

Age range is quite large. Did you check for age-related differences? I understand the sample size is not big enough to analyze data across different age groups but maybe as a covariate? (there is also the problematic issue of determining sample size of children based on the study in young adults).

Not sure why the effects of prior stimuli are considered adaptation effects, particularly in the first experiment where stimuli were briefly presented. Also, regarding the argument in the Introduction about Bayesian priors producing positive effects -- there are other prior effects that may cause 'negative effects' in relation to prior expectations (for example, in perceptual illusions such as the weight-brightness illusion).

Can you think of a reason why controls did not show significant consistency bias in their responses in the heading discrimination?

There is some wording in the reports of the statistics such as 'more significant' or 'more marginally' that needs to be rephrased.

Were the analyses corrected for multiple comparisons?

Usually RTs in this sort of perceptual task are longer in ASD. Wonder how this is not the case here, although instructions for the subjects emphasize speed and accuracy.

I agree with the authors. It is interesting to look at correlations between the effects of prior choices and clinical scores of repetitiveness and flexibility in ASD. Did you look at the correlation between the effects of prior choices and SCQ scores across the two groups? Previous work documenting correlation between autistic traits (AQ) and modulated perception provided important information about the generalization of the findings to the broader spectrum of autism in the wider, nonclinical population (see Lawson, Mathys, & Rees, 2017; Hadad, Scwartz, & Binur, 2019).

Reviewer #2:

Nonlinear microscopy is in the unique position that high-resolution images of cells and other tissue components can be obtained in live tissue. However, scattering and absorption limit the penetration depth. The impact of nonlinear microscopy in biomedicine and biology would be much improved if higher imaging depths can be achieved. Lately a few key studies have appeared achieving this. This manuscript contains a well-motivated extension of this research, in particular on the benefits of high-pulse-energy low-duty-cycle infrared excitation near 1300 and 1700 nm over 2-photon excitation, in heterogenous and dense tissue. The authors compare three types of excitation, at 1650 and 1300 nm at 1 MHz and at 1100 (or 1270) nm at 80MHz. They characterize photodamage in the tissue and determine the limits for power densities to stay below that. They study the achieved resolution at high depth for each of the processes and show a deeper imaging depth is resolved in bone and tumor core with 3P and 4P than with 2P. The article is a very solid and extensive study.

Though I have no major concerns with article, I do have some minor points:

l.57: Are the resolutions reported for 2-, 3-, or 4- photon processes. Do you not expect these to differ for the different processes? l.60 It is not explained that power is increased from X to Y, instead the peak power of 87 nJ in L 67 is not found back in fig. S2.

L. 103 Given is the power at the sample surface, after which the readout for cell stress via Ca imaging is done (very elegant). Is not the imaging depth of the readout relevant too, as it is probably the power density at the focus which matters. What imaging depths can be reached with this low power? This comes back later, but would be good to mention here.

L.110 The phrase 'Furthermore' confuses me. I guess the authors mean to say that with their 2.8-8.7 nJ of power they were well below the 100 mW level? Which is kind of obvious at 1 MHz?

L. 126 Some words are missing, 'but 1180'.

Why do some signals show a peak in intensity in fig. 3C and G rather than a slope?

Reviewer #2:

The authors quantify virulence factors in Cryptococcus neoformans and C. gattii in a large number of clinical isolates and correlate these virulence factors to survival in a g. mellonella infection model and to the clinical outcome. The authors found a correlation between secreted laccases and disease outcome in patients. In addition, the authors show that a faster melanization rate in C. neoformans correlated with phagocytosis evasion, virulence in the g. mellonella model and worse prognosis in humans.

The manuscript is well structured with an appropriate abstract summing the main findings, a clear introduction, well described methods section and appropriate number of figures and tables. The results are clearly described.

1) The authors identify and acknowledge the most important limitation of the study: line 365-366 the patients were treated with different regimens in distinct health services. This reviewers agrees this is a limitation. However, to get a feeling about the impact of these differences the authors should indicate how the patients were treated and whether there were differences in patients that died and survived. Without this information clearly presented, I cannot interpret the correlations between virulence factors and outcome found in this study. Perhaps the authors can show how many patients that were included in the phenotype-survival analysis, that died and survived were treated according to Brazilian guidelines.

2) The melanin production evaluation assay is an important tool that the authors use in this study and the measurements from these assays were correlated with G. mellonella and patients survival and thus are essential to the conclusions of the study. The method is well standardized, and the authors show elegantly that the outcomes are highly reproducible. Can the authors describe when melanization occurs: does it occur in mature colonies and may growth rate itself may influence the measurements? Do isolates with a high growth rate/colony maturation have a low T-HMM or high melanization Top. Have the final colonies of different species have a different final cell number after 7 days incubation and how does this correlate to melanization? And how does the growth rate/ budding rate/ colony maturation/ correlate to G. mellonella survival?

3) The figures 1-5 give a clear picture of the wide distribution and variation of virulence parameters e.g. the distribution of melanization kinetics parameters, the distribution of capsule sizes, GXM secretion and LC3 phagocytosis. But what does this distribution mean, it only shows that the isolates are not the same but does not contribute majorly to the final conclusion. Can the authors think of a way to give more meaning to these figures: e.g. indicate with colors which isolates were retrieved from patients that eventually died and which survived (although this may be inappropriate as not all clinical information is available. Figure 6 really gives meaning to the numbers displayed in figure 1-5. Perhaps move some figures to the supplementary file.

Reviewer #2:

The topic of this manuscript is the basis of continuous and episodic bursting electrical activity in developing spinal cords. The approach used is to employ a simple mathematical model as a representation of the central pattern generator underlying the bursting pattern, and examine how the properties of bursting change with variation in three key system parameters. Some of the model predictions are tested in an actual in vitro spinal cord preparation. Although I enjoyed reading the manuscript, I have some serious concerns about the model that is employed, which I discuss below.

Major concerns:

1) The model is a half-center oscillator (HCO) in which one cell inhibits the other, resulting in anti-phasic electrical activity of the two cells. (Each "cell" actually represents a cell population, so the model is a mean field model.) This is certainly one way to get electrical bursts. However, it is not at all clear that such a HCO structure exists in the developing spinal cord, or that there are neural populations with this anti-phasic activity. If such data exists, it is not mentioned in the paper or cited. Indeed, the recordings in Supp. Fig. 1 show extracellular neurogram recordings from ventral roots in different lumbar segments and in which the bursting appears to be synchronous. So I see no evidence that the HCO model reflects the actual neural circuit, other than the fact that it can produce bursting and episodic bursting. This does not mean that such a phenomenological model is without value, but it should be made clear to the reader that that is what the model is. Also, the next two points below do appear to cast doubt on the utility of this model.

2) In Fig. 3 it is shown that the inter-episode interval (IEI) is increased in the model when the conductance g_h is reduced. Because of this, the episode period (EP) also increases. The data, also in Fig. 3, show the opposite. They show that blocking the h-type current decreases the EP. This seems like a flaw in the model, since it is the h-type current that is responsible for episode production (at least I think it is, see point 4 below). The discrepancy is mentioned in the manuscript, but only briefly and it should be fully addressed.

3) In Fig. 5 it is shown that, in the model, there is a very small interval of g_NaP where episodic bursting is produced. Otherwise, the model produces continuous bursting (for larger g_NaP values) or silent cells (for smaller g_NaP values). However, the data that is also shown in the figure indicates that blocking the NaP channels has little effect on episodic bursting. This is another serious discrepancy between the model and the experimental data.

Points for clarification:

4) It appears from Fig. 1 that episodes stop when h-type current activation slowly moves to an insufficient level to kick off a new burst. Logically, a new episode would start once that activation grows back to a sufficiently large value. Is this right? The mechanism for episode production is never discussed, and it should be.

5) The model is deterministic, yet there is variation in burst duration and episode duration (see Fig. 3). What is the source of the variation? Does this mean that the episodes are not periodic?

6) The model has a multistable region in parameter space, and much is made of this in the Results and the Discussion. In Fig. 6, it was demonstrated that hyperpolarizing pulses could switch the system from one behavior to another. Can this be done experimentally in the in vitro prep? If so, was it tried?

Other:

7) Discussion is too long and touches on things that were far from the focus of the manuscript. For example, there is about a page and a half of text discussing short term motor memory (STMM) although the Results section did not focus at all on homeostatic functions of the circuit or STMM. Furthermore, some points were made several times during the Discussion, where one time would have been sufficient.

8) Almost two pages of the Discussion was dedicated to multistable zones, yet in the model the multistable zone was tiny, and there was no evidence that the experimental prep lies in or near that zone. The authors state that in actual neural circuitry there could be a much larger multistable zone, which is true, but there also may be none at all. This discussion appears irrelevant.

Reviewer #2:

Amyotrophic lateral sclerosis (ALS) used to be considered primarily a disease of motoneurons. Recent work using mouse models of ALS has revealed that pathological changes can also be detected in spinal interneurons, particularly inhibitory interneurons, and that some of these changes can be detected before birth. The present paper is the first to directly examine the electrical properties of spinal inhibitory interneurons in a mouse model of ALS and show that some of these are altered in the neonatal period well before the mice start to exhibit symptoms. The authors show that SOD1 Lamina IX neurons are smaller than the Lamina IX WT neurons whereas no differences were found between WT and SOD1 neurons outside Lamina IX. They also use whole cell recordings to reveal that putative 'Renshaw cells' are less excitable in SOD1 mice than wild type animals whereas non-Renshaw inhibitory SOD1 neurons are more excitable.

Major Comments

1) The authors claim that Renshaw cells are in lamina IX, when they have been shown to be located mostly in the ventral part of lamina VII, ventromedial to the motor nucleus (Alvarez and Fyffe, 2007). In addition, not all calbindin+ neurons in lamina VII are Renshaw cells. From the location of the whole cell recordings shown in fig.2, it seems likely that most of the recorded neurons are not Renshaw cells because they are outside the classical 'Renshaw' area. It is not clear why the authors are focusing on glycinergic neurons in lamina IX, as there is no evidence that they belong to a unique class or that they are presynaptic to motoneurons.

2) The concern about the identity of the Renshaw cells obviously undermines the statistical modeling to segregate Renshaw versus non-Renshaw cells. Furthermore, it was not clear from the text whether the model used both WT and SOD1 calbindin-positive neurons to define 'Renshaw cells'. Assuming it did, and given that there were changes in the electrical and morphological properties of the calbindin+ SOD1 neurons, is it not surprising that they could be grouped with the WT 'Renshaw cells'?

In addition, the characteristics the 'Renshaw cell' population used for the model are not clear. On line 186 that it states that 15/23 of the whole cell recorded interneurons were positive for calbindin. Does this refer to 15 WT and 23 SOD1 neurons? Thus 38 neurons were calbindin positive. Of the remaining 21 neurons how many were calbindin-negative and how many were not tested? How many of the 38 calbindin-positive neurons had their dendrites reconstructed sufficiently from the intracellular fill to be used in the model? The model predicted that 80% of the 59 patched interneurons were Renshaw cells. How many of these were in the calbindin-negative group and how many were in the not-tested group? The spatial distribution of these groups should also be plotted. However, it seems very unlikely that 80% of the recorded cells are Renshaw based on their location as shown in fig.2B.

Second it would have been useful apply the model to known non-Renshaw cells, to establish that it was not generating too many false positives. Another way the authors could test the model is to establish if it could distinguish WT and SOD1 neurons based on their morphology.

3) The authors suggest that the reduced excitability of 'Renshaw cells' might contribute to the excitability changes seen in motoneurons. However, based on their own data, this is not a straightforward conclusion. They find that 'non-Renshaw cells' are hyperexcitable and since this population would include 1a inhibitory interneurons and other premotor inhibitory interneurons, it is not clear what the overall effect on motoneuron excitability would be. Additionally, because the authors suggest that 'Renshaw cells' are less excitable this would presumably lead to reduced inhibition of 1a inhibitory interneurons counteracting a potential loss of inhibition onto motoneurons from Renshaw cells.

Reviewer #2:

Kandul et al. present an interesting study that could lead to important improvements on the use of homing-based gene drives. However, there are a number of things that should be addressed to improve the manuscript for better comprehension by readers.

Overall the manuscript presents a load of data. But the presentation of these data could be made in a better digestible way. The authors should go over their manuscript with a reader in mind, that is interested but not necessarily knows all the relevant literature in the very detail.

Abstract (line 18): Please remove "inherently confinable" from the abstract. The drive is indeed designed in a split drive design, however, all the experiments were done in a homozygous Cas9 background. Therefore, there are no experimental data for a split drive provided in this manuscript. The split situation seems to be here more for a practical reason to be allowed to do the experiments in a less stringent laboratory environment. Thus there are no experimental data that would support the confineable nature of this drive. Actually there are not even modelling data to this. Thus, such a statement should not be put in the abstract. This manuscript is not a demonstration of a confineable drive.

Results (line 124): How was Pol-gamma35 identified? It would be interesting to the reader to get to know about the exact reasoning, why this gene was chosen. Or were there several ones chosen before and this turned out to work the best or was the easiest to design. This could be very interesting considerations important to the field.

Results (lines 147-148 Fig. 1B; lines 155-156 Fig. 1C) and Methods (lines 698 and 706) and Figure 1 (both Figure and legend): The addressing of the Figure panels and the writing to it don't fit! Has there been a rearrangement of the Figure that was not worked through the text? When referring to "B" in the text, it is still about Act5C-Cas9 and the nos-Cas9 data are in the text referred to Fig1C! But Fig1C is BLM! In current panel Fig1B, what does "all" mean below the X-axis? This is not comprehensible. Panel C is not really described in the Figure legend!

Results (line 253), Discussion (lines 526-527), and supplementary Figure 1 (line 1101). "converting recessive non-functional resistant alleles into dominant deleterious /lethal mutations" is completely misleading! There is no "conversion" and how should that be done molecularly. There is a continuous removal of such alleles from the population because of lethal transheterozygous conditions caused in the drive. However, there is no active conversion of such alleles into dominant lethal ones. This needs to be clearly rewritten to avoid the misleading idea. Supplementary Figure 1 also seems to have a slight conceptual problem. What are "cells" (rectangles) with a red frame and a green core? Green means at least one wt allele (this must include the recoded rescue allele!). Red means biallelic knock-out: thus a red cell cannot have a wt allele. Thus what is a red-framed green core cell? To explain the removal of R2 alleles, a depiction of yellow framed red core cells in the germ line would be helpful, since this would explain how R2 alleles are selected against and might be continuously removed from the population!

Results (from line 424 to end of results): Before going into the modelling, the reader should be clearly informed about all the different approaches that are now to be compared. This is currently not done well, if at all! Thus moving current Fig 6 before current Fig. 5 might clearly help! Also a better explanation of the panels in Figure 6 is necessary as well as a correction of Fig6 Panel E! A comparison of a great number of the currently approached toxin-antidote (gene destruction - rescue, but not killer-rescue!) systems is greatly appreciated. However, the authors cannot expect the general reader to know about the small detailed differences between the systems that are compared here. Thus the authors need to provide some explanations and categorization of the different approaches here and also cite all the respective literature.

-First subdivision: Non-homing (interference-based drives) VERSUS Homing (thus overreplication-based drives). This will also help them to better understand why the interference-based drives (TARE and ClvR) are more sensitive to fitness parameters than overreplication drives.

-Second subdivision: same-site VERSUS distant site. This is important to understand the difference between the here modelled TARE and the CLvR. Actually ClvR is a TARE, but you use TARE here more specifically as the results in the respective paper are demonstrating only a same-site TARE! But this needs to be clearly stated here!

-Third subdivision: viable VERSUS haplosufficient VERSUS haploinsufficient. This also needs to be clearly depicted in labelling panels C to F of Figure 6, which are currently hard to grasp what the essential differences are, before looking at the panels in detail: C: HGD of viable gene (HGD) D: HGD of viable gene with rescue (HGD+R) E: HGD of haploinsufficient gene with rescue (HGD-hi+R). THIS PANEL NEEDS MAJOR CORRECTION!! F: HGD of haplosufficiant (essential) gene with rescue (HomeR)

-Forth subdivision: split VERSUS non-split. Here for the split HGD situation, the respective papers of which the current authors are co-authors should be cited: Kandul et al. 2020 (actually published end of 2019 and still cited as biorxiv Archives article 2019a!?) and Li et al. 2020, Elife). In addition, it is also important to state clearly that "split or two locus" is completely independent of the "distant site" concept! The reader needs to understand the differences of the systems that are compared here, without having the reader to go to the respective publications themselves and then try to find out what the differences really are. This is not so obvious and the current authors have a clear chance here to do that and help the reader in the mists of all this similar but still distinct approaches.

Figure 6 Panel E: This depiction is not consistent within itself, not consistent with the legend, and not consistent with the cited literature!

-Why should the rescuing drive construct over the wt allele be lethal as indicated in the right two boxes?

-The cited paper Champer et al. 2020b, which is by now also published in PNAS! clearly states that there is maternal carry over, which actually makes it so hard to use and is probably only working via male propagation. In the Figure legend, it is said that "maternal carryover and somatic expression ... are empirically unavoidable", which is in contrast with the depiction! The legend then also states that this is "unachievable". This should be better replaced by "hard to achieve", since the approach is published and seems to drive, even though probably just via the males! Thus the depiction of panel E needs to be thoroughly revised.

Discussion (lines 499-500): The haplolethal HGD works (admittingly poorly) despite the maternal carryover (Champer et al 2020b). Therefore, your statement needs to be refined or deleted: "requires germline-specific promoter that lacks maternal carryover" is not consistent with the published paper! The drive could go via the males because then you do not have maternal carry over! And homing based drives can go via males and do not necessarily have to be promoted through females, see also KaramiNejadRanjbar et al. 2018.

Discussion (lines 540 to 543). This sentence is based on an old but clearly overruled idea! NHEJ repair is not restricted to a time before the fusion of the paternal and maternal genetic material. It has been clearly demonstrated that R1 and R2 alleles are also generated in the early embryo after the zygote state (Champer et al 2017, KaramiNejadRanjbar et al. 2018). Actually, all of the authors' Figure 1C and Supplementary Figure 1 are about NHEJ mutation in the early embryo causing "BLM". Thus this sentence is inconsistent with current beliefs and also with the authors' own writing!

Figure 4: Panel C graph: Why is, in the controls, the transgene consistently and significantly higher inherited to the next generation (0). It is about 75% progeny sired by the transgenic fathers compared to the wild type fathers? Was there an age advantage of the transgenic ones or whatever other fitness factor? This is surprising and no explanation is given at all! In contrast, in the Cas9 background in generation 0, less than 50% carry the drive allele, which is probably due to induced lethality. But this should also be commented upon. In the legend it is stated that 7 of 9 flies carried an R1 allele heterozygous to an R2 allele. What about the other two?

Reviewer #2:

This work from Beier et al. elegantly dissects the rod circuits contributing to the mouse pupillary light reflex through ipRGCs. The authors combine multiple genetic mouse models with electrophysiology and behavior to demonstrate that the primary rod pathway is the primary driver of the dim light pupillary light reflex, and that the secondary pupillary light reflex cannot effectively compensate for this pathway if it is lost. My technical comments are minor. This will be a welcome addition to the field of ipRGC research. My main concern, which I will leave to the editors, is that the actual advance may not be substantial enough.

This is the first study to attribute the rod contribution to the PLR to the primary rod pathway. Though elegant, the fact that the primary rod pathway through ipRGCs is the major contributor in low light and that both primary and secondary pathways contribute to the photopic light PLR is not particularly surprising given the previous clear demonstration by the Hattar group that the rod pathway itself is required for the pupillary light reflex (Keenan et al., 2016).

The authors do convincingly show that the OFF pathway cannot drive the PLR, but again this is in agreement with data showing ipRGCs are the sole conduit for light to drive the PLR (Güler 2008; Chew 2015) and that all ipRGCs get info primarily or solely from the ON pathway (Dumitrescu et al. 2009 and Schmidt 2010, etc.).

Is 1 lux of mixed wavelength light truly in the scotopic regime? How was this calculation/determination made?

Was there any difference in the dark adapted pupil diameter between each of the mouse lines?

Reviewer #2:

In this study, Zhang et al. use a semi-novel method to track acyltransferase activity using fluorescently labeled palmitic acid (NBC-16:0) to track where specific lipids are incorporated with subcellular specificity. They show that NBD-16:0 can be incorporated into different lipid classes that segregate based previously known on subcellular specificity. While this is an interesting technique, it is difficult to determine how much fidelity this method has in recapitulating biological function without additional experimentation, orthogonal measurements, and a more descriptive methods section.

Comments:

1) The authors do not specify which lysophospholipids were used in their study. In the method section they specify that they came from Avanti, but there are >100 different lPLs in their catalog. Also, the authors give a range of lPL concentrations in the methods, but do not specify which concentration was used for which experiment. Without this information and other unspecified aspect of their studies, interpreting subsequent experiments is difficult.

2) One potential advantage of this method is that it is a method to track endogenous lipids in live cells, however the authors show the NBD-16:0 transporting to lipid species where palmitate is almost never measured. For example, the use of the transport of NBD-16:0 to CL as evidence this is working. However natural cardiolipins are almost completely devoid of 16:0. In mammalian cells >80% of the fatty acids in CL is 18:2 with most of the remaining being 18:1 and 18:3. Similarly (assuming you are using sn-1 lPL-16:0), phospholipids with two 16:0 are extremely rare in mammalian cells with the exception of lung surfactant. Further, 16:0 composes <5% of cholesteryl esters in typical cells. The authors should be clearer about how this discrepancy between natural sorting of palmitate and the sorting of NBD-16:0 supports this as an accurate model of acyltransferase activity and intracellular transport.

3) The authors state that PA is primarily remodeled in the ER and transported to the mitochondria as a precursor to CLs (lines 108-111). This statement needs a source. In most studies I am aware of, the vast majority of both PA and 16:0 are primarily converted to TGs or PC/PE with only a small fraction going towards the CDP-DAG pathway required for CL biosynthesis. Are C2C12 cells unique in this regard? Does lPA stimulation specificity induce CL production? Does any of the NBD get into the TG or phospholipid fractions?

4) This study would be much stronger if another fluorescently labeled fatty acid was added. A comparison of the sorting of 20:4 and 16:0 would be very informative. This is especially true if the studies were done in the context of a known acyltransferase, for example LPCAT3.

5) This study would also be strengthened by an orthogonal technique showing similar sorting. For example, separation of the organelles and measurement of labeled fatty acids by MS or nano-SIM analysis would greatly strengthen these studies.

6) In figure 1A, the authors draw a schematic with an sn-2 lyso-PL in the figure. Sn-2 lyso-PLs as labile and will acyl migrate to the sn-1 position without careful handling of the PL in a basic solution. The authors make no mention of this type of handling in the method section. This figure should either be corrected or more details of how they handled their lysophospholipids should be provided.

Reviewer #2:

I think this is a superb manuscript - it is written in a clear way, such that the story starts at the historical understanding of lipoprotein trafficking and builds up convincingly using various experimental methods to show that a new class of lipoproteins is trafficked via acylation of glycine, through the Aat secretion system.

It is highly exciting that a protein that does the acylation AND the secretion from the periplasm to the cell surface has been identified! Next step is to get a structure.

The data are convincing and the paper is extremely well-written. My comment is that I am not convinced by the argument that CexE would not be recognised by the lol system, when it is acylated it likely would be as the hydrophobic pocket of LolA and LolB are fairly indiscriminate - see e.g. the binding of small hydrophobic molecules to these proteins. The authors should comment on this aspect.

It is intriguing how glycine in particular is recognised for acylation.

Overall, a great paper - authors should be commended.

Reviewer #2:

The manuscript prepared by Kim and Colleagues provides a solid attempt at understanding the neural correlates associated with self-reassurance and self-criticism in relation to what they term neural pain. While it is well written and there is a clear story presented here, there appears to be insufficient details in the introduction and discussion. The methodology appears sound for the most part, but I have some concerns relating to stimuli and gender effects that I believe would make the findings more compelling if addressed.

Criticisms:

1) The example items of the neutral statements appear to involve an external agent (i.e., a reference to a friend), while the neural pain is purely about the self. Are there also references to other people in the neural pain condition? If not, how have the authors ensured that the neutral condition is actually neutral. It seems likely that the inclusion of an external agent for many of the neutral statements could pose problems with interpretation, especially when talking about self-criticism and self-reassurance. The presence of an external agent in the neutral statements changes the meaning from a purely self-oriented experience to a shared experience.

2) I am curious as to why the inverse contrasts (i.e., reassurance - criticism) were not run? Knowing whether there was a unique network associated with self-reassurance would provide a more comprehensive understanding of the authors' findings.

3) I am wondering why the authors did not accommodate for gender differences in their study? Given recent evidence (See citation) it seems likely that this may play a part in self-compassion. The authors report an almost equal distribution of males and females, so it should be possible. If the authors did explore this and found no difference with gender as a regressor then this should be noted in the manuscript. Mercadillo, R. E., Díaz, J. L., Pasaye, E. H., & Barrios, F. A. (2011). Perception of suffering and compassion experience: brain gender disparities. Brain and cognition, 76(1), 5-14.

4) It seems as though a whole body of literature is being very lightly touched on here but would benefit from inclusion. I think it would be useful to have some information in the introduction regarding moral emotions (i.e., compassion) and the link with empathy and emotion regulation (see work by Jean Decety). This would also be beneficial for the discussion as the authors are in essence describing empathy.

Reviewer #2:

The authors report on a model system to study the infiltration of growing thrombi by leukocytes using fluorescent microscopy. Such a system will facilitate studies on the role of leukocytes in the context of immuno-thrombosis and thrombus growth. I like the proposed model and I'm convinced about the utility of such a system. However, although the model is sound, I do have a couple of major concerns:

1) The authors describe crawling neutrophils; which methodology has been applied to guarantee that the crawling of the neutrophil is a general phenomenon in this system and not a feature of selected neutrophils? Has there been used a method of quantification (e.g. 86% of the neutrophils are crawling)?

2) The authors identify two types of granulocytes (uniform DiOC6-type A vs cluster-like DiOC6-type B granulocytes. Although the pictures provided (fig 2) do represent nice and clear examples of type A vs type B granulocytes, the experiment will reveal for sure staining patterns which have been less clear. What kind of systematic methodology has been applied to delineate type A from Type B neutrophils?

3) Figure 3 and 4 are nice figures showing differences in granulocytes/FOV and velocity- but it is not clear to the reader what percentage of the neutrophils visible in the FOV do move or not. Was there a minimal amount of neutrophils being in motion?

4) The authors want to point out the synergistic effects of neutrophils and platelets in the thrombus growth. To finally make the point they use whole blood of a WAS patient. However, since WAS affects neutrophil motility as well as platelet morphology/number the individual role of platelets and neutrophils in this process remains open. Therefore control experiments targeting either platelets (whole blood of a thrombocytopenic patient and/or platelet depletion) may contribute to identify the role of platelets in the model. On the other hand, inhibition of neutrophil activation/motility may illustrate the individual contribution of neutrophils in this setting.

Reviewer #2:

Summary and comments:

This study presents an analysis of five large datasets of cancer cell viability including both genetic and chemical perturbations and find that RNA-seq expression outperforms DNA-derived features in predicting cell viability response in nearly all cases, and the best results are typically driven by a small number of interpretable expression features. The authors suggest that both existing and new cancer targets are frequently better identified using RNA-seq gene expression than any combination of other cancer cell properties.

Overall, none of the main conclusions in the paper are surprising, and begs the question whether sequencing more cancer exomes is really meaningful? This is a question that deserves serious debate as major resources are being diverted to large-scale exome sequencing projects with low information content returns.

The paper is well written. And at first glance, the results seem to support the provocative title. Improved clarity around what the predictor and response variables are earlier in the paper would improve readability, particularly around what a "genomic" variable is. Most of the helpful details are buried in the methods.

The main benefits of the manuscript: (1) emphases on simplistic (i.e. few features) predictors that are themselves easily interpretable; and (2) the choice of random forest classifiers also makes interpretation of the predictions pretty straightforward. One concern is whether the breadth or depth (i.e. completeness) of the genomic predictor variables somehow unfairly bias the findings against the ability to predict with those variables compared to expression variables, which are quite easy to encode and interpret. This concern is alluded to in the discussion when reviewing the findings of previous, related publications, and could be further explored. For instance, while variations in mutant RAS (H, K or N) or B-RAF were the only dependencies noted to be predicted better by genomics (i.e. mutations), are all driver mutations known and represented in the data? One would expect that amplified EGFR or HER2 would be predicted well from genomics, but these are notably missing, presumably because they do not meet the filtering criteria.

A notable finding was that a single genes' expression data produced notably better results than gene set enrichment scores overall, despite having many more presumably irrelevant features. Predictive models for many vulnerabilities exhibit relationships expected to be specific to a single genes' expression (e.g. los of a paralog's expression predicts dependency on its partner). There is no biological validation for any of the predictions in the manuscript.

Specific comments:

What was the thought process for choosing 100 perturbations in each dataset to label as SSVs? Why not 82, or 105? Was there a systematic analysis done to pick this number (e.g. harmonic mean)?

Did the authors estimate the effect size they are measuring across the 100 selected SSVs? In other words, was there an estimation of fitness effect, single mutant fitness or degree of essentiality for the 100 SSVs and what range of effects are they exploring? One possible way to measure the fitness effect of each of the 100 vulnerabilities is to examine the dropout rate in pooled screens at the guide RNA level, looking for consistency in gRNA behaviour.

Did the authors include essential and non-essential genes as reference points in their analyses? This wasn't clear from the methods.

The authors describe a clear gradation of response to either TP53 or MDM2 knockout according to the magnitude of EDA2R expression observed in multiple datasets (i.e. Achilles, Project Score, RNAi, GDSC17, PRISM). Using EDA2R expression to infer TP53 activity could have clinical benefit and deserves more attention (i.e. validation).

Reviewer #2:

Asprosin, as identified by the authors' group, is reported to stimulate glucose release from the liver and also centrally act as an orexigenic hormone. The present study developed monoclonal antibodies for asprosin and demonstrated that antibody-based asprosin depletion lowered food intake, prevented diet-induced body weight gain, and lowered blood glucose levels in mice. Overall the data are supportive of the conclusion; however, several concerns were identified as follows:

1) One of the central issues is the specificity of the antibody action. The authors should demonstrate if the effect of the asprosin antibodies is blunted in mice that lack either asporosin or its receptor OR4M1.

2) Previous studies from the authors' group show that asprosin acts on hepatocytes and triggers cAMP signaling. The authors should examine if the neutral antibodies blunt the cAMP signaling in DIO mice.

3) Similarly, asprosin was shown to stimulate AgRP+ neurons. The authors need to demonstrate the effect of asprosin antibodies on AgRP+ neuronal activity.

4) A recent paper (von Herrath et al. Cell Metabolism 2019) challenged the author's observation of the metabolic action of asprosin. The authors claim that this is due to "due to use of poor quality recombinant asprosin". However, no scientific evidence was presented. This study needs a more rigorous assessment of data reproducibility.

5) Most of the bodyweight data are presented as "body-weight change". However, the authors should present them as whole-body weight.

6) Some of the data points and stat analyses require further clarification. e.g.) lack of SE in Fig.1c, statistical analysis of Fig.3, Sup Fig.1

Reviewer #2:

The authors investigate the neural correlates of second order conditioning in carefully designed behavioural experiments coupling multivariate fMRI and functional connectivity. They found that the lateral OFC in connection with the amygdala, plays an important role. I think the paper represents a valuable addition to the human cognitive literature, where second order conditioning is surprisingly under-investigated. I have only a few suggestions to make.

I encourage the authors to complement the multivariate analyses with a standard univariate analysis. To be clear, I am not without seeing the added value of the multivariate approach, however, given the extensive literature on the neural bases of conditioning using univariate analyses and the strong prediction about directionally of the effects in the OFC (which should positively encoded expected values and rewards), I think the paper would definitely benefit from including the univariate results for the main contrasts / variables.

I am also curious to see the reaction times in the attentional control task analyzed to check if they were affected by the underlying conditioning procedure. Following the Pavlovian-to-Instrumental transfer theory, we should observe that the reaction times are slower for negative (aversive) stimuli and faster for positive (appetitive) stimuli.

Reviewer #2:

In this work, Sims and colleagues use resting-state functional connectivity and diffusion tractography in human connectome project data to examine the connectivity of the central and peripheral aspects of the primary visual cortex. They find that central V1 connects more strongly to regions of the prefrontal cortex interpreted as the Fronto-parietal network than does peripheral V1.

The idea that central V1 may be directly connected to control-related networks is an interesting one, and has fascinating implications for the study of top-down modulation of visual cortex function. However, I must say I am somewhat skeptical of these findings, for several reasons.

First, I find the a priori anatomical basis for these proposed connections to be dubious. The authors themselves describe how Markov et al. explicitly conducted tract tracing with central V1 and found connections with posterior frontal and parietal cortex, but nothing with areas classically associated with the fronto-parietal cortex. The authors propose that the inferior fronto-occipital fasciculus may connect V1 with lateral prefrontal regions only in humans. However, they provide no evidence for this suggestion. Indeed, my understanding of the iFOF is that it connects to inferior and lateral occipital cortex (see e.g. figures from the Takemura study cited in this work). Can the authors better support the idea that the iFOF might be the route of connection between V1 and frontal cortex?

Second, I am concerned that both 1) the Central V1 ROI employed in this work and 2) the inferior frontal cortex region showing strong FC with that Central V1 ROI overlap very closely with regions where we have seen poor BOLD signal in our own fMRI data (I would like to attach a figure if possible).

We are not confident what the source of the poor signal might be in posterior occipital or inferior frontal cortex; we suspect the presence of large veins (possibly the transverse sinus in V1; see Winawer et al., 2010, Journal of Vision). In any case, the data quality is low enough that we believe our data should not be considered to represent actual neural function in those regions. Can the authors demonstrate convincingly that this is not the case in their HCP data?

Third, I have an issue with the localization of effects in this paper. The paper describes effects in the fronto-parietal network throughout the manuscript, including the title. How surprising, then, that the strongest effects are not in the FP network at all! Figure 4A makes it very clear that the largest effects are in the IFG, which is outside the green outlines describing the extent of the fronto-parietal network, but inside the Default network. Figure 3A also supports this Default-centric localization, with Central V1 effects in posterior lateral parietal, medial parietal, and superior frontal cortex, all outside FP but inside Default. Since the FC effects are not actually primarily in FP, I see no reason why FP should be used as a mask in Figure 5. Indeed, the authors should show the localization of SC effects throughout the cortex, not just in FP. I also see no reason why these V1-Default connections should be characterized in any way as "attention" or "control".

Fourth, I feel that these FC and SC differences are wildly over-interpreted. From the scale, the actual strength of FC and SC between central V1 and lateral parietal cortex is extremely weak (around Z(r) = .1 for FC and p-track = .1 for SC). Under no circumstances would I believe that either of those values represents any sort of real connection. Cortical regions with direct structural connections have much stronger FC values, as do regions that influence each other indirectly via multi-step connections. Further, very large portions of the brain probably have both stronger FC and SC to central V1 than these FP regions (the authors show this for FC but exclude this info for SC). Most glaringly, I certainly don't believe there is a "direct structural connection" as is claimed in the discussion--a claim based, strangely, on the spatial correspondence between the structural and functional maps, which really has nothing to do with any evidence for a direct connection.

Finally, the authors must note that p values may not be used for spatial correlations between brain maps. This is because these maps are always highly autocorrelated, which violates the independence assumption of the correlation procedure.

Reviewer #2:

In the manuscript, "Structural characterization of an RNA bound antiterminator protein reveals a successive binding mode," the authors present the solved crystal structure of Enterococcus faecalis EutV by itself as well as bound to its RNA substrate. In previous work, the RNA substrate was proposed to consist of a dual hairpin and the genetics strongly suggested that both hairpins of this feature were crucial to functional antitermination in vivo. The finding revealed by the crystal structure in this work is that the EutV dimer does not appear to bind both hairpins simultaneously. The structure shows one EutV chain binding a hairpin in one RNA molecule and the second binding a second hairpin in a separate RNA molecule. The orientation of the two ANTAR domains is such that it is not possible to bind one RNA molecule simultaneously. Based on their findings, the authors propose a model of successive antitermination in which EutV binds to the first hairpin as it is generated by RNA polymerase and then this somehow favors binding to the second hairpin overlapping the terminator sequence as soon as it is made to prevent terminator formation. My overall assessment is that this is potentially an important and interesting contribution to the fields of transcription termination/antitermination and RNA/protein structural biology. However, there are concerns with how conclusive the data is, how exactly the model can work, and a lack of experimental evidence for the model.

Major Comments:

1) One major concern about the structure is that it is of non-phosphorylated EutV bound to its RNA substrate. Two-component system regulators almost always undergo conformational changes upon phosphorylation and therefore I think it is still an open question whether the structure truly represents active EutV bound to RNA. Perhaps the ANTAR binding domains of the EutV dimer change orientation upon phosphorylation such that binding to both hairpins can occur.

2) If binding does only occur with one hairpin, then why are two necessary for activation? If it is impossible for one dimer to bind both hairpins simultaneously, how does binding to the first hairpin help binding to the second? This is not clearly explained. Also, no experimental evidence is presented to support the model.

3) Wording of the abstract does not well reflect the final model presented. The abstract makes it sound like the second hairpin is not important, which is not what is shown here or in the previous work. I think the authors should say a bit more about what the actual model is in the abstract to eliminate this misconception.

4) Ramesh et al. (2012) observed that EutV bound the eutP UTR with a higher KD (less efficiently) when just the P1 loop was used in an EMSA assay compared to P1/P2. This study found the same KD, whether P1, P2, or both are used in a SPR assay. Could the difference in these findings be related to the different techniques or the fact that slightly different versions of the EutV protein were used?

Bae et al.(2020) Asymptomatic Transmission of SARS-CoV-2 on Evacuation Flight. Johns Hopkins Bloomberg School of Public Health. Retrieved from: https://ncrc.jhsph.edu/research/asymptomatic-transmission-of-sars-cov-2-on-evacuation-flight/

Reviewer #2:

The findings presented in this manuscript are really exciting. They show that selection is happening at multiple scales - among viruses within a cell - and between their host cells within a population. The conflict between these levels of selection results in evolved populations that are less fit than the ancestors. This result is exciting because it happens repeatedly in independently-evolving populations, showing that it can be a general result. It is also an example of how a non-transitive interaction can evolve de novo, as the authors claim in the manuscript. The experiments seem to rule out most alternative hypotheses. However, the authors could explain their reasoning more clearly in some cases.

1) In particular I found it difficult to understand some of their conclusions on page 9, in the first paragraph around lines 210 - 219, without rereading, rewriting results, and lots of thinking. On lines 211-213, they state that production of active toxin or maintenance of the virus has no detectable fitness cost to the host". There are a lot of comparisons to think through here to get to that conclusion, and I think the average reader needs to be taken through that. Even though I have some experience thinking about costs and how they can be estimated, I still spent quite a lot of time trying to follow the logic from figure A to that statement. In fact, I still do not understand how they are distinguishing between 'production of active toxin' and 'maintenance of the virus'. I also had to spend a lot of time thinking through the results in figure 3 and the conclusion stated on line 217.

2) I think it would be helpful to the reader, and interesting, if there were more of an explanation about WHY K+|+ cells have positive frequency-dependent fitness relative to K-|- cells. Why is the presence of an active virus and immunity more beneficial at higher frequencies?

Reviewer #2:

This is an interesting study that provides convincing evidence that a Draxin mutation underpins forebrain commissure phenotypes in BTBR mice and crosses.

The use of BTBR x C57 N2 crosses where commissure phenotype is correlated with the Draxin mutation (Figure 5) is a nice illustration of unpicking variable penetrance. The phenocopy of the BTBR/c57 phenotype to Draxin mutants is a nice confirmatory experiment.

Further, analysis of midline fusion shows that problems in MZG proliferation and hemisphere fusion are prevalent in BTBR mice supporting the hypothesis that Draxin is needed for midline fusion.

MRI scans of human subjects with a spectrum of CC abnormalities show that commissure abnormalities correlate with midline fusion defects.

Major comments.

1) As a central contention of this study is that variable penetrance of the commissure phenotypes in the BTBR x C57 mice stems from an earlier midline fusion phenotype is would have been useful to see if the (embryonic) midline fusion phenotype also showed the same partial penetrance in BTBR x C57 mice, perhaps also correlated with the WT/MUT Draxin alleles (as in Figure 5). This would be a testable prediction of the hypothesis that midline fusion (and not something else) mediates the Draxin phenotype.

2) I am not sure the human data adds substantially to the paper as it is not related to Draxin mutations. It is already well known that corpus callosum phenotypes are variable in humans (and mice).

Minor comments:

Some of the data are not normally distributed (particularly clear for pink data points in Fig 5a,e,i,m) so it is not appropriate to show standard errors (the SEM bars could simply be removed), a non-parametic Kruskal-Wallis ANOVA has been used which is appropriate.

Reviewer #2:

This paper presents the results of a study of optogenetic visual restoration. ChR2 was targeted either to a subset of ganglion cells (GCs) or to a subset of ganglion cells-not necessarily the same ones-plus starburst amacrine cells (SACs) using an intersectional genetic strategy. Photoreceptors were ablated using MNU in animals expressing ChR2, and then retinal and whole animal responses to visual stimuli were assessed. Interestingly, co-expression of ChR2 in SACs and GCs resulted in different, potentially more "naturalistic" responses than expression in GCs alone. This is an interesting result, but given the number of possible explanations for it, the lack of any rigorous investigation of the underlying mechanism is problematic. Results presented by the authors indicate that ACh release from stimulated SACs acts upon some network(s) containing electrical synapses and presynaptic to the GCs to alter GC responses, but the identities of these network(s) remain unknown. Given that ACh is considered to act in a paracrine manner within the retina, the affected cells could be any number of amacrine or bipolar cells.

There are a number of lines of investigation that the authors could pursue to identify-or at least, rule out-specific presynaptic networks. While too numerous to discuss individually, potential lines of investigation could differentiate nicotinic from muscarinic effects and effects on inhibitory and excitatory inputs to ganglion cells. As well, it would be important to express ChR2 in SACs alone to see if this drives changes in GC spiking.

In all, the authors here have the opportunity to examine the effects of paracrine signaling by SACs on inner retinal network excitability and function using a nice model system, and they should take advantage of it.

Reviewer #2:

This is an important piece of work addressing in-vivo measurements where two coupled components are to be measured ideally in the same time and space components. Unfortunately, the impact of this work is likely to be minimized due to its poor organization and the attempt to deal with a number of separate but related issues in the same manuscript. Accordingly, it is suggested that this work be divided into two manuscripts to be published together. The focus of the two might be:

A) A Tetrode-Based Microsensor (TACO) - This work would focus on the criteria for performance that would be expected for a new sensor, presumably with new and unique properties. This work would include differential plating of electrodes (It is unclear whether some or all of this work has been previously reported), dimension considerations, and the simulation of sensor response. (An important consideration but frequently overlooked is that a sensing element with a 17um diameter will exhibit hemispherical diffusion (Eq. 4)). Other issues such as interferences, stability, sensor response time and linearity need to be more fully explained. Presumably such a sensor configuration would be useful in other applications involving oxidase-based sensors.

B) Effects of Local Field Potential and Oxygen-evoked ChOx transients in the In-Vivo Measurement of Acetylcholine in Freely Moving Rodents (A better title can surely be presented!) - Here the focus should be on the in-vivo measurements including a qualitative explanation of the LFP and O2 response and how the TACO sensor corrects for this. Presumably the detection of REM and NREM sleep will be detected by EEG. This is not well explained. Also unclear is how the improved performance of the sensor affects the conclusions of the in-vivo studies.

Reviewer #2:

The manuscript represents a lot of hard work on an interesting topic. Understanding how threatened populations are impacted by human-derived processes is critical, and requires more study. However, as it stands, the study suffers from some logical flaws that detract from the scientific insights that can be gained from this study. These are:

1) The authors argue that older individuals are important repositories of ecological knowledge, which is now well-established knowledge. However, the authors then build their study around the consequences of poaching in terms of the effects on network metrics that are assumed to correspond to transmission properties. The logical problem here is that removing ecological knowledge from a network leaves nothing to transmit-hence the transmission properties of the network are inconsequential.

2) Linked to this point is the issue that the results and discussion focus a lot on the concept of network transmission, but the study uses network metrics (e.g. diameter) as proxies of transmission properties. It is pretty well known that there are many factors (e.g. clustering coefficient) that contribute to transmission dynamics, and it is unlikely that any one network metric alone can capture the ability for a network to transmit information.

3) The authors note that continuous data on the reorganization of the network after poaching are not existent, and that they justify using a static approach (i.e. the network does not change after a removal/simulated poaching event) by focusing on the consequences immediately after deletion. However, the simulations involve removing up to 20% of the individuals in the population, meaning that their model assumes that poaching events are occurring substantially faster than the network is reorganizing itself. This seems too unrealistic an assumption.

4) A further issue with using a static approach is that the networks captured in the study may not represent the network structure that is in place when an event takes place in which ecological knowledge is important. For example, studies from other multilevel societies, e.g. hamadryas baboons (from Kummer's work), suggest that units come together when conditions necessitate forming larger groups. So, the network measured in the empirical data may not be the network through which ecological knowledge is transferred when an event necessitates it.

5) Finally, the results and the conclusions drawn from the study seem in conflict. On the one hand, the main summary of the results are that removing older individuals has little, if any, impact on the network's capacity to transmit information. On the other, the conclusions seem to be slanted towards removal of older individuals as a conservation issue (e.g. L662). Thus, there is tension in the manuscript that, unfortunately, reduces both the clarity of the findings and the clarity of the take-home messages.

Overall, the study was enjoyable to read, with lots of biology, which is a strength for a modelling study. However, some of its construction, and the reliance on simple node deletions, really limits the capacity to gain substantial new insights from this study.

Reviewer #2:

In this study, Ortuste Quiroga et al. showed that the mechanosensitive ion channel Piezo1 promotes myoblast fusion during the formation of multinucleated, mature myotubes. The authors show that Piezo1 knockdown suppressed myoblast fusion during myotube formation and maturation. This was accompanied by a decrease in Myomaker expression. In addition, Piezo1 knockdown lowered Ca2+ influx in response to stretch. In contrast, the agonist (Yoda1)-mediated activation of Piezo1 increased Ca2+ influx and enhanced myoblast fusion, but only under certain conditions. Over-activation of Piezo1 resulted in the loss of myotube integrity. Surprisingly, the myotubes were thinner in Yoda1-treated cells compared to the control. Furthermore, the authors showed that Piezo1 activation enhanced Ca2+ influx in cultured myotubes and the influx of Ca2+ increased in response to stretch. However, it is unclear how this is related to myoblast fusion.

Overall, the authors made several interesting observations in this study, such as Piezo1's role in myoblast fusion and Piezo1-mediated Ca2+ influx, etc. However, how these phenomena are linked and what is causal remain largely unclear. Another issue is the discrepancy between this study and Tsuchiya et al. Nature Communication (2018) on the function of Piezo in myoblast fusion.

Major comments:

1) In this study, the authors uncovered a positive role for Piezo1 in myoblast fusion. This is in contrast to Tsuchiya et al., which demonstrated an inhibitory role of Piezo1 in this process. While this study used an RNAi approach to knock down Piezo1 and found a decrease in myoblast fusion, Tsuchiya et al. used CRISPR/Cas9 to knock out Piezo1 in muscle cells and observed a significant increase in myoblast fusion. These two opposite results are difficult to interpret and made the role of Piezo1 in myoblast fusion confusing. It is necessary that the authors make some effort to bring clarity to this issue. First, the authors need to perform rescue experiments in their RNAi cells to make sure that the fusion defect is not due to off-target effects caused by the siRNAs. Second, the authors should design an siRNA that causes a more significant knockdown of Piezo1 than the current siRNAs and test if myoblast fusion is enhanced as in the knockout cells (Tsuchiya et al.). Third, the authors could make their own CRISPR/Cas9 knockout cells and examine the resulting fusion index.

2) How does Ca2+ influx regulate fusion? Tsuchiya et al. provided evidence that Piezo1-mediated Ca2+ influx activates actomyosin activity and inhibits myoblast fusion. This current study suggests that Ca2+ influx increases fusion, but without providing mechanistic explanations. What are the effects of Ca2+ influx that lead to an increase in myoblast fusion? Does it cause more IL4 secretion? Or transcription upregulation of Myomaker? How? Does the Ca2+ influx level correlate with Myomaker expression level? If Ca2+ influx indeed leads to upregulation of Myomaker, why would Piezo1 knockout cells (low Ca2+ influx) show increased levels of fusion (Tsuchiya et al.)?

3) Is Piezo1 required in myoblasts or myotubes or both cell types for fusion? Is it localized to the fusion sites?

Reviewer #2:

Naetal et al. studied the effect of Lap2a on lamin A/C dynamics-of-assembly and mobility as well as telomere movements. This study indicated that lamin A/C are first assembled into the lamina, before some of the lamin A/C is re-localized to the nucleoplasm. Interestingly, the amount of nucleoplasmic lamins is independent of Lap2a although its physical properties are different. The results indicated that Lap2a contributes to the dynamics of lamin A/C in the nucleoplasm while its absence reduces nucleoplasmic lamin and telomere dynamics. These results reveal the function of Lap2a as regulator of lamin anchorage in the nucleoplasm but it has no major role in recruiting lamins into the nucleoplasm. Since the impact of lamins on the nuclear organization is critical for nuclear functions and important for nuclear integrity, these results are fundamental for the understanding of both lamin A/C and Lap2a.

The authors also identified two pathways in which nucleoplasmic lamin emerged. First, lamin can be localized to the lamina and then relocated to the nucleoplasm, and second, from the pool of mitotic lamins which are not associated with the lamina.

The authors may consider some textual changes, in particular regarding the state of nucleoplasmic lamin polymerization:

1) The nuclear lamina filaments are typically 200-400 nm in length, but they are very flexible. A 200 nm filament would have a molecular weight of <1.4MDa ( ~50% of a ribosome) and can be bent and curved. That would mean that a single filament has a reasonably high diffusion coefficient. At the lamina, lamins are less mobile, however, it is likely to be due to binding partners that anchor lamins to the INM and chromatin (e.g. emerin is a membrane protein that binds lamin A) - the diffusion of 1.4 MDa protein complexes is quite fast. The above is mentioned because nucleoplasmic lamins may be polymerized but more mobile (less anchored) than their lamina-hosted lamins population.

2) The authors show that nucleoplasmic lamins are first localized to the lamina, where they can polymerize. Isn't it possible that filaments can be released into the nucleoplasm?

3) In vitro assembly assays of lamin A in the presence of Lap2a indicated that lamin A assembly is inhibited by Lap2a. Based on these results the authors suggest that Lap2a keeps lamin in a less polymerized state. Previous work by Zwerger et al. 2015, showed that inhibitors of in vitro lamin A assembly, have no impact on incorporation and localization of lamin A into the lamina, while incorporation of lamin A into the nuclear lamina was abolished when other lamin binders that have no effect on lamin assembly in vitro were used. That would suggest that either in vitro assembly is not representing the cellular lamin assembly or assembly of lamin into the lamina is independent of polymerization states of lamins. The authors may want to discuss these views.

Reviewer #2:

This manuscript asks how learners solve the problem of continuous motor control. The authors find qualitatively distinct components of learning under continuous tracking conditions: the adaptation of a baseline controller and the formation of a new task-specific continuous controller. These learning components were differentially engaged for rotation-learning and mirror-reversal. Further, the authors present a methodological advance in motor control and learning analysis that relies on frequency-based system identification techniques.

Overall, this paper presented a valuable third perspective on the learning processes that underlie motor performance and provided an impressive analysis of continuous control data. Furthermore, the system identification technique that they developed will likely be of great value to the study of motor learning. However, I believe that there are some issues with the framing of the de novo learning mechanism and in their interpretation of the results.

1) Positing a de novo learning mechanism as the absence of established learning process signatures.

The authors introduce the concept of de novo learning in contrast to both error-driven adaptation and re-aiming: 'a motor task could be learned by forming a de novo controller, rather than through adaptation or re-aiming.' However, the discussion reframes de novo learning as purely in contrast with implicit adaptation: '[...] de novo learning refers to any mechanism, aside from implicit adaptation, that leads to the creation of a new controller'. While this apparent shift in perspective is likely due to their results and realistically represents the scientific process, this shift should be more explicitly communicated.

As explicitly raised in the discussion and suggested in the introduction, the authors have categorized any learning process that is not implicit adaptation as a de novo learning process. To substantiate this conceptual decision, the authors should further explain why motor learning unaccounted for by established learning processes should be accounted for by a de novo learning process.

2) The distinction between de novo learning and re-aiming is unclear.

Participants could not learn mirror-reversal under continuous tracking without the point-to-point task, which the authors interpret to mean that re-aiming is important for the acquisition of a de novo controller. This suggests that re-aiming may not be important for the execution of a de novo controller.

However, the frequency-based performance analysis presented in the main experiment would seem to suggest otherwise. As mentioned in the introduction, low stimulus frequencies allow a catch-up strategy. Both rotation and mirror groups were successful at compensating at low frequencies but the mirror-reversal group was largely unsuccessful at high frequencies. Assuming that higher frequencies inhibit cognitive strategy, this suggests to me that catch-up strategies might be essential to mirror-reversal, possibly not only during learning but also during execution.

Further, the authors note that, in the rotation group, aftereffects only accounted for a fraction of total compensation, then suggest that residual learning not accounted for by adaptation was attributable to the same de novo learning process driving mirror reversal. This framing makes it unclear to me how the authors think re-aiming fits into the concept of a de novo learning process (e.g. Is all learning not driven by implicit adaptation de novo learning? What about the role of re-aiming?)

3) Interpretation of spectral linearity as support for the absence of a catch-up strategy.

Using linearity as a metric for mechanistic inference has limitations.

• The absence of learning (errors) would present as nonlinearity.
• The use of cognitive strategy could present as nonlinearity.
• It doesn't seem possible to parse the two mechanisms, especially as you might expect both an increase in error at the beginning of learning and possibly an intervening cognitive strategy at the beginning of learning.

Given these issues, a more grounded interpretation is that linearity simply represents real-time updating. If the relationship between the cursor and the hand is nonlinear, then updating is not in real time.

The data shown in Fig 4B do not appear to provide clear evidence that the relationship between the cursor and the hand was approximately linear. Currently, it seems equally plausible to say that the data are approximately non-linear. Establishing a criterion for nonlinearity would be useful (e.g. shuffling a linear response for comparison).

4) The presentation of mean-squared error in Figure 2 seems to have limited utility. As the authors mention, it does not arbitrate between mechanisms or represent the aftereffects observed in rotation learning. I suggest removing panel 2C altogether and magnifying panel 2B so that the reader can better appreciate the raw data.

Reviewer #2:

While much independent progress has been made in the development of RL models for learning and DDM-like models for decision-making, only recently have people begun to combine the two (e.g. Pedersen et al., 2017). In this paper, Miletić et al. develop a new set of combined reinforcement learning (RL) and evidence-accumulation models (EAM) in an attempt to account for learning/choice data and reaction time data in a series of probabilistic selection tasks (Frank et al., 2004). While previous developments have provided proof-of-concept that these models can be joined, here the authors present a new model, Advantage Racing Diffusion, which additionally captures stimulus difficulty, speed-accuracy trade-offs, and reversal learning effects. Using behavioral experiments and Bayesian model selection techniques, the authors demonstrate a superior fit to choice/RT data with their model relative to similar alternatives. These results suggest that the Advantage framework may be a key element in capturing choice/RT behavior during instrumental learning tasks.


I think this paper asks some really interesting questions, the methods are quite sound, and it is written nicely. I do think that the central focus of the Advantage learning element is key to the study's novelty. However, I feel that the framing of the paper and the implementation are somewhat at odds, and thus additional experiments (or re-analyses of extant data sets) may be needed to transform the paper from a welcome, modest incremental improvement to a qualitative theoretical advance. I outline my major concerns/suggestions below:

Major Points:

In the abstract, the authors allude to both learning tasks with >2 options and to the role of absolute values of choices in characterizing the limitations of the typical DDM. However, in the manuscript the former is not addressed (and actually does not appear to be amenable to the current model implementation; see below), and the latter is addressed via modest improvements to model fits rather than true qualitative divergence between their model and other models' ability to capture specific behavior effects. Thus, I think the authors' could greatly strengthen their conclusions if they extend their model to RL data sets with a) >2 options, and b) variations in the absolute mean reward across blocks of learning trials. For instance, does their model predict set size effects during instrumental learning? Does their model predict qualitative shifts in choice and RT when different task blocks have different µ rewards? At the moment the primary results are improved fits, but I think it would be important to show their model's unique ability to capture more salient qualitative behavior effects.

Moreover, I'm not sure I understand how the winning model would easily transfer to >2 options. As depicted in Equation 1, the model depends on the difference between two unique Q-values (weighted by w-d). How would this be implemented with >2 options? I see some paths forward on this (e.g., the current Q relative to the top Q-value, the current Q minus the average, etc.) but they seem to require somewhat arbitrary heuristics? Perhaps the authors could incorporate modulation of drift rates by policies? Or use an actor-critic approach? I may be missing something, but I think if the model in its current form doesn't accurately transfer to >2 options, the primary contribution is the utility of urgency, which has been presented in earlier studies.

I appreciate the rigorous parameter recovery experiments in the supplement, but I think the authors could also perform a model separability analysis (e.g., plot a confusion matrix) - it seems several of the models are relatively similar and it could be useful to see if they're confusable (though I imagine they're mostly separable).

I may be missing something, but I do not think the authors are implementing SARSA. SARSA is: Q(s,a)[t+1] = Q(s,a)[t] + lr(r[t+1] + discount(Q(s,a)[t+1]) - Q(s,a)[t]. However, this is a single-step task...isn't it just 'SAR' (aka, the standard Rescorla-Wagner delta rule)?

Reviewer #2:

In this manuscript, Lee and Usher study choices between two options, and model how such choices are affected by the certainty with which the decision-maker evaluates the two options. They insist that this value certainty should be incorporated in current models, and compare ways to do so within the framework of the drift-diffusion model (DDM).

My main concern is that I find the main contribution a bit light. Mathematically, we know that in a DDM higher noise leads to shorter RTs. Empirically, we already know that options rated with low certainty lead to longer RTs (e.g. as demonstrated by the first author in Lee & Coricelli, 2020). So it is not surprising that low certainty cannot correspond to higher noise in a DDM, and might be captured by a lower drift instead. Then, the specific way it can be done deserves to be investigated, but the authors should explore in more details the different classes of models, and the ways in which value certainty could affect other parameters of the model as well.

Suggestions:

I would suggest presenting in the introduction more details about how DDM is currently used in studies of value based decisions, to better explain the context of the present work and highlight the specific contribution of the study.

The authors consider a number of models in the discussion (effects of uncertainty on the bounds, balance of evidence, collapsing bounds, etc.) but do not give the full details of these models. I would suggest including these models in the analyses presented in the result section. Maybe the authors could capitalize on the amount of data they have to do some model fitting, to estimate how the parameters of the DDM would change with value certainty. Parameters of interest are the drift and the drift variability (in the extended version of the DDM) but the authors could also explore the bounds and the variability in the starting point. A basic approach would be to split the data based on value certainty: using a median-split for both options, they could fit separately the choices between 2 options rated with high certainty, and the choices between 2 options rated with low certainty, etc. A more involved approach would be to estimate the effect of value certainty on the parameters in a single analysis across all the data (e.g. using a hierarchical ddm).

Minor points:

The motivation for model 5, which includes an additional component for accumulating certainty, should be more detailed. This approach is not standard, and would deserve more details and some references to prior work offering the same approach, if it exists.

A figure would be helpful to present the typical experimental paradigm, and including the notations of the variables.

In Figure 2, the variable C1 and C2 are not properly defined.

Reviewer #2:

Chromatin remodelers use the energy derived from ATP hydrolysis to reposition or evict nucleosomes, thus shaping the chromatin landscape of the cell. In this study, the McKnight lab use creative genetic and genomic approaches to understand how the apparently nonspecific biochemical activity of one such chromatin remodeler, Isw2, is targeted to specific nucleosomes in the budding yeast genome. The use of an isw1/chd1 mutant is a nice approach to remove the effects of spacing factors, and the SpyTag/SpyCatcher approach is a novel idea for artificial recruitment of factors. The bottom line of the study is that small, conserved epitopes in transcription factors act as recruiting elements for Isw2, allowing precise targeting of a nonspecific biochemical activity to specific genomic loci. From a larger perspective, the results lend support to an interacting barrier model of nucleosome positioning, wherein positioning of specific nucleosomes defines the borders of nucleosomal arrays. The data appear to be of high quality and soundly interpreted, and I believe that the results will be of great interest to those interested in chromatin and transcription. There are many questions raised by the results that I believe will drive further investigation into specificity in chromatin remodeling. My one major criticism (not that major in the scheme of things) is that the authors analyze the interesting subsets of their sites, as detailed below. One example is the analysis of the Isw2/Itc2 co-bound sites to the exclusion of the Isw2-alone sites. I think some exploration of these sites would be warranted, as discussed below.

1) In Fig. S1C, there is nice correspondence between strong Isw2 K215R binding and Isw2-dependent nucleosome remodeling. However, at PICs where there is no apparent Isw2 remodeling, there does seem to be some Isw2 K215R ChIP-seq signal, albeit at a lower level. Does this potentially represent capture of transient sampling-type interactions, or something else?

2) In Fig. S1D, Ume6 ChIP (WT and DBD alone) is shown at 202 intergenic Ume6 motifs. It is stated that the rows are linked with Fig. 1B - it would be nice to see the nucleosome data next to the ChIP data in this panel, as it appears that Ume6 is bound to at some level to the majority of these 202 sites, while Isw2 seems only to be active at the 58 sites of cluster 1. Germane to this point, I of course understand why the authors focused on the cluster 1 sites, but it would be nice to have some speculation on why Isw2 only seems to function at a fraction of Ume6-bound loci. Also, the lengths of the cluster-denoting bars appear to be off here relative to Fig. 1B.

3) In Fig. 5C, it appears that only a subset of Isw2 sites are bound by Itc1 as well. Again, as with the selection of the 58 Ume6 sites, I understand why the Isw2/Itc1 co-bound sites are selected for further analysis, but the Isw2 sites without Itc1 could be discussed as well. Are these sites non-functional? How does Itc1 ChIP-seq data compare to the Isw2 remodeling activity shown in Fig. 1A? How does it compare to Ume6 binding? Does it specify the Isw2-remodeled nucleosomes?

4) Did the authors perform western blots to ensure that their various truncation constructs were stable? This is important for interpretation of the results vs deletions.

5) To summarize the above points, a major thing missing from the discussion is why only subsets of TF binding sites recruit Isw2. For instance, as mentioned above, 58 Ume6 sites seem to specific Isw2 remodeling - what is special about those sites versus the other ~150 sites that appear to be bound by Ume6? It's mentioned briefly in the discussion that only three Swi6 sites were identified as Isw2-recruiting and that this may be tuned by cellular context, but this is quite vague and superficial. More speculation on what differentiates these sites from the TF-bound but non-Isw2 recruiting sites could be included.

Reviewer #2:

In this manuscript, the authors examine the neural correlates of perception and memory in the human brain. One issue that has plagued the field of memory is whether the neural processes that underlie perception can be dissociated from those that underlie memory formation. Here the authors directly test this question by introducing a behavioral paradigm designed to dissociate perception from mnemonic binding. In brief, while recording MEG data, they present subjects with a sequence of visual stimuli. Following the sequence, the subjects are instructed to bind the three stimuli together into a cohesive memory, and then are tested on their memory for which pattern was associated with an object, and which scene. The authors investigate changes in alpha/beta power and theta/gamma phase amplitude coupling during two separate epochs - perceptual processing and mnemonic binding. Overall, this is a well written and clear manuscript, with a clear hypothesis to be tested. Using MEG data enables the authors to draw conclusions about the neurophysiological changes underlying both perception and memory, and establishing this dissociation would be an important contribution to the field. I think the conclusions are justified, but there are several issues that should be addressed to improve the strength and clarity of the work.

The fundamental premise of the task design is that subjects view a sequence of stimuli, and then separately at a later time actively try to bind those visual stimuli together as a memory. However, it is entirely possible, and even likely, that memories are being formed and even bound together as the subjects are still viewing the sequences of objects. How would the authors account for this possibility? One possible way would be if there were a control task where subjects were just asked to view items and not remember them.

Another possibility would be to examine the trials that the participants failed to remember correctly. Presumably, one would still see the same decreases in alpha power. Yet it seems from the data, and the correlations, that during those trials that were not remembered properly, alpha power changed very little. Of course, it is unclear in these trials if failed memory is due to failed perception, but one concern would be that this would imply that decreases in alpha power are relevant for memory too. It would be helpful to see how changes in alpha power break down as a function of the number of actual items remembered. It would also be helpful to know how strong these correlations actually are.

A related issue is with respect to hippocampal PAC. The authors investigate this during the mnemonic binding period. Yet they also raise the possibility in discussion that this could also be happening during perception, which goes back to the point above. Did they analyze these data during perception, and are there changes with perception that correlate with memory? This would suggest that binding is actually occurring during this sequence of visual stimuli.

The authors perform a whole brain analysis examining the correlation between alpha power and memory to identify cluster corrected regions of significant. However, the PAC analysis focuses only on the hippocampus, raising the question of whether these results can account for the possible comparisons one could make in the whole brain. They do look at four other brain regions for PAC, which it would be helpful to account for. In addition, are there other measures of mnemonic binding that are significant? For example, theta power, or even gamma power?

The authors note in the discussion that the magnitude of hippocampal gamma synchrony has been shown to be related to the decreases in alpha power. Is this also true in their data?

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Reviewer #2:

This paper is the second in a series of landmark studies from the Richards lab that re-assess the molecular and cellular mechanisms that permit the corpus callosum (CC) to cross the interhemispheric midline in the telencephalon. The Richards lab previously showed key role for a specialized population of fetal astrocytes, the midline zipper glia (MZG), establishing this substrate when the MZG migrate into the interhemispheric fissure (IHF), intercalate with one another and degrade the intervening leptomeninges. In this manuscript, the authors now assess the requirement for the Ntn1/Dcc pathway in remodeling the IHF. In an elegant series of experiments, they show that Ntn1/Dcc regulate the migration pathway of the MZG, potentially by directly controlling cytoskeletal dynamics. This mechanism is conserved between humans and rodents; the authors show that Dcc mutations that cause CC dysgenesis in humans, cause striking changes in the morphology of astroglial-like cells, consistent with the regulation of MZG migration. Thus, Dcc appears to have two roles first, remodeling the MGZ and then guiding CC axons towards the telencephalic midline. Together, these studies continue the overgoing re-evaluation of the role of netrin1/Dcc in establishing neural circuitry, and shed further understanding on a fascinating and beautiful piece of biology.

This is a very beautiful manuscript, the authors are to be congratulated for the very high quality of their images, and detailed quantifications. Would that all studies were so thorough! These studies will be of great interest to the developmental neuroscience research and clinical communities.

Major comments

The authors should be congratulated by including what was clearly a difficult conditional analysis to assess whether Dcc is required in the callosal axons, or in the MZG radial fibers. This analysis was confounded a) by the low efficiency of the shRNA to knock down Dcc and b) the mosaic nature of Emx::cre line, which appears to be variably expressing cre in both callosal neurons and MZG, given that TDT/Dcc are present in both axons (Fig 5B), and the MZG (Fig 5O) in the less severely affected animals.

As currently presented, however, the analysis (sadly) does not greatly add to the paper, since technical issues beyond the authors' control, have made it difficult to assess specifically where Dcc is required with much confidence. Would the authors could consider removing the shRNA approach from the manuscript, and re-focusing the cKO data on a description of a Dcc phenotypic series? This analysis might fit better with the initial description of lack of interhemispheric remodeling observed in Dcc/Ntn mutant mice, and how they relate to (variable?) phenotypes observed in patients.

Minor Points:

1) Fig 3C, D. The failure of the MZG radial fibers to extend along the IHF in Dcc mutant at E15 is very striking, and well described in the text. However, there appears to be an additional more punctate Glast/Nestin signal immediately above the radial fibers in IHF in the E15 mutants, what is that?

2) Fig 4E. Could the increased numbers of migrating MGZ cells seen on the surface of the IHF in E16 Dcc mutants be because there is no "stop" signal created when the IHF is remodeled?

3) Fig 5B. The failure of the GFAP cells to move away from the third ventricle in Dcc mutants seems profound in both the figures and the quantification. Can the authors elaborate more on why the 0-400 um measurement doesn't rise to being significant in the Dcckanga mutants? Perhaps spell out (p=0.0?) where the trend lies on Fig 5B. ?

Reviewer #2:

This manuscript represents a very considerable amount of work, both wet lab and analytic, constituting excellent science. This may be the best paper yet produced on Bdelloids. Despite this glowing recommendation I have some very significant concerns about certain parts, their conclusions section, and the evidence for "enhanced cellular defence mechanisms" in the abstract. Some parts are very rigorous, but others give in to excess speculation. This paper does not really need additional work, it needs some re-writing. Afterwards this important manuscript would be a welcome addition to the field, even without the supposedly unique defence mechanisms.

Substantive concerns:

1) Line 273 onwards: There is a comparison in the manuscript between Bdelloids and Monogonants. It wasn't clear to me however that these groups had been sampled sufficiently. The Monogonants are represented by 5 species (8 genomes) within a single genus in no way representing the diversity of Monogonants and the sampling of Bdelloids is also small. The authors should take a more cautious tone to any conclusions.

2) Line 276-278: The rationale for focussing on this specific group of TEs did not appear robust. The authors say "this class of TEs is thought to be least likely to undergo horizontal transfer and thus the most dependent on sex for transmission". But other groups are not evolving predominantly by horizontal transfer, transposons can change without meiotic sex and this section needs writing a little more clearly. The following lines make a case that some transposon groups increase, and some decrease in frequency. The obvious hypothesis is drift, but the writing was unclear, I always felt that some other mechanism was being proposed but never really stated clearly.

3) Lines 288-300, comparison of TE abundances across animals; this section was very poorly done. I thought the authors could delete this comparison and have a better manuscript. How were these other species chosen? Is C. elegans a good representative of the entire phylum Nematoda? Are the tardigrades representatives of their phylum? Assembly and annotation methods vary enormously across datasets so what can the authors conclude without standardising assembly and annotation for these other animal groups? The authors say "as expected, both the abundance and diversity of TEs varied widely across taxa" This was indeed expected, Figure 2b seems to show noise, and suggests to me that the inclusion of this data was not a good idea. I suggest it is removed, or a very substantive analysis and discussion of the way in which it is an accurate and representative sample of animal transposon loads is written.

4) Line 350-353: This section is weak and needs to be improved. The authors need to make it very clear that this is not a test, it is a single observation. The phrase "as predicted by theory for elements dependent on vertical transmission" seems rather unsupported. Does this relate to the argument put forward in lines 276-278? It was unconvincing at this point also. The current description that some families increase and some decrease is couched in what sounds like too meaningful sounding language, which could be improved to be more consistent with the results. Lines 353-355 here seem to make an argument that the variation of TEs in bdelloids is purely a phylogenetic effect variably present in some bdelloid lineages and related groups. If this is their view (and it seems very reasonable indeed) then the manuscript would be improved considerably if they stated it more clearly.

5) Lines 533-535 "consistent with a high fit of the data to the phylogeny under a Brownian motion model as would be expected if TE load evolves neutrally along branches of the phylogeny." I felt that this was a truly excellent result that needed to be put forward more strongly in other areas of the manuscript. In this area, and some others in this manuscript the authors have truly unique data dramatically improving our understanding of bdelloids. The manuscript would be improved if authors concentrated much less throughout on ideas this data is exceptional and different from other animals, and instead followed their own analysis that this fits with current biological thought.

6) Lines 621-632: "no significant difference between monogononts and bdelloids, or between desiccating and non-desiccating bdelloids" It is not clear to me here what statistical test is being carried out. All tests require phylogenetic control of course. I do agree that they are quite similar, perhaps this should be rewritten to reflect only that?

7) 705-706 The authors look at 3 gene families concerned with transposon control to examine copy number. In one of them they say "the RdRP domain in particular is significantly expanded". I am unclear of what test of significance was carried out and where to find this analysis. Unlike the query concerning desiccating and non-desiccating above I think this analysis is essential. The authors make a really big thing about the expansion of this gene family, including it in the abstract. If they wish to keep its prominence then they need to clearly show whether there is evidence that the size of this domain family is significantly expanded along the branch leading to bdelloids. I understand that this is illustrated in Figure 7 but this is not a test. This needs to be made much clearer in a quantitative rather than descriptive way. There is a need for broad taxonomic sampling, standardisation of assembly and annotation, and a phylogenetic design for this analysis. Else it should be removed or at the least described more conservatively.

8) Line 725: "Why do bdelloids possess such a marked expansion of gene silencing machinery?" There is no evidence presented that they do. There may be a hypothesis that they do it differently, rather than more, but that also needs testing. There is a lot of speculation in this paragraph, and I think removing this whole paragraph would improve the manuscript.

9) If there is an expansion of this family what can we then conclude? The authors say in the abstract "bdelloids share a large and unusual expansion of genes involved in RNAi-mediated TE suppression. This suggests that enhanced cellular defence mechanisms might mitigate the deleterious effects of active TEs and compensate for the consequences of long-term asexuality" yet they also review that animal groups can utilize different gene families for transposon control. Is there evidence that clade 5 nematodes with PIWI have a quantitatively different transposon defence mechanism? No, they just use a different pathway to some other groups, and the default position surely has to be the same for bdelloids, there is no evidence presented that their defence is enhanced. I would strongly recommend that the authors reduce the strength of their claims about the significance of bdelloid transposon control gene families in this manuscript.

10) I felt that the Conclusions (and Abstract) were too speculative and not fully supported by the existing data, though this can easily be addressed by a substantial re-write.

Reviewer #2:

This is a beautiful and clever paper, expanding the authors' tracking method for fast psychophysics to the domain of interocular delay. They find that it is possible to measure interocular delay quite accurately by comparing 1D tracking (in x) in each eye. The tracking technique is exciting because it potentially makes psychophysics much more accessible, and this paper demonstrates that it can be used to measure interocular timing differences.

The authors also examine whether it's possible to estimate interocular delay in a single binocular experiment where people track in depth (x and z). The answer at this point is no - while some aspects of the depth tracking are beautifully accounted for in this way, other factors clearly contribute.

I don't have any substantive concerns at all but I would be interested to see some quantification of the advantage of tracking over button-press psychophysics. It's clear from the error bars in Fig 6B that button-press results are considerably more precise, but presumably they take a lot longer. Could the authors quantify this for us? E.g. button-press psychophysics: 95% confidence interval is 1ms after 100 minutes of experimentation; tracking : 95% CI is 5ms after 10 minutes, or similar.

Could you select a subset of the button-press psychophysics (fewer trials per data point) in order to say what precision could be achieved after the same time as the tracking? This would really help readers assess the costs & benefits of the two approaches.

Reviewer #2:

Generally, this paper is excellent. It explores many characteristics of Brachypodium distachyon population genetics and demography, many of which have been assumed or hypothesised by less data-rich papers over the last two decades. The authors do so with whole-genome sequencing of both a pre-existing global collection and some novel "gap-filling" sampling. The authors appear to have conducted all analyses using best practices, and the conclusions are largely not over-interpreted. I have only a few minor comments.

L68: Ideally a more detailed summary of the work summarised in Supp File 1 would be brought into the main manuscript. The introduction in and of itself largely skims over the quite large amount that is already known or assumed about the population genomics and dynamics of B. distachyon, especially the ~4 other recent WGS popgen papers which cover adjacent/overlapping collections and topics to this manuscript.

L165: with regards random sequence subsets for BPP: does this include sequence only from genes, or from intergenic space? what about TE or other repeat loci? How do you ensure subset regions are single-copy orthologs in all accessions? I'm no expert on BPP, but I'm largely aware of BPP being used on exon capture data (i.e. genic sequence and flanking introns), admitted at different evolutionary scales with a greater expectation that assumptions of orthology are not met.

L338: the speculation about heterozygosity being induced "in the lab" is very interesting. If you have the data which allows investigating this, could you test if the maternal/paternal haplotypes in heterozygous regions match implausibly distant accessions, suggesting in-lab outcrossing?

L364-365: wouldn't a decrease in diversity as one moves east imply an eastwards migration? I'm not sure if I'm misreading this sentence or there is a typo which switches the direction of the decrease. In any case perhaps reword this sentence for clarity.

L403: typo: distance is week -> distance is weak

L405: typo: descent -> descend. Also, a suggestion: did not descend from a single recent colonization (add "single")

L410: Seed dispersal then ensures OR "would then ensure" (delete would, or ensures -> ensure).

L421: While human-commensal seed dispersal likely explains most recent migration, surely the estimated branch times (fig 5) predate significant human movement? Or, phrased alternatively, were there other/additional historical agents of migration?

L433: are pathogens not a potentially strong selective pressure on (nearly) all plants? How then do pathogens relate uniquely to the reproductive strategy/population structure and dynamics of B. distachyon?

L435: Is a concluding paragraph required? I feel the discussion ends somewhat abruptly.

L539: (optional suggestion): given the non-linearity in the IBD plots you present, it would be interesting to apply Generalised Dissimilarity Modelling to test for/examine IBD.

L567: Please give light measurements in uE PAR (umol photos /m2/sec; 400-700nm) in addition to/instead of klux.

Reviewer #2:

This is a fascinating study demonstrating the role of KIF21B in control of T cell microtubule network required for T cell polarization during immunological synapse formation. The authors show that knockout of KIF21B results in longer microtubules that result in an inability to move the polarise the MT network by a mechanism consistent with dynein motor function at the immunological synapse to capture long MT and center the MT aster at the synapse. They use the Jurkat cell line, which is a classical model for this step in immune synapse function and fully appropriate. They show that KIF21B-GFP can rescue the knockout phenotype and then use this as a way to follow KIF12B dynamics in the Jurkat cells. KIF21B works by binding to the + end and inducing pausing and catastrophe, thus, more MT that are shorter when present. They also rescue the defect in the KIF21B Kos with 0.5 nM vinblastine, that directly increases catastrophes, shortens the MT and restores MT network polarization to the synapse. As a functional surrogate they investigate lysosome positioning at the synapse, which is one of the proposed functions of this cytoskeletal polarization. The use of expansion microscopy in this system is relatively new and clearly very powerful. The modelling component adds to the story and supports the sliding model proposed by Poenie and colleagues in 2006, but cannot say that there is no component of end capture and shrinkage as proposed by Hammer and colleagues more recently.

Reviewer #2:

This short study highlights the complexity of the octopaminergic system in insect behavior. This aspect of neuromodulation has received little attention in comparison with the role of dopamine in learning and motivation. The main question being addressed is whether, how and where octopamine modulates the generation of rhythmic behavior (peristalsis) upon noxious sensory stimulation (touch and pain). Using a combination of functional imaging and behavioral inspections, the authors explore the role of octopamine released by the VUM neurons on the escape crawling behavior of the Drosophila larva.

The specific observations reported in the study are:

1) Isolated larval CNS preparations that do not receive sensory input (deafferented preps) show spontaneous rhythmic wave patterns of neuronal activity in octopaminergic VUM neuron cluster.

2) In vivo preps that receive sensory input did not show spontaneous rhythmic patterns in the neural activity of the VUM neuron cluster.

3) The VUM neurons show weaker responses in clusters that get sensory input from physically stimulated body segments and stronger responses in clusters that get input from segments further away from stimulated segments.

4) In functional (GCaMP) imaging experiments, repeated gentle (rod) touch stimulations led to decreased VUM response intensities. Repeated harsh (brush) stimulations resulted in increasing VUM intensities. The authors correlate these physiological observations of the VUM activity with an increase in crawling speed upon repeated harsh stimulations, and a decrease in crawling speed upon repeated gentle touch stimulations.

Based on observations (4), the authors propose that the differences in the behavior elicited by series of gentle touch and harsh stimulations are due to differences in adaptation of two classes of mechanosensory neurons. The class III da neurons responsible for detecting gentle touch would quickly adapt, whereas the class IV da neurons responsible for detecting harsh touch would integrate neural activity over time. The authors also conclude that (i) the octopaminergic system is strongly coupled to the CPG underlying peristalsis and (ii) "it is simultaneously activated by physical stimulation, rather intensity than sequential coded" (line 53). The first conclusion is supported by observations (1-2). While the involvement of octopamine in the modulation of a key CPG of the larva is a certainly interesting result, it represents the starting point of a mechanistic inspection. The problem is that the rest of the study falls short of testing or establishing any concrete mechanism.

Although the topic of this study is exciting and its results are generally promising, the work is largely inconclusive. In addition, some conclusions are phrased in a way that is cryptic. For instance, I found it difficult to decipher the meaning of "the octopaminergic system is simultaneously activated by physical stimulation, rather intensity than sequential coded" (line 53). This conclusion appears to contradict the observation that repeated gentle touch stimulations produce a gradual decrease in the overall activity of VUM neurons. In the discussion section, the authors nicely refer to published findings in stick insects, honey beers and locusts. Compared to these systems, the advantage of Drosophila is that it offers the neuro-genetic tools to shed mechanistic insights into the molecular and cellular bases of neuromodulation.

Questions and mechanisms that the authors might have wanted to address at a mechanistic level:

Re. observations (1-2): What explains the observation that sensory inputs present in in-vivo preps abolish the spontaneous rhythmic pattern in the VUM activity? How does this relate to the VUM activity elicited by the tactile stimulations presented in Fig 3?

It would be important to establish the importance of the VUM activity on peristalsis through loss of function experiments. Expression of Tdc2 could be restrictive to the VNC by using tshirt-Gal4. These experiments would support the authors' proposal that octopamine is released to facilitate motor coordination (in lines 474-478).

Technical concerns:

-How can you rule out that the mini-stage featured in the in-vivo prep (Fig 2A) does not sever nervous fibers innervating the VNC? The plate placed under the CNS is very large. It is difficult to believe that this plate can be inserted while leaving all nerves (afferent and efferent neurons) intact on both sides. The integrity of the preparation should be controlled anatomically.

-In Fig 2, a statistical analysis should be performed to establish a lack of correlation between the VUM activity and patterns of crawling. Trial 2.2 suggests the existence of some correlation. This correlative analysis would be important to back up the statement that "unstimulated larvae showed no consistent VUM neuron responses correlated to crawling movements" (lines 228-229; see also lines 235-236).

-Lines 234-236: How can "movements" be assessed in an isolated deafferented prep?

Re. observation (3): Do the mechanosensory inputs have an inhibitory effect on the VUM activity patterns? If so, how does the inhibition come about?

How do you explain that harsh stimulation at the posterior end inhibits activity of both the most abdominal and thoracic segments? Does this imply that the t1 and a8 segments are somehow coupled?

In line 400, the authors propose that "VUM neurons as one possible system to modulate either indirectly the endogenous input or directly the central pattern generating neurons as a response to external tactile stimulation of the body wall." How does this model and subsequent discussion fit with the observations of Fig 3? It would be helpful to test the validity of the two alternatives described in line 400.

Technical concerns:

-Line 292: The segments displaying highest activity upon tactile stimulations are said to be consistent across consecutive simulations. Are they consistent across preparations as well? Were the data of Fig 3 generated on more than one prep?

-Are the results of Fig 3 dependent on the strength of the tactile stimulations? More than one intensity should be tested to rule out intensity coding, as is stated in the abstract (lines 53 and 55).

Re. observation (4): One of the observations reported in Fig 3 is that posterior harsh stimulations produce an overall increase in VUM activity whereas anterior harsh stimulation produce a decrease in activity. In Fig 4, larvae undergo harsh physical stimulations. However, it is unclear whether the harsh stimulations are applied to the posterior or anterior end of the larva. Based on the physiological results of Fig 3, wouldn't the authors expect that harsh stimulations of the head/neck region should lead to a deceleration of the larva, as was observed for gentle touch? Couldn't this prediction be tested experimentally? For the same reason, stating in line 512 that the same stimulation is used to activate the VUM neurons in Fig 3 and Fig 4 is misleading.

The discussion about the adaptive nature of the class III and IV da neurons is compelling. However it ought to be supported by more direct experimental evidence that could be collected in the Drosophila larva.

Reviewer #2:

This is a super interesting exploration of the dynamic allosteric changes in the SARS-CoV-2 S protein upon engagement with the angiotensin 2 converting enzyme 2 (ACE2) receptor (and vice versa). It also represents a tour de force for HDX-MS since the S protein is almost 1200 amino acids long and the ACE2 is also very large. The data are beautiful and the analysis is well-done. The S protein consists of two sub-domains S1 and S2 with the S1 needing to be cleaved-off so the S2 can become the fusion protein responsible for getting the SARS-CoV-2 into the cell. Structures are available but they do not shed light on how the protease furin can access the cleavage site between S1 and S2 in order to begin the process of fusion. In this paper, the Anand group shows that when ACE2 binds to the S protein, a conformational change occurs near the S1/S2 cleavage site exposing it and likely making it more susceptible to furin cleavage. It also dampens exchange in the stalk region. They call these regions "dynamic hotspots in the pre-fusion state".

There are some things that need to be addressed:

1) The manuscript appears to have been hastily written, it would benefit from a scientific editor making it more readable. For example, line 90 ff "Average deuterium exchange at these 91 reporter peptides was monitored for comparative deuterium exchange analysis of S protein, ACE2 receptor and S:ACE2 complex, along with a specific ACE2 complex with the isolated RBD." Presumably "reporter peptides" refers to the 321 peptides mentioned two sentences earlier...Why is the ACE2 complex with the isolated RBD qualified as "specific" while none of the others are? Then the article continues with more information about glycosylation…

2) Figure S1B the concentrations should be reported in molar not ng/ml

3) Line 90 and Figure S2: A bit more should be said about the glycosylation sites. If only non-glycosylated peptides are observed in the pepsin digestion, the coverage map (Fig. S2), shows expected lack of coverage for only a few sites (17, 122, 149, 165, 234, 282, 709, 1134) whereas many other sites are covered by peptides. Does this indicate that these sites are mostly not glycosylated?

4) Fig. S3 legend seems to indicate that uptake of each peptide is plotted, whereas uptake per residue should be plotted because overlapping peptides make these data misleading. The peptides are shown in the other relative uptake graphs, but then there is more than one data point per peptide. Can the authors explain a bit more in the legend how they got the data in these figures?

5) Fig. S4 seems to indicate that the cleavage site is already very dynamic. Can the authors explain this?

6) Line 98-99 "... Mapping the relative deuterium exchange across all peptides onto this S protein model showed the greatest deuterium exchange at the stalk region" seems to contradict lines 105-106 "The deuterium exchange heat map showed the highest relative exchange in the S2 subunit (Fig. S3) and helical segments," Please clarify.

7) Fig. 2 A and B look like the same molecular structure (nice that they are in the same orientation) but the domains are labeled differently. Yet a third domain listing is used in panel E. Comparing panels A and B, it's a little strange that some of the least dynamic spots in the Head/ECD are the highest exchanging, do the authors want to comment on this?

8) I thank the authors for the details provided in the Methods section regarding the HDX-MS data. If it wouldn't slow things down too much, it would be great if the RFU data were calculated after back exchange correction. Even an imperfect correction (such as a global correction for the back exchange during analysis) would make the data more meaningful.

9) Fig. 3C and 3D look remarkably different considering that they both are reflecting the RBD:ACE2 interaction. Did the authors attempt to find a convergent set of peptides to do this analysis? Perhaps if the binding site were labeled it would help make the differences look less important (overall the top part of the molecule is blue and the bottom more-or-less has some red and if that's all we are supposed to get out of this figure then it is ok).

10) Fig. 4. The authors state that the significance cut-off for difference in deuterium exchange is 0.3 D but I don't see where they explain how they derived this value.

DOI: 10.1016/j.celrep.2020.108404

Resource: (ZFIN Cat# ZDB-ALT-160726-2,RRID:ZFIN_ZDB-ALT-160726-2)

Curator: @Naa003

SciCrunch record: RRID:ZFIN_ZDB-ALT-160726-2

Curator comments: allele name: ubs10Tg Danio rerio ZFIN Cat# ZDB-ALT-160726-2

What is this?

DOI: 10.1016/j.celrep.2020.108404

Resource: (ZFIN Cat# ZDB-ALT-110707-2,RRID:ZFIN_ZDB-ALT-110707-2)

Curator: @Naa003

SciCrunch record: RRID:ZFIN_ZDB-ALT-110707-2

Curator comments: allele name: i186Tg Danio rerio ZFIN Cat# ZDB-ALT-110707-2

What is this?

DOI: 10.1016/j.celrep.2020.108404

Resource: (ZFIN Cat# ZDB-ALT-060719-2,RRID:ZFIN_ZDB-ALT-060719-2)

Curator: @Naa003

SciCrunch record: RRID:ZFIN_ZDB-ALT-060719-2

Curator comments: allele name: f1Tg Danio rerio ZFIN Cat# ZDB-ALT-060719-2

What is this?

Reviewer #2:

General assessment:

Using rsfMRI data, the authors showed that unlike the cortex, cerebellum, and caudate, the thalamus and the pallidum of the lenticular nucleus have strongly asymmetric principal functional gradients across the two hemispheres. Using a laterality metric and confirmed with seed-based rsfMRI, they showed that these thalamic and lenticular asymmetries correspond with hemispheric laterality. They report that the cerebellum and caudate have asymmetric secondary and tertiary gradients. Finally, by summing cortical connectivity maps weighted by the functional gradients, the authors show that the asymmetric functional gradients of the cerebellum and caudate are associated with the default network, while those of the thalamus and lenticular nucleus are associated with the ventral attention network. The Discussion argues for an anatomy-informed model explaining these results.

These observations and the posited model are very interesting, but I have a serious concern with grouping the putamen with the pallidum as the lenticular nucleus, and drawing conclusions based on this. Also, more work needs to be done to rule out technical artifacts and improve the writing.

List of substantive concerns:

1) Why did you group the putamen and globus pallidus together into the lenticular nucleus? The globus pallidus is equally connected to the caudate as to the putamen. There's nothing special functionally between the putamen and pallidum-they were called lenticular nuclei by early anatomists based on their lens-like shape. In fact, I would have grouped the caudate and putamen together as the striatum, and considered the pallidum separately. Grouping the putamen and pallidum together creates a false sense of variability in the lenticular nucleus (Table 1). Based on that, the inferences resting on observations with the lenticular nucleus do not hold in the Discussion. The manuscript should be re-written to address the results of the pallidum specifically, rather than lenticular nucleus. Critically, how would this change the authors' interpretations and dichotomous model in the Discussion?

2) Another problem with the pallidum is that this is adjacent to the thalamus and may suffer from signal bleeding. Work needs to be done, perhaps by regressing out each signal from the other, to show that the pallidal results are not due to signal bleeding from the thalamus.

3) As the authors state, a known asymmetry in the brain is the lateralization of certain heteromodal cortical networks, yet these "positive controls" appear highly symmetric (Supp Fig. 1A), at least in comparison to the asymmetry of the thalamus and pallidum. Is this surprising to the authors?

4) My first order interpretation of the results-that there's greater functional asymmetry/lateralization for the pallidum and thalamus than other brain structures-would be that these structures simply have preferentially ipsilateral connections. The pallidum in particular is a middle link in cortico-basal ganglia-thalamic circuits-it could simply have asymmetry because its connections are mostly with the ipsi basal ganglia and thalamus. A simpler explanation is to see whether these results correspond to anatomical connectivity strength. What are the ispi versus contra connections of these thalamic nuclei to cortical regions?

5) What does it mean that the asymmetric (sensorimotor?) parts of thalamus are associated with the ventral attention cortical network?

6) In the Discussion, my first order prediction of the rsfMRI reflections of indirect/direct and driver/modulatory connections would be that direct or driver connections lead to a stronger "influence" of the cortex's properties to the downstream subcortical region. Thus, regions receiving direct or driver connections would be symmetric or asymmetric in a manner consistent with the cortical regions they are connected to. Wouldn't you expect the "influence" of the cortex to be stronger for the regions receiving driver versus modulatory or direct versus indirect inputs?

7) What other connectional differences explaining these results did you consider and rule out (and for what reason), in addition to cortical inputs?

8) The dichotomous model interpretation is very interesting, but as there is no direct evidence presented by this paper, I would state these interpretations more speculatively in the Abstract and throughout the paper.

Reviewer #2:

Here authors show interesting, seemingly counter-intuitive, associations between key Alzheimer's pathological hallmarks (Aβ and tau) and free-water corrected diffusion measures in a large cohort of cognitively healthy older adults with family history of Alzheimer's. They show direct associations between amyloid (and tau in some cases) and increased FA and decreased MD/RD in key white matter bundle cortical endpoints. Whilst for some tracts this association is only just 'statistically significant' at p<0.05, results for the uncinate fasciculus are very convincing. Overall, this paper is an interesting, well-written and potentially highly impactful piece of work with robust methodology, in which the authors should take pride.

I have no major concerns to raise regarding this paper. However, I will mention for the authors' interest, that the principle of a biphasic change in quantitative MRI measures (initial decrease due to water mobility restriction, followed by later increase associated in symptomatic phase) is one discussed in a recently published paper (rdcu.be/b62Yp). A linear change across the course of the disease (which the authors here say would be impossible to detect in slowly progressing individuals) may be brought about by studying the changing and increasing distribution width, rather than averaging across a region of interest. I am not suggesting the authors change their analyses to reflect this, it is merely food for thought, or worth a mention in the paper as an avenue of future research.

Reviewer #2:

General assessment of the work:

The authors present the Phenotypix, a device that uses piezoelectric pressure-sensors, in combination with video recording and signal analysis, to observe physiological states within a subject mouse. Using computational approaches, they show that this device can detect locomotion, and even sub-components of locomotion such as grooming. Similarly, they show the device can detect heart rate and breathing rate in both anesthetized and awake (but immobile) subjects. Next, in a series of proof-of-concept experiments they show that differences in pain, fear, and gait responses can be detected between control and experimental subjects.

Numbered summary of substantive concerns:

1) The anti-vibrational setup that the system is located on appears to be critical to successful use of the system. Please provide some parametric data showing how different degrees of dampening influence system performance. This will be critical for replication of results in different labs.

2) How does the device account for changes in the environment, such as bedding moving around or the animal defecating/urinating? Is this system compatible with behavioral enrichment like cotton bedding, etc?

3) Is it possible to track multiple subjects in a single chamber? This seems like it should be feasible with the inclusion of video data in the analysis.

4) It appears that only locomotion related data can be reliably recorded while the subjects are moving, and that features such as heart rate and respiration rate are limited to immobile states. Is this correct? If so, a discussion of potential ways to overcome this confound would be welcomed.

5) The lack of publicly available code and data is not compatible with the mission of supporting the open science environment. It has also made evaluating the technical merit of the work in this manuscript difficult.

Reviewer #2:

Extracting ion channel kinetic models from experimental data is an important and perennial problem. Much work has been done over the years by different groups, with theoretical frameworks and computational algorithms developed for specific combinations of data and experimental paradigms, from single channels to real-time approaches in live neurons. At one extreme of the data spectrum, single channel currents are traditionally analyzed by maximum likelihood fitting of dwell time probability distributions; at the other extreme, macroscopic currents are typically analyzed by fitting the average current and other extracted features, such as activation curves. Robust analysis packages exist (e.g., HJCFIT, QuB), and they have been put to good use in the literature.

Münch et al focus here on several areas that need improvement: dealing with macroscopic recordings containing relatively low numbers of channels (i.e., hundreds to tens of thousands), combining multiple types of data (e.g., electrical and optical signals), incorporating prior information, and selecting models. The main idea is to approach the data with a predictor-corrector type of algorithm, implemented via a Kalman filter that approximates the discrete-state process (a meta-Markov model of the ensemble of active channels in the preparation) with a continuous-state process that can be handled efficiently within a Bayesian estimation framework, which is also used for parameter estimation and model selection.

With this approach, one doesn't fit the macroscopic current against a predicted deterministic curve, but rather infers - point by point - the ensemble state trajectory given the data and a set of parameters, themselves treated as random variables. This approach, which originated in the signal processing literature as the Forward-Backward procedure (and the related Baum-Welch algorithm), has been applied since the early 90s to single channel recordings (e.g., Chung et al, 1990), and later has been extended to macroscopic data, in a breakthrough study by Moffatt (2007). In this respect, the study by Münch et al is not necessarily a conceptual leap forward. However, their work strengthens the existing mathematical formalism of state inference for macroscopic ion channel data, and embeds it very nicely in a rigorous Bayesian estimation framework.

The main results are very convincing: basically, model parameters can be estimated with greater precision - as much as an order of magnitude better - relative to the traditional approach where the macroscopic data are treated as noisy but deterministic (but see my comments below). Estimate uncertainty can be further improved by incorporating prior information on parameters (e.g., diffusion limits), and by including other types of data, such as fluorescence. The manuscript is well written and overall clear, and the mathematical treatment is a rigorous tour-de-force.

There are several issues that should be addressed by the authors, as listed below.

1) I think packaging this study as a single manuscript for a broad-audience is not optimal. First, the subject is very technical and complex, and the target audience is probably small. Second, the study is very nice and ambitious, but I think clarity is a bit impaired by dealing with perhaps too many issues. The state inference and the bayesian model selection are very important but completely different issues that may be better treated separately, perhaps for a more specialized readership where they can be developed in more detail. Tutorial-style computational examples must be provided, along with well commented/documented code. The interested readers should be able to implement the method described here in their own code/program.

2) The authors should clearly discuss the types of data and experimental paradigms that can be optimally handled by this approach, and they must explain when and where it fails or cannot be applied, or becomes inefficient in comparison with other methods. One must be aware that ion channel data are very often subject to noise and artifacts that alter the structure of microscopic fluctuations. Thus, I would guess that the state inference algorithm would work optimally with low noise, stable, patch-clamp recordings (and matching fluorescence recordings) in heterologous expression systems (e.g., HEK293 cells), where the currents are relatively small, and only the channel of interest is expressed (macropatches?). I imagine it would not be effective with large currents that are recorded with low gain, are subject to finite series resistance, limited rise time, restricted bandwidth, colored noise, contaminated by other currents that are (partially) eliminated with the P/n protocol with the side effect of altering the noise structure, power line 50/60 Hz noise, baseline fluctuations, etc. This basically excludes some types of experimental data and experimental paradigms, such as recordings from neurons in brain slices or in vivo, oocytes, etc. Of course, artifacts can affect all estimation algorithms, but approaches based on fitting the predicted average current have the obvious benefit of averaging out some of these artifacts.

The discussion in the manuscript is insufficient in this regard and must be expanded. Furthermore, I would like to see the method tested under non-ideal but commonly occurring conditions, such as limited bandwidth and in the presence of contaminating noise. For example, compare estimates obtained without filtering with estimates obtained with 2, 3 times over-filtering, with and without large measurement noise added (whole cell recordings with low-gain feedback resistors and series resistance compensation are quite noisy), with and without 50/60 Hz interference. How does the algorithm deal with limited bandwidth that distorts the noise spectrum? How are the estimated parameters affected? The reader will have to get a sense of how sensitive this method is to artifacts.

3) A better comparison with alternative parameter estimation approaches is necessary. First of all, explain more clearly what is different from the predictor-corrector formalism originally proposed by Moffatt (2007). The manuscript mentions that it expands on that, but exactly how? If it is only an incremental improvement, a more specialized audience is more appropriate.

Second, the method proposed by Celentano and Hawkes, 2004, is not a predictor-corrector type but it utilizes the full covariance matrix between data values at different time points. It seems to me that the covariance matrix approach uses all the information contained in the macroscopic data and should be on par with the state inference approach. However, this method is only briefly mentioned here and then it's quickly dismissed as "impractical". I am not at all convinced that it's impractical. We all agree that it's a slower computation than, say, fitting exponentials, but so is the Kalman filter. Where do we draw the line of impracticability? Computational speed should be balanced with computational simplicity, estimation accuracy, and parameter and model identifiability. Moreover, that method was published in 2004, and the computational costs reported there should be projected to present day computational power. I am not saying that the authors should code the C&H procedure and run it here, but should at least give it credit and discuss its potential against the KF method.

The only comparison provided in the manuscript is with the "rate equation" approach, by which the authors understand the family of methods that fit the data against a predicted average trajectory. In principle, this comparison is sufficient, but there are some issues with the way it's done.

Table 3 compares different features of their state inference algorithm and the "rate equation fitting", referencing Milescu et al, 2005. However, there seems to be a misunderstanding: the algorithm presented in that paper does in fact predict and use not only the average but also - optionally - the variance of the current, as contributed by stochastic state fluctuations and measurement noise. These quantities are predicted at any point in time as a function of the initial state, which is calculated from the experimental conditions. In contrast, the KF calculates the average and variance at one point in time as a projection of the average and variance at the previous point. However, both methods (can) compare the data value against a predicted probability distribution. The Kalman filter can produce more precise estimates but presumably with the cost of more complex and slower computation, and increased sensitivity to data artifacts.

Fig. 3 is very informative in this sense, showing that estimates obtained with the state inference (KF) algorithm are about 10 times more precise that those obtained with the "rate equation" approach. However, for this test, the "rate equation" method was allowed to use only the average, not the variance.

Considering this, the comparison made in Fig 3 should be redone against a "rate equation" method that utilizes not only the expected average but also the expected variance to fit the data, as in Milescu et al, 2005. Calculating this variance is trivial and the authors should be able to implement it easily (and I'll be happy to provide feedback). The comparison should include calculation times, as well as convergence.

4) As shown in Milescu et al, 2005, fitting macroscopic currents is asymptotically unbiased. In other words, the estimates are accurate, unless the number of channels is small (tens or hundreds), in which case the multinomial distribution is not very well approximated by a Gaussian. What about the predictor-corrector method? How accurate are the estimates, particularly at low channel counts (10 or 100)? Since the Kalman filter also uses a Gaussian to approximate the multinomial distribution of state fluctuations, I would also expect asymptotic accuracy. Parameter accuracy should be tested, not just precision.

5) The manuscript nicely points out that a "rate equation" approach would need 10 times more channels (N) to attain the same parameter precision as with the Kalman filter, when the number of channels is in the approximate range of 10^2 ... 10^4. With larger N, the two methods become comparable in this respect.

This is very important, because it means that estimate precision increases with N, regardless of the method, which also means that one should try to optimize the experimental approach to maximize the number of channels in the preparation. However, I would like to point out that one could simply repeat the recording protocol 10 times (in the same cell or across cells) to accumulate 10 times more channels, and then use a "rate equation" algorithm to obtain estimates that are just as good. Presumably, the "rate equation" calculation is significantly faster than the Kalman filter (particularly when one fits "features", such as activation curves), and repeating a recording may only add seconds or minutes of experiment time, compared to a comprehensive data analysis that likely involves hours and perhaps days. Although obvious, this point can be easily missed by the casual reader and so it would be useful to be mentioned in the manuscript.

6) Another misunderstanding is that a current normalization is mandatory with "rate equation" algorithms. This is really not the case, as shown in Milescu et al, 2005, where it is demonstrated clearly that one can explicitly use channel count and unitary current to predict the observed macroscopic data. Consequently, these quantities can also be estimated, but state variance must be included in the calculation. Without variance, one can only estimate the product i x N, where i is unitary current and N is channel count. This should be clarified in the manuscript: any method that uses variance can be used to estimate i and N, not just the Kalman filter. In fact, the non-stationary noise analysis does exactly that: a model-blind estimation of N and i from non-equilibrium data. Also, one should be realistic here: in some circumstances it is far more efficient to fit data "features", such as the activation curve, in which case the current needs to be normalized.

7) I think it's great that the authors develop a rigorous Bayesian formalism here, but I think it would be a good idea to explain - even briefly - how to implement a (presumably simpler) maximum likelihood version that uses the Kalman filter. This should satisfy those readers who are less interested in the Bayesian approach, and will also be suitable for situations when no prior information is available.

8) The Bayesian formalism is not the only way of incorporating prior knowledge into an estimation algorithm. In fact, it seems to me that the reader would have more practical and pressing problems than guessing what the parameter prior distribution should be, whether uniform or Gaussian or other. More likely one would want to enforce a certain KD, microscopic (i)reversibility, an (in)equality relationship between parameters, a minimum or maximum rate constant value, or complex model properties and behaviors, such as maximum Popen or half-activation voltage. A comprehensive framework for handling these situations via parameter constraints (linear or non-linear) and cost function penalty has been recently published (Salari et al/Navarro et al, 2018). Obviously, the Bayesian approach has merit, but the authors should discuss how it can better handle the types of practical problems presented in those papers, if it is to be considered an advance in the field, or at least a usable alternative.

9) Discuss the practical aspects of optimization. For example, how is convergence established? How many iterations does it take to reach convergence? How long does it take to run? How does it scale with the data length, channel count, and model state count? How long does it take to optimize a large model (e.g., 10 or 20 states)? Provide some comparison with the "rate equation method".

10) Here and there, the manuscript somehow gives the impression that existing algorithms that extract kinetic parameters by fitting the average macroscopic current ("fitting rate equations") are less "correct", or ignorant of the true mathematical description of the data. This is not the case. Published algorithms that I know of clearly state what data they apply to, what their limitations are, and what approximations were made, and thus they are correct within that defined context and are meant to be more effective than alternatives. Some quick editing throughout the manuscript should eliminate this impression.

11) The manuscript refers to the method where the data are fitted against a predicted current as "rate equations". I don't actually understand what that means. The rate equation is something intrinsic to the model, not a feature of any algorithm. An alternative terminology must be found. Perhaps different algorithms could be classified based on what statistical properties are used and how. E.g., average (+variance) predicted from the starting probabilities (Milescu et al, 2005), full covariance (Celentano and Hawkes, 2004), point-by-point predictor-corrector (Moffatt, 2007).

Reviewer #2:

The article brings to light the functional consequences of the activity of SuM afferents terminating at CA2 neurons in the hippocampus using a combination of a variety of methods like whole-cell voltage clamp and optogenetics. In addition, the authors provide evidence that modulation of the CA2 neurons by SuM afferents affects the activity pattern of CA1 neurons. Specifically, the study reveals that the 'functional' connectivity between SuM and CA2 is mainly mediated by the regulation of PV+ basket cells that are involved in the feed forward inhibition of CA2 principal neurons. This study is also relevant in the context of neuropsychiatric disorders where PV+ IN density in the CA2 area is preferentially reduced.

It would be good if some results and implications are further clarified for better understanding in the discussion section:

1) The results indicate that SuM recruits a feed forward inhibition onto CA2 PNs, which contributes to the shaping of CA2 AP firing. However, it is not entirely intuitive how the feed forward inhibition of CA2 PNs by SuM also reduces CA1 activity, as CA2 has also been known to recruit strong feed forward inhibition onto CA1. This would intuitively suggest that decrease in CA2 activity by photostimulation of SuM afferents will in turn decrease the feed forward inhibition by CA2 onto CA1, and thereby increase CA1 activity. However, the results suggest otherwise. Would this be suggestive of a stronger direct excitatory projection from CA2 to CA1 PNs that is more dominant than the feed forward inhibition of CA1 PNs by CA2? This may be a good point to further elaborate on in the discussion section, so that the effect of SuM-CA2 connectivity on CA1 output becomes clearer.

2) In the introduction section line 44, it is written that 'CA2 neurons do not undergo NMDA-mediated synaptic plasticity'. This may not always be the case; rather it may be better to rephrase 'NMDA-mediated' as 'high frequency stimulation-induced'. It has been shown previously that NK1 receptor activation by pharmacological application of substance P in hippocampal slices triggers a slow onset NMDA-dependent LTP in CA2 neurons by high frequency stimulation of CA3 afferents to CA2 (Dasgupta et al., 2017).

3) Line 250: "BC transmission is insensitive to MOR activation (Glickfeld et al., 2008)."

Was the Glickfeld study done in CA2 neurons? If not, it would be good to show that PV+ CA2 BCs are also sensitive to DAMGO and to what degree? The experiment shows that IPSC in PNs are inhibited by DAMGO that should have enhanced light induced EPSCs if PV+ BCs are responsible for feed forward inhibition. But it seems that has not been observed. What are direct EPSCs - electrical stimulation of CA3-CA2 synapses?

4) Overall, the results seem to suggest that SuM stimulation would induce a net inhibition (?) of CA2 PNs by recruiting interneurons (INs). However, the role played by the direct glutamatergic connections from SuM to CA2 PNs is not entirely clear. Is it less prominent due to sparse SuM-PN projections compared to SuM-IN connections in the CA2 area? It may be good to elaborate on this a bit in the discussion.

Reviewer #2:

In this manuscript, the authors combine genetic/hormonal manipulation of expansin expression, localization studies, and mechanical measurements of root cell walls to study how this family of cell wall-loosening proteins influences root growth and development. This is an exciting topic, since expansins have a long history of in vitro characterization, but their characterization in living plants has lagged behind. The localization patterns of EXPA1, EXPA10, EXPA14, and EXPA15 are depicted using mCherry fusion proteins, and are shown to be distinct from one another. Despite the wide range of interesting approaches described here, I have some important concerns about the work as it stands, in terms of providing new insights into how expansins actually influence root growth.

Major Comments:

One major concern is the lack of appropriate controls, statistical appropriateness, and reporting (e.g., defining "n" clearly in all cases) in this work. All comparisons should include wild type and no-treatment controls; for example, in Figure 8, no AFM images are shown for wild type or EXPA1 overexpression cells.

Figure 1-S1: there is no change in pEXPA1::nls:3xGFP - why is there this discrepancy with the EXPA1 qPCR result? This is not explained.

Figure 3-S1: The finding of a lack of colocalization between EXPA10 and CFW staining is not convincing, due to a lack of a control showing positive colocalization and a lack of quantification of the degree of colocalization (e.g., Pearson correlation coefficient between red/blue pixels). The authors use these data as a lynchpin for part of their discussion, but this lack of colocalization could simply be an artifact of chromatic aberration, etc.

L256: This statement is not supported by the statistical comparisons shown in Figure 5B-C. In Figure 5B, why does the WT show higher MOC with Dex than without? In Figure 5B-C, you do not compare 8-4 + Dex with WT + Dex statistically, which is the salient comparison, and instead compare each genotype with vs. without Dex. In addition, the fact that the pRPS5A>GR>EXPA1:mCherry line does not show a significant difference in BLS signal with Dex addition (Figure 5-S1) argues against a clearly established relationship between expansin expression and BLS signal. The data in Figure 5D-E are more informative, but there is no wild type control for these experiments.

In Figure 8, the AFM color code scales do not seem to match the graphs, in that the color scales range from 0-2 MPa, whereas the graph Y axes range from 0 to 3 e6 MPa (unless that is supposed to be 0-3 MPa, or 0 to 3 e6 Pa!). No-Dex controls are missing from 8B.

In the Discussion, the authors use the words "unclear" and "elusive", and "remains to be identified" to sum up their work, and this to me is an indication of the state of this work overall. Although some of the data are intriguing, they are neither conclusive nor explanatory in revealing the mechanisms of expansin-mediated growth control in roots.

Finally, the manuscript needs to be revised for proper English grammar, syntax, and style.

Reviewer #2:

This study performs behavioral assessment of the impact of watching lip movements on tone detection in noise and EEG recordings from passive observers of the same movies. The basic paradigm is that listeners watch a silent movie of lip movements (selected to be at ~theta rate) while listening for tone bursts that occur most commonly twice in a trial (early and late). The key findings are that perceptual sensitivity is higher when tones are in the second half of the trial, when hits align at a particular phase angle of the visual stimuli. Brain signals were also observed to entrain through the course of the trial. The authors conclude that visual modulation of auditory excitability explains these effects.

The stimulus design is elegant, and if taken at face value are a nice demonstration that visual stimuli can modulate auditory perception in a temporally specific manner. However, I have concerns with the interpretation of the data while also feeling to some extent that these findings are expected; stimulating AC with a speech envelope modulates speech perception (Wilsch et al., 2018), silent speech modulates human auditory cortex (Calvert 1999) and visual stimuli modulated at theta rates directly entrain auditory cortical phase in animals (Atilgan et al., 2018) as do audiovisual speech stimuli in humans (Zion-Golumbic et al., 2013). This study is a further piece of evidence along these lines, but it's hard to be certain of a causal relationship when the behaviour and neurophysiology are in different listeners. I also have some concerns about the current interpretation some of which are addressable with additional analysis.

I'm not convinced that the authors have sufficiently ruled out the possibility that the first tone causes a phase reset in AC that causes detected second tones to be entrained to a particular stimulus phase. In theory this should be easily addressed by looking at the 1 tone trials where the tone is in the second half of the stimulus. These data are in the supplemental material but are not particularly reassuring - while the d' is higher for the second tone, but the phase angles are uniformly distributed across participants in comparison to the clustering observed in the 2-tone data. This finding calls into question the causal link between the phase relationship and performance. The authors note that there are relatively few trials (50% of those available in the 2 tone data) - the contribution that this plays could be addressed by subsampling half the trials from the 2 tone dataset and re-estimating the phase modulation to estimate whether the single tone condition is any different. Another analysis that could be enlightening/ reassuring would be to compute the phase of the hits to tone 2 relative to the onset of tone 1 using the modulation rate of the clip (or 6 Hz, if clips were selected to be that anyway).

I would like to see the distribution of the tones w.r.t. the phase of the lip movement (all tones, not just hits) to be reassured that there is nothing inherent in the movies that causes the phase alignment?

The neurophysiology does not demonstrate a significant increase in entrainment from early to late windows, only that there is a different phase angle. Doesn't this also call into question the conclusion that performance is better in the second half due to better entrainment? While the phase in the second might be 'more efficient' if the entrainment is equivalent shouldn't there be a behavioural relationship in both cases? This is where performing both behaviour and EEG simultaneously (or at least in the same listeners) may have proved enlightening.

Reviewer #2:

This manuscript addresses the evolutionary benefits of integrase activity using experimental evolution of integrons in the presence of antibiotics. The authors demonstrate that activity increases survival of populations at high gentamicin concentrations, by shuffling a gentamicin resistance cassette towards the start of the integron.

The paper is very well written and interesting, and demonstrates neatly the benefits of integron shuffling. I am suggesting a few additional assays, in order to measure phenotypic effects of evolved integrons. However, if these are not possible to perform , the main conclusions could be slightly altered instead to focus more on the genomics.

Major Comments:

1) The paper would benefit from MIC assays (or any other resistance measure) using evolved clones, to properly demonstrate and quantify the evolution of increased resistance associated with the different integron arrays. For now, the only phenotypic data measured from the evolution experiment is survival of populations during the experiment itself. I was first going to say that this is a minor comment, as the genetic / genomic data is very interesting and solid on its own, but the paper is still framed around evolution of increased antibiotic resistance, which is not directly quantified. Survival of populations might be influenced by other factors, including the chromosomal mutations described in the manuscript but also non-genetic effects, for instance population density effects, with populations that grow slightly more at a given time point then having a higher inoculum for the next step.

2) MIC assays could even be done with no need for further sequencing, using clones from the populations in which integrons are not polymorphic (Fig 3B). Comparing resistance levels for the aadB-blaVEB-1-dfrA5-aadB array, and the aadB-aadB and aadB arrays with the ancestral array would allow the authors to link genotype and phenotype, and to demonstrate more directly the selective advantages (or absence of, for some of the arrays) that they suggest. Effects of plasmid evolution could also be separated relatively easily from chromosomal mutations that contribute to gentamicin resistance by transferring evolved plasmids to an unevolved host.

3) I don't actually think anything else is happening than the evolution of increased resistance via shuffling that the authors are suggesting - and they are very careful in stating clearly that increased resistance is only 'suggested' whenever they discuss the genomic results directly. But I am still a bit uneasy about drawing conclusions of increased antibiotic resistance (in the title, end of introduction, and conclusion) when the only phenotypic data is survival at the population level. Alternatively, this text could be reformulated to focus clearly on the genetics and not on phenotypic resistance.

Reviewer #2:

In this work, the authors analyze fungal and bacterial communities in 49 host species and find evidence of phylosymbiosis, a correlation between these microbiomes and host that suggests host recruitment of specific microbial communities. They further carry out a network analysis that suggests co-occurrence of fungal and bacterial communities across hosts. While host recruitment has been shown previously for bacteria, the authors here include a broad survey of mycobiomes and based on their analysis conclude that fungal communities are also critical to interactions and host health.

This descriptive study provides important insight regarding the general characteristics of the mycobiome and its relationship to the bacterial communities and the host. The work is in agreement with these fungal communities being important for host function and health, the work does not provide direct information on these communities, their interactions or possible effects on the host.

The overall presentation of the results are geared towards a focused readership.

The authors could be more explicit regarding the value behind the modularity of networks for a given host (in mammals) and what exactly is the significance of this finding in the broad context of microbiomes.

Some groups of samples are obtained from very varied sources (amphibia) but others are not. Beyond sample type being important, what other effects could these sampling differences have on the final conclusions, for example in their network analysis?

What is the significance of having some species with more negative interactions? Are there any ideas how a negative interaction can be sustained over time?

Reviewer #2:

In this manuscript, Jado et al. studied the in vitro evolution of the haploid cell line HAP1 in the presence of five common anti drug agents. The authors exposed the cells to the drugs and then performed whole-exome or whole-genome sequencing (WES or WGS) in order to identify point mutations (SNVs) and copy number changes (CNVs) associated with resistance. In multiple cases, the authors confirmed that shRNA-mediated knockdown of a candidate gene (that is, a gene that was recurrently mutated at high allele fractions, or recurrently lost/gained) indeed conferred resistance to the drug.

Overall, this is an elegant demonstration that in vitro evolution in cancer cell lines can be useful for the study of chemotherapy resistance. Surprisingly, relatively few studies attempted to identify resistance mechanisms to anticancer drugs using spontaneous evolution experiments, despite the prevalence of this approach in the study of antibiotics resistance. While the authors were able to identify and validate a few known resistance mechanisms to very commonly-used drugs, a major limitation of the current study is that it doesn't really shed any new light on chemotherapy resistance mechanisms. While I appreciate the time and effort that were required to perform the drug experiments and sequence the various clones, the follow-up studies are rather superficial and do not really extend our knowledge on any of the proposed mechanisms of drug resistance.

Specific Comments:

1) The AF threshold of 0.85 seems pretty arbitrary. Can this threshold be determined empirically based on the sequencing depth and noise of each sample? Mutations with AF>0.85 may still be subclonal, whereas mutations with AF<0.85 may still be of interest.

2) While the rationale for performing the initial experiments in HAP1 cells is clear, it is unclear why no validation experiments were performed in additional cancer cell lines. It is imperative to perform the knockdown experiments not only in HAP1 cells but in a panel of additional cancer cell lines, in order to examine whether these are general mechanisms of resistance.

3) Multiple CRISPR-Cas9 studies were performed to identify mechanisms of drug resistance to anticancer drugs. The authors note in the Discussion that these studies "are useful but cannot readily reveal critical gain-of-function, single nucleotide alleles". This makes sense, yet in almost all cases the authors use a simple loss-of-function shRNA assay in order to confirm their initial sequencing results. This means that the added value of the spontaneous evolution approach is rather limited, either because other mechanisms of resistance are much less common or because it is much easier to identify them.

4) In the gemcitabine resistance experiment, the authors confirmed that RRM1 KD increased the sensitivity of the cells to the drug. A complementary experiment should be to test whether the overexpression of RRM1 would increase the resistance.

5) In several cases, multiple SNVs or CNVs were identified in the same resistant clone at a clonal (or near-clonal) AF. Other than following up on "immediate suspects", is there a systematic way to tease apart resistance "drivers" from "passengers"? This should be at least discussed.

6) The manuscript would benefit from language editing, there are quite a few grammatical errors.

Reviewer #2:

In this paper, Kilroy, J.K. et al. Assess if inactivity in dmd zebrafish is deleterious for muscle structure and function. The authors first, categorized dmd fish into mild and severe phenotypic groups but by 8dpf this phenotypic variability disappears. Next, the authors devised two inactivity regimes: intermittent and extended and found that only fish undergoing extended inactivity exhibited improved muscle phenotype followed by rapid deterioration of muscle structures. Furthermore, these fish were more susceptible to contraction-induced injury. Finally, by varying the frequency, amplitude, and pulse of an electrical current, the authors developed four types of neuromuscular stimulation (NMES) aimed to mimic varying levels of strength training exercises. They found that endurance NMES improved muscle structure, reduced degeneration and increased fiber regeneration.

Major Concerns:

1) For the dmd phenotypic variability: the authors conclude that mild dmd phenotypic fish undergo extensive degeneration for the first three days followed by slight regeneration, while severe dmd fish undergo muscle regeneration throughout the study merit some caution. The authors should consider degeneration and regeneration rates. Compared to dmd fish exhibiting a mild muscle phenotype, dmd fish rate of degeneration early in development might exceed that of regeneration, while later in development, the rate of degeneration is probably lower compared to that of regeneration. To confirm that regeneration is the cause for increased muscle brightness over time in fish with severe muscle phenotype, assays showing degeneration, regeneration (and eventual failure of regeneration) should be performed.

2) Intermittent inactivity: zebrafish are diurnal, thus it is not surprising that sedating fish at night, when they are naturally at rest, resulted in no major effects on muscle organization. Authors should consider repeating this experiment with daytime sedation and/or alternating between day and night intermittent inactivity. It is not obvious if the authors are referring to fish with mild and/or severe muscle phenotype. This is particularly important because the authors are focusing their birefringence analysis between 5-8 dpf in which phenotypic variability was reported and the mild and severe phenotype have not yet converged. Please clarify.

3) Birefringence is one of two main assays used throughout the study. Birefringence is an assay that relies on polarized light bouncing from the anisotropic surfaces. Due to the anisotropic nature of the muscle this assay allows for visualizing the structure of the muscle. However, alignment of the fish is a critical part for this assay, if fish are not aligned with the direction of polarized light will exhibit a reduced and variable birefringence results. Thus, this might explain the discrepancy between muscle structure (birefringence assay) and muscle function (swimming behavior) in comparing the different NMES paradigms.

Perhaps a Western blot assays for quantifying either a muscle or housekeeping protein during 5, 6, 7, 8 dpf between wildtype, dmd and dmd NMES treated fish might provide a quantitative picture of degeneration and regeneration cycles based on protein mass of the fish. That is, if the muscles are degenerating, these fish will have less total protein to that of its control and treated counterparts.

4) Although the authors showed that inactive fish are more susceptible to NMES training. NMES was performed after the inactivity period. No experiments showing NMES treatments during extended inactivity will rule out if NMES could alleviate muscle wasting in relatively inactive fish.

5) Although the authors found differential gene expression between dmd and wildtype fish that have undergone eNMES treatment. The authors fail to show differential gene expression in dmd and wildtype fish not undergoing eNME treatment. This comparison is critical for determining if eNMES is the result of these changes in genes expressed between both strains.

6) Authors argue that eNMES improves cell adhesion based on % of fish exhibiting muscle detachment recovery. Authors should consider staining for ECM proteins in dmd and dmd plus eNMES fish to determine if indeed eNMES treatment improved cell adhesion.

Reviewer #2:

General assessment of work:

In contrast to the author's claim of OSA, the experimental design mostly focused on intermittent hypoxia neglecting sleep pattern and arterial oxygen level. The entire study is based on exploratory approach without any validation, confirmatory experiments. The selection of marker to cluster many cells is not critical. It seems that this selection method caused various abnormal biological process patterns, types and proportion of certain reported cells in the lung.

Summary:

1) OSA is having complex pathophysiology and IH is the one aspect of OSA. As it seems that the authors did not measure arterial oxygen pressure upon the induction of IH and also it was not sure IH was induced when the animals were really on sleeping mode. In Figure 6, they should have tested the gene expression of OSA patients to make sure that their models are physiologically relevant. So it would be better to avoid OSA in the manuscript but they can mention the IH.

Results:

2) While it is understood that the authors tried to mimic OSA by doing the experiments in "inactive phase" to conduct IH, what will happen if they do in active phase? Do the authors expect the changes in circadian rhythm related genes when they induce IH in active phase? As the authors did not focus on sleep pattern (it seems), "inactive" and "active phase" should not be an issue. The authors should clearly mention that what is the sleep pattern during "inactive" or experimental phase. As they are exposed to IH inactive phase, it seems there is no surprise in getting circadian rhythm related pathways. What will happen if they do the experiments in active phase? Then also they will find circadian gene effects?

3) The induction of hypoxia might have disturbed the sleep pattern and this could have precipitated the endogenous stress via HPA axis. It is well known that HPA axis is linked with reduction in immune response. So the authors should check these.

Figure 1:

4) Angiogenesis is a kind of compensatory mechanism for hypoxia. Similarly other biological processes mentioned in Figure 1B should have some mechanisms related to hypoxia. This should be explained. Because some biological process like organ development has less meaning.

5) Though they found the alteration in the proportion of different cell types in the lung based on the analysis, this should have been confirmed with the other techniques like flow cytometry. At least a few cell types that have seen gross alteration should have been checked. This is very crucial as most of the story is woven with the type of cells. BAL should have been performed to see the cellular proportions in the airway.

6) Though it is not surprising to see the changes in endothelial cells, the change in myofibroblasts is interesting and this should be explained.

7) It is not clear the downregulated genes in immune cells are due to reduction in cell number? Did they normalize to the number of cells? If cell numbers are reduced, what could be the possible reason? Was there any change in pathways related to apoptosis?

Figure 2:

8) In the context of almost 60% airway epithelial cells are non-ciliated and among these cells clara cells are predominant one and more than 95% of non-ciliated cells are Clara cells. In fact, Clara cells reside throughout the tracheobronchial and bronchiolar epithelium. Surprisingly the authors did not find Clara or Club cells in Figure 2. Also smooth muscle cells have not shown. What could be the reasons behind these? How have these markers been selected to segregate each cell type? How to explain the presence of abundant erythroblasts that are generally observed in bone marrow.

9) While it is known that single cell sequencing has indicated the possible presence of new cell types, it should not ignore the already well known cell types. It is really surprising to see the predominant presence of endothelial cells. This is different from available literature based on single cell sequencing based molecular cell atlas. In general, Sox17, a marker of endoderm, is also expressed by other endoderm derived derivatives like epithelia. (Park et al, Am J Respir Cell Mol Biol. 2006 Feb;34(2):151-7). Please clarify.

10) Amine oxidase C3 is a relatively new marker of myofibroblasts (Hsia et al, Proc Natl Acad Sci U S A. 2016 Apr 12;113(15):E2162-71). But this ectoenzyme is also expressed abundantly in adipocytes, endothelial cells and other cells. Please clarify.

11) It is not clear why the authors have not chosen a well established marker to identify the cells.

12) Figure 3: Top panel, it seems that hypoxia images had shown the lungs seem to be congested with relative thickening of the alveolar wall. This is well evident with HOPX staining in which one can see clear cut higher expression of HOPX in hypoxic mice. Same thing is partially true for Pro-SFTPC as well. All these seem to be a representative picture and so, the morphometry may be required to see the overall status of each marker.

Figure 5:

13) Though it is known that endothelial cells are able to phagocytose cells like red blood cells in conditions like aging, it is not clearly known that alveolar capillary endothelial cells, capillary aerocytes, will have professional phagocytic function in the context of main function in gas exchange. In this context, biological processes derived from softwares could lead to abnormal patterns. Also, how to explain decreased "vasculogenesis" and "regulation of angiogenesis" in capillary general cells while Figure 1B mentioned about increased angiogenesis.

14) In a dynamic environment, these biological processes derived from the altered gene expression without actual demonstrative studies could lead to distortion in biological understanding. This is also evident in Figure 4: Figure supplement 2 where both upregulation and downregulation are observed in Erythroblasts (inflammatory response) and MPhage-DC (apoptotic process related). Similar dual altered pattern is observed in Figure 4.

15) Figure 6: It is worrisome as there is no single validation or demonstrative experiment.

Reviewer #2:

In this study the authors claim that short lasting low intensity ultrasound stimulation activates many neurons in the whole brain. They further claim that the activation mechanism is via the ASIC1a channel. There are some intriguing results in this paper, but there are also many open questions and methodological issues that should be addressed. The authors use pERK as a surrogate for neuronal activation by a global ultrasound stimulus. Some but not all neurons in cortex seem to show activation (it seems only large pyramidal cells, why not interneurons? More analysis needed here.

This experiment is followed by an in vitro experiment with cultured cortical neurons from neonates (no ages given for the animals used in this experiment as far as I can see). These are also not equivalent to the adult cells tested in the in vivo experiment. In the bulk of the experiments calcium imaging is used as a surrogate to measure neuronal activation. Unfortunately, in none of the graphs displayed of the Delta F/Fo is there any indication of the number of cells selected and measured. This is critical to evaluate the robustness of the results. In addition, it is normal at the end of the experiment to permeabilize the neurons to calcium by using an ionophore. This allows the assessment of the maximum fluorescence signal when calcium outside concentration equilibrates with the intracellular concentration. This was not done which means the experiments have no internal calibration.

It is for me impossible to assess the robustness of the calcium imaging experiment when I do not know what each data point corresponds to, take Figure 2I as an example. Are these individual cells or means values from many cells from individual cultures? Many critical methodological details are indeed missing from the paper.

The idea that ASIC1a is THE critical mediator of this effect is quite surprising and the more dramatic and implausible the conclusion may seem, the more solid the evidence needed. The authors should use ASIC1a mutant mice both in vivo and in vitro to prove that ASIC1a really is critical. The same applies to the apparent effect on neurogenesis.

The videos show quite large physical effects of the ultrasound on the cultures (cells moving around). This is problematic as it may be that what the calcium signals are purely indicative of cell damage. Controls should be provided to ensure this was not the case.

Reviewer #2:

This paper explores the effect of all-trans retinoic acid (atRA) on synaptic plasticity in human and murine brain slices. The paper builds on previous work showing that atRA plays a key role in various forms of homeostatic and Hebbian plasticity, but extends our understanding in two very significant ways. First, the work convincingly shows that atRA enhances synaptic function in human layer 2/3 pyramidal neurons in intact cortical slices, and like previous studies using murine models and human ipSCs, this is critically dependent on new protein synthesis. Second, the studies show that atRA-mediated synaptic plasticity requires synaptopodin, a protein that is specifically localized to the spine apparatus.

Overall, the studies have been well-executed and the data are both rigorous and convincing. The paper is very clearly written and the findings are significant. This is a very strong body of work that will be of broad interest.

Comments:

1) While the authors rightly point out in the introduction that no previous studies have assessed atRA effects in human cortical circuits, the Zhang et al. (2018) paper did elegantly show synaptic plasticity effects in human neurons (derived from ipSCs). This is noted in the discussion, but should also be pointed out in the introduction as it bears directly on the rationale for the studies described in the paper.

2) Figure 1C illustrates responses of layer 2/3 pyramidal neurons to intracellular current injection. While the passive membrane properties are quantified and similar regardless of atRA exposure, it is not clear if atRA affects intrinsic excitability of these neurons (i.e., the number of spikes elicited by different levels of injected current). These data should be included.

3) The legend for Figure 1 C-E is too vague and does not describe the specific measures that are shown in the figure.

4) For the mouse studies shown in Figure 3A and 3B, did wild-type littermates serve as controls (the gold standard)? Data from wild-type neurons is described in the text but it is not clear if these were collected from a different cohort of animals or from the WT littermates of the Synpo-deficient mice. Also, the authors should state whether the deficient allele is null.

5) The Synpo-deficient mice have basal sEPSC amplitudes that are noticeably larger than WT mice (as reported in the text). Some discussion of this observation is warranted.

6) The cumulative frequency plots shown throughout the paper show a curious trend where the smallest events appear to be at least 10 pA or larger. This is somewhat atypical, as most studies find a large number of events between 5 and 10 pA (and many lower still). Does this reflect events only larger than 10 pA being included in the analysis? If so, the points to the left of 10 pA should probably be removed from these plots as including them implies that this data range was adequately sampled.

7) The schematic shown in Fig4B refers to early-phase and late-phase LTP, but the recordings appear to be limited to 60 min post-LTP induction (i.e well before the late-phase). These terms should be replaced with the actual times post-LTP induction.

8) The discussion is quite on point, but is rather brief. The paper would benefit from a more detailed discussion of the link between the spine-apparatus and translation-dependent forms of synaptic plasticity.

Reviewer #2:

In this work by Sachella and colleagues, the role of the lateral habenula (LHb) is investigated for its role in fear conditioning during initial encoding and subsequent retrieval in a later setting. This diencephalic nucleus has received a significant amount of attention in the preceding decade after its connectivity and regulation of neuromodulatory systems during learning and motivation was discovered. However, much less is known about its function in fear learning and memory. Building on the findings the authors report in an earlier avoidance setting, the present study deftly employs a series of pharmacological and optogenetic tools to identify the potential time-limited role of LHb in fear memory. Overall, the findings fit well with their previous work, and builds upon these observations by adding in more contemporary genetic tools to parse these aspects of the task. In particular, I was very enthusiastic about the further exploration of LHb in an associatively-learned fear approach; the strategies that have been highly successful in our understanding of amygdalo-hippocampal fear systems here are compelling applied to the LHb which traditionally has been better understood in stress and motivational settings. However, while the studies themselves were carefully conducted, it was not clear that these observations provided a conceptually transformative approach to the understanding of these neurobehavioral processes. Furthermore, some potential limitations in controls and isolation of important circuit function limits the impact of these findings. Specific concerns are numbered below:

1) First, while the optogenetic inhibition of LHb via ArchT selectively during the cue confirms the pharmacological observations in the preceding experiments, the use of that approach did not significantly extend those observations. Other controls such as a neural stimulus (CS-) or equivalently-applied optical inhibition during the inter-trial interval may have provided insights into the selectivity of the manipulation on the stability of the fear memory beyond that observed in the pharmacological approach. Adding to this, it would also have been of value (particularly with the optogenetic approaches where this would be quite straightforward) to explore some of the encoding vs retrieval vs expression distinctions that the LHb may contribute by providing stimulation/inhibition selectively during memory retrieval/expression in the 24h/Day7 test days.

2) The authors comment on the potential circuit-related contributions of LHb to portions of the amygdalo-hippocampal fear system, which would be of tremendous interest, yet without some isolation of these pathways in their approach, the authors are correct that these predictions would be largely speculative.

3) The use of optogenetics in the final study was quite unorthodox and I am not sure I found it entirely convincing as an approach to understand contextual representation via chronic optical stimulation. The utility of optogenetics should ideally derive from its temporal specificity, and as such, non-specific pulses applied throughout the session would take away from that core strength. Indeed, it seems to me that were the authors particularly invested in this chronic stimulatory or inhibitory approach intersecting with a vector-based targeting that DREADDs would likely present a superior option for these populations. Building on my last comment, this approach would also gain value from being able to target selected populations (e.g., hippocampal or DRN projections) via intersectional strategies.

Reviewer #2:

Verhelst et al. used a multishell tractography (b-value: 700/1200/2800) fixel-based analysis, to map white matter lateralisations relevant for language dominance in a sample of left-handed healthy volunteers (n=23 right hemisphere dominant and n=38 left hemisphere dominant as per fMRI word generation task). The authors show "lateralisation" in the anterior corpus callosum as the main white matter difference between their two groups.

While this manuscript is methodologically sound, the lack of novel anatomical, cognitive or clinically-relevant conclusions limits its scope (i.e. the arcuate finding is not novel and the callosal finding is not explained in the context of language dominance). The authors raise several interesting points about the common practice in the field (e.g. calculation of lateralisation index, clinical lesion flipping) and challenge them in this manuscript. But without further in-depth discussion, the current results will not be impactful in the field of clinical-anatomical studies.

Overall, this study is data-driven methodological rather than hypothesis-driven, which leads to a lack of a rationale in the manuscript or a comprehensive embedding in the white matter literature. For example, it has been previously shown that there is no direct linear relationship between the lateralisation of the arcuate fasciculus and handedness or language dominance (e.g. PMID: 32707542, PMID: 32723129, PMID: 29666567, PMID: 27029050, PMID: 29688293 amongst others). The dataset available in this manuscript is of interest, however, and further analysis should be conducted to study the extended white matter network of language in more depth given the ubiquitous findings of alterations mentioned in the results.

How did the authors determine the fixel clusters as designated white matter tracts (such as the arcuate, uncinate, etc)?

The authors praise their fixel-based analysis over the use of previous tensor-based models. Some previous studies have also employed advanced tracking algorithms with varying possibilities to map fibre-specific indices or resolve crossing fibres and their uses have been compared (e.g. PMID: 31106944, PMID: 25682261, PMID: 30113753 amongst others). with the advancement of current algorithms many improvements have been achieved which does not categorically negate previous findings, especially when they were shown to be meaningful for cognitive or clinical applications.

The authors further discuss the "lateralisation" of the forces minor. This terminology I do have an issue with as this is a commissural connection that cannot per se be lateralized. A difference between both hemispheres can, however, possibly be seen in terms of the asymmetry of the callosal projections. This result needs a lot more explanation and warrants an extensive discussion especially in the light of language processes.

Overall, the anatomical descriptions should be clearer. For example, when the authors mention the "anterior part of the arcuate fasciculus" do they mean the anterior segment or any frontal lobe projections of this pathway?

Reviewer #2:

This is a longitudinal aging study of the physiological changes in a specific Drosophila neural circuit that participates in flight and escape responses. To date there have been few examples of longitudinal aging studies looking at the vulnerability or resilience of neurophysiology at the resolution presented in this study. The analyses have revealed different trajectories for individual neural components of the studied behaviors during aging. The study also reveals different sensitivities of neural components to stressors that are known to alter lifespan (temperature, oxidative stress). The study is well-written and the experiments are performed at a high level. A concern is that the study is highly descriptive and provides very little mechanism to explain the differences in the vulnerability or resilience of neural functions observed. In addition, the authors present little evidence other than lifespan to support their interpretation of the effects of the experimental conditions at the cellular level.

Major Critiques:

1) Overall, the study is highly descriptive and there is a lack of experiments aimed at understanding the cellular effects of aging on neural function.

2) There is a lack of supporting data or discussion about the expected cellular mechanisms of the high temperature manipulations or SOD mutants. While it is true that both of these manipulations shorten lifespan, their relationship in the natural process of aging remains controversial. The ability to extend the resilience of the neural components studied by a manipulation that extends lifespan would be very supportive (i.e. diet, insulin signaling mutants).

3) The data from the current study demonstrates that the major effect of SOD mutants on neural function and mortality exists in newly eclosed animals suggesting significant issues during development in SOD mutants. This complicates the comparison of this condition to the other conditions or even considering it a manipulation of aging. The authors should also consider showing that the effects on neural function by SOD mutants is mimicked by other conditions that alter ROS more acutely such as paraquat exposure or test mutations in insulin signaling (i.e. chico) which have been shown to increase antioxidant expression.

4) The authors contend that the changes in neural function, particularly in regards to seizure susceptibility, provide indices for age progression. It is unclear to this author how these neural functions described in this study, including the appearance of seizures, contribute to lifespan of the flies. One could imagine that changes in flight distance or escape response could contribute to lifespan in the wild, but do changes in flight, jump response, or seizure susceptibility have any bearing on the lifespan of flies in vials? Why would seizure susceptibility be predictive of mortality? In addition, the assays presented here utilize experimental conditions (intense whole head stimulation) that are seemingly non-physiological so it is unclear what the declines represent in a normal aging fly. The authors need to discuss this.

5) There are no experiments aimed at understanding the cellular or molecular nature of the functional declines presented.

Stefan Rahmstorf zu den noch zur Verfügung stehenden CO2-Budgets.

Reviewer #2:

The authors show that neonatal LPS (nLPS) treatment is associated with downregulated PFC levels of ATPase phospholipid tranporting8A2 (ATP8A2) that is associated with elevated IFN in serum and PFC and blocked by an IFN blocking antibody. Antibody treatment marginally antagonized effects of nLPS to cause depressive-like behavior, but was ineffective when females alone were examined.

This paper adds to a long list of publications reporting alterations in a number of diverse signaling molecules after nLPS treatment. Strengths are that it is generally well done, with appropriate attention to experimental design (eg litter effects) and statistical treatment. However, while the down regulation of ATP8A2 is indisputable, a major weakness is that there is no functional relationship revealed between this and any subsequent behavioral, anatomical or physiological alterations. While the possible role of IFN in causing the increased depressive-like behavior is of some interest, the data here are not convincing. Furthermore, while other work has reported extensively on sex-specific alterations in behavior after nLPS, the behavioral analysis here ( FST, TST) is rather limited.

1) There is little justification for reverting to the non-alpha corrected LSD test when the Tukey does not show significance.

2) The extensive literature on the effects of nLPS is only superficially reviewed.

3) The direct involvement of ATP8A2 in any behavioral or functional outcomes should be tested.

4) How does IFN cause down regulation of the ATP8A2?

5) Other behavioral alterations should be tested such as open field that are less stressful than FST or TST.

Reviewer #2:

In this study, Mackay and colleagues show that resting calcium levels are increased in axons of neurons derived from YAC128 mice, a Huntington Disease model expressing full-length mutant Huntingtin with 128 CAG-repeats in a yeast artificial chromosome. This increase in baseline calcium signaling is due to continuous leak of calcium from the ER that leads to increased spontaneous neurotransmission and reduced evoked neurotransmission. Overall, the manuscript thoroughly documents a clear example of inverse regulation of spontaneous and evoked glutamate release in a well-established monogenic neurological disease model. Moreover, the authors link this observation of dysregulation of calcium release/leak from presynaptic endoplasmic reticulum. I have some relatively minor comments that may help improve this work.

1) While the authors nicely document and interrogate the relationship between resting axonal calcium signals and spontaneous release, the impact of dysfunctional ER calcium signaling on evoked release is not causally linked. For instance, it would be nice to show that buffering excess baseline calcium (EGTA-AM?) can equilibrate the difference in evoked release phenotype between wild type and YAC128 neurons.

2) Figure 7: The authors state that evoked glutamate release is reduced in YAC128 neurons, can they show this? i.e. a bar graph with the absolute values of iGluSnFR amplitudes.

3) Minor: Figure panels are labeled with small letters in the figures but with capital letters in the main text.

Reviewer #2:

In this study, Deng and colleagues have sought to assess the neural correlates of individual differences in responsiveness variability across wakefulness and moderate levels of propofol-induced anaesthesia. In addition to resting state scanning and an auditory story task, the participants underwent behavioural assessments including memory recall and a target detection task. Furthermore, the auditory story task was independently rated by a separate group for its "suspensefulness". Focusing their analysis on three major large-scale brain networks, the group-level results first indicated significant differences in the between network interactions of the chosen networks across wakefulness and sedation, specifically in the narrative condition. Furthermore, during the same condition, there was reduced cross-subject correlation between wakefulness versus sedation centred mainly on the sensorimotor brain regions. Moreover, based on the responses in the target detection task, the participants were grouped into fast and slow responders which then showed significant differences in gray matter volume as well as connectivity differences in the wakeful auditory story task condition within the executive control network.

Overall, this is a well-written manuscript. However, my initial enthusiasm about the question of interest was hampered by major theoretical and methodological concerns related to this study. Below I outline these points in the hopes that they improve this study and its outcomes.

First and foremost, the authors state that their major interest in this study was to assess individual differences in sedation-induced response variability and its potential brain bases. Despite the attractiveness of this topic, which is undoubtedly of interest both to the academic community and the general public, I do not believe that the current study design would allow the authors to answer this question. First of all, although I completely appreciate the difficulty in recruiting participants to take part in such pharmacological studies, I do not think that a group of 17 participants is enough to be able to assess "individual differences". For this to work, there has to be a large enough sample based on adequate power calculations, keeping in mind all the spurious false positive effects that are generated by pharmacological interventions and their downstream effects on connectivity estimates (e.g. motion, global signal etc.). Second, though it is perfectly valid to carry out the initial within-group connectivity and whole-brain activity analyses for the task/rest (which I believe are the only statistically and experimentally sound sections), following these results, the authors mainly carry out multiple exploratory analyses that aim to infer what happened to 3 non-respondent participants (or 6 slow responders). This to me is closer to a case study rather than an experimental study with proper statistics. Overall this fast/slow responder split only comes as an afterthought and does not seem to be the main intention behind the study. This is at odds with the major goal stated in the introduction that the main aim of the authors was to assess inter-individual differences. As such, I do not think that the analyses highlighted by the authors provide enough evidence to support their claims. More detailed points are provided below:

• The introduction is well-written, citing as much of the relevant literature on this topic as possible. Having said that, I am not really convinced about the justification for selecting the dorsal attention, executive control and default mode networks as the sole focus of the authors' analysis. Although it is true that there is a strong a priori basis that these associative networks play an important role in maintaining consciousness, the references that the authors refer to are equally biased in focusing their analyses on specific higher-order networks, creating a circular argument. In light of evidence highlighting the importance of sensorimotor networks in this context, as well as the balance in their interactions with associative cortices, I would argue that a whole-brain approach would be better suited. Furthermore, as indicated by the whole-brain analysis during the auditory story task, most alterations were centered on the primary somatosensory regions. This is at odds with the justification of the authors on focusing their connectivity analyses solely on associative brain networks.

• Given the wide age range (and its potential influence on the obtained results), it would be great for the authors to provide the mean and standard deviation of age within groups, and whether the groups were age-matched (though the range seems similar).

• The authors state that only the reaction time was measured in the auditory target detection task, but later in the results section they mention "omissions". Given that such omissions might be strongly indicative of unresponsiveness/sleep, it is unclear how one can interpret the observed brain-based effects solely from the perspective of reduced information processing (especially when the data was collected under eyes-closed conditions).

• The authors provide a thorough description of the sedation administration procedures, which is excellent. Nevertheless, I was wondering whether the blood plasma propofol concentrations could be used to explain some of the results in individual differences or even a nuisance regressor to show that the effects were not simply driven by this factor.

• I failed to find any information in the methods section as to why/how the authors have decided on a mean-split of the participants to fast/slow responders. Given the already small sample size, further reducing degrees of freedom by a split of 11 versus 6 participants makes it very problematic in terms of any statistical tests that can be carried out.

• Line 441 - Results should not be reported if it did not reach statistical significance.

• Line 448 - For the two analyses on this page the authors indicate that although in the wakefulness condition there were significant brain activity that correlated with (not "predicted") task stimulus, no significant effects were observed in the sedation condition. This absence of evidence should not be then taken as evidence of absence. In other words, such lack of evidence can be explained by a variety of factors not attributable to the effect of sedation on brain activity (e.g. simply by the fact that the participants were not paying attention to the story or falling asleep).

• Line 484 - I do not think it is acceptable/justifiable to carry out post-doc tests, when there was no significant difference in the main ANOVA.

• Line 503 - I am not really sure about the justification behind the assessment of gray matter volume. Besides the issues related to small sample size, the observed differences in functional connectivity may then simply be due to differences in the quality of the data that can be extracted from the defined ROIs in a subset of participants. Was this analysis corrected for age (as a continuous variable)? In any case, as far as I am aware, there is no simple relationship between gray matter volume and functional connectivity (i.e. greater/smaller gray matter volume does not necessarily mean greater/smaller functional connectivity). Hence, once cannot make the conclusion that: "These results lend support to the functional connectivity results above, and together they strongly suggest that connectivity within the ECN, and especially the frontal aspect of this network, underlies individual differences in behavioural responsiveness under moderate anaesthesia."

• Line 509 - Again, I am not really sure about the justification behind the analysis carried out here. The authors state that the ROIs that were found in the gray matter volume analysis overlapped with a priori ROIs which they suggest explain differences observed in functional connectivity. They then select a subset of these ROIs and again show that there are differences in connectivity. This seems rather circular.

• The authors state that "Rather, only the functional connectivity within the ECN during the wakeful narrative condition differentiated the participants' responsiveness level, with significantly stronger ECN connectivity in the fast, relative to slow responders." I apologise if I am missing something, but I do not see any evidence for such a strong claim. All that the authors have found was that there were significant functional connectivity differences in the executive control network in the wakefulness condition between fast and slow responders (which was defined and grouped by the authors themselves), with no significant effect of condition or state. I fail to understand why this one result from a multitude of exploratory analyses that were conducted was picked out as the "main finding" when one cannot make any inferences about its direct relation to sedation.

• Overall, I would urge the authors to re-think their analysis strategy and the corresponding discussion of their results.

Reviewer #2:

This paper contributes to the large number of papers currently posted on BioRxiv showing that the N protein of SARS CoV2 can undergo liquid-liquid phase separation on its own and in the presence of RNA, and that this behavior can be modulated by phosphorylation. The work here is somewhat different from much of the other work in that the authors have generated the N protein from mammalian cells. The authors have also examined the effects of known drugs on the phase separation process. Given the importance of coronavirus it is imperative to get out information on its biology. But it is also imperative that the information be correct, interpreted with appropriate caution, and of sufficient depth to be valuable to others in the field and not potentially misdirect future research and clinical efforts. In this respect, I think the authors need to clean up some of their experiments and pull back on some of their claims, as I detail below.

Major comments:

1) In general, the authors' use of size, number and morphology of droplets to assess the effects of small molecules in figure 4 is problematic. The authors should be measuring the effects of the compounds on the phase separation threshold concentration (of N+RNA or of salt) to see whether the compounds stabilize or destabilize the droplets. Changes in size, number and morphology can be due to many factors, many of which are unlikely to be relevant to viral assembly.

For example, the authors report that nelfinavir mesylate and LDK378 produced fewer but larger droplets, and conclude that these compounds could disrupt virion assembly. This is problematic for two reasons. Most importantly, it is almost impossible to interpret what fewer larger droplets means. Are they nucleating more slowly and/or growing more rapidly? Are they more viscous and thus less disrupted by handling? Are they denser and thus settling more rapidly? Has the thermodynamic threshold to phase separation changed? Secondarily, because of these uncertainties, it is an overinterpretation to state based on the data that these compounds could act by disrupting virion assembly.

The class II molecules, which increase both size and number of droplets, are probably more relevant, since concomitant increases in both probably mean that the threshold concentration for LLPS has decreased, and thus the compound has stabilized the droplets.

The changes in morphology induced by the class III molecules are also hard to interpret. Does the change reflect greater adhesion to and spreading on the slide surface (probably irrelevant to drug action)? Or changes in droplet dynamics--slowed fusion or increased viscosity? What does it mean that nilotinib causes the morphology of N+RNA condensates to become filamentous, and could this same effect account for the (modest) decrease in N protein foci in cells upon drug treatment?<br> I honestly am concerned that the authors conclude the paper urging use of nilotinib in clinical trials, and the effects of drugs on phase separation as a proxy for vRNP formation, based on these very thin data.

2) In Figure 1 (and beyond), it is not good practice to use fractional areas of droplets that have settled to a slide surface to quantify droplet formation in LLPS experiments. Droplets fall to the slide surface at different rates depending on their sizes, which in turn depend on many factors, some biochemical (the relative rates of nucleation and growth; density; all of which can vary with buffer conditions) and some technical (exactly how the sample was handled). Turbidity, which also is imperfect, is nevertheless a more reliable measure; so is microscopic assessment of the presence or absence of droplets. The authors should provide at least some additional measure in these initial experiments to show the numbers obtained from the fractional area are qualitatively correct.

3) In figure 1C, the dissolution with salt is not a measure of liquid-like properties, as claimed at the bottom of page 3. The authors should look for evidence of droplet fusion, spherical shape (for droplets larger than the diffraction limit) and rapid exchange with solvent.

4) The claims on page 4 that the condensates formed with viral RNA fragments are gel-like should be supported with some measure of dynamics, and not simply the shape of the objects that settle to the slide surface.

5) In the CLMS experiments, how do the authors know that the changes observed are due to LLPS per se and not to differences in structure induced by differences in salt? It seems like additional controls are warranted to make this claim. Relatedly, the authors should state/examine whether higher salt affects dimerization of the dimerization domain.

6) The analogy made on page 4 between the asymmetric structures observed upon mixing N and viral RNA fragments to the strings of vRNPs observed by cryoEM is quite a stretch. The vRNPs are 15 nm in diameter. The structures observed here are vastly larger. Such associated but non-fused droplets are often observed for solidifying phase separating systems. The superficial similarity of connected particles between the cellular vRNPs and the structures here is, in my opinion, unlikely to be meaningful.

Reviewer #2:

In the manuscript by Gore et al., the authors show evidence that MMP9 is a key regulator of synaptic and neuronal plasticity in Xenopus tadpoles. Importantly, they demonstrate a role for MMP9s in valproic acid-induced disruptions in development of synaptic connectivity, a finding that may have particular relevance to autism spectrum disorder (ASD), as prenatal exposure to VPA leads to a higher risk for the disorder. Specifically, the authors show that hyper-connectivity induced by VPA is mimicked by overexpression of MMP9 and reduced by MMP9 knockdown and pharmacological inhibition, suggesting a causal link. The experiments appear to be well executed, analyzed appropriately, and are beautifully presented. I have only a few suggestions for improvement of the manuscript and list a few points of clarification that the authors should address.

1) The authors refer to microarray data as the rationale for pursuing the role for MMP9 in VPA-induced hyperconnectivity. How many other MMPs or proteases with documented roles in development are similarly upregulated? The authors should say how other possible candidate genes did or did not change, perhaps presenting the list with data in a table (at least other MMPs and proteases). If others have changed, the authors should discuss their data in that context.

2) Please cite the microarray study(ies?).

3) In a related issue, the authors should comment on the specificity of the SB-3CT, particularly with regard to other MMPs or proteases that may/may not have been found to be upregulated in the microarray experiment.

4) Results, first paragraph: although it is in the methods, please state briefly the timing of the VPA exposure and the age/stage at which the experiments were performed. Within the methods, please give an approximate age in days after hatching for the non-tadpole experts.

5) The finding that a small number of MMP9 overexpressing cells is fascinating. Have the authors stained the tissue for MMP9 after VPA? 6) Do the authors have data on the intrinsic cell properties (input resistance, capacitance, etc.)? If so, they should include that data either in Supplemental information or in the text. These factors could absolutely influence hyperconnectivity or measurements of the synaptic properties, so at least the authors should discuss their findings in the context of the findings of James, et al.

Minor Comments:

1) Page 15: 'basaly low' may be better worded as 'low at baseline'.

2) The color-coding is very useful and facilitates communicating the results. The yellow on Figure 5, however, is really too light. Consider another color.

Reviewer #2:

Lang et al. Investigate and document the role of myeloid-endogenous circadian cycling on the host response to and progression of endotoxemia in the mouse LPS-model. As a principal finding, Lang et al. report how disruption of the cell-intrinsic myeloid circadian clock by myeloid-specific knockdown of either CLOCK or BMAL1 does not prevent circadian patterns of morbidity and mortality in endotoxemic mice. As a consequence of these and other findings from endotoxemia experiments in mice kept in the dark or the observation of circadian cytokine production in CLOCK KO animals, the authors conclude that myeloid responses critical to endotoxemia are not governed by their local cell-intrinsic clock. Moreover they conclude that the source of circadian timing and pace giving that is critical for the host response to endotoxemia must lie outside the myeloid compartment. Finally, the authors also report a general (non-circadian) reduced susceptibility of mice devoid of myeloid CLOCK or BMAL1, which they take as proof that myeloid circadian cycling is important in the host response to endotoxemia, yet does not dictate the circadian pattern in mortality and cytokine responses.

The paper is well conceived, experiments are very elegant and well carried out, statistics are appropriate, ethic statements are OK. The conclusions of this study, as summarized above, are important and will be of much interest to readers from the circadian field and beyond, also to sepsis and inflammation researchers. To me, there is one major flaw in the argumentative line of this story, as the study relies on the assumption that the systemic cytokine response provided by myeloid cells is paramount and central to the course and intensity of endotoxemia. While this is assumed by many, a rigorous proof of this connection and its causality is still lacking (most evidence is of correlative nature). As a matter of fact, there is an increasing body of more recent experimental evidence that argues against a prominent role of myeloid cells in the cytokine storm. Overall I would like to raise the following points and suggestions.

Major Points:

• As mentioned, a weakness of this paper is that it assumes systemic cytokine levels as produced by myeloid cells are center stage in endotoxemic shock (e.g. see line 164). However, recent evidence has shown that over 90 % of most of systemically released cytokines in sepsis are produced by non-myeloid cells (as proven e.g. by use of humanized mice, which allows to discriminate (human) cytokines produced by blood cells from (murine) cytokines produced by parenchyma (see e.g. PMID: 31297113). (Interestingly, there is one major exception to that rule, and that is TNFa). Considering this, it is not surprising that circadian cytokine levels do not change in myeloid CLOCK/BMAl1 KO mice. Also, assuming that myeloid-produced cytokines are not critical drivers, the same applies to the observation that circadian mortality pattern is preserved in those mice. I recommend that the authors more critically discuss this alternative explanation in the paper. In fact, this line of arguing would be in line with the concept that the source for the circadian susceptibility /mortality in endotoxemia resides in a non-myeloid cell compartment, which is essentially the major finding of this manuscript.

• Intro (lines 51-54): the authors describe one scenario as the mechanism of sepsis-associated organ failure. This appears too one-sided and absolute to me, many more hypotheses and models exist. It would be good to mention that and/or tone down the wording.

• Very analogous to Light/Darkness cycles, ambient temperature has been shown to have a strong impact on mortality from endotoxemia (e.g. PMID: 31016449). Did the authors keep their animals in thermostated ambient conditions? Please describe and discuss in the text.

• Fig.2C; The large difference in mortality in the control lys-MCre line looks somewhat worrying to me. Could this be a consequence of well-known Cre off-target activities? Did the authors check this by e.g. sequencing myeloid cells of or using control mouse strains?

• Line 320: Bmal1flox/flox (Bmal-flox) [48] or Clockflox/flox (Clock-flox) [38] were bred with LysM-Cre to target Bmal1. I suggest showing a prototypical genotyping result, perhaps as a supplemental figure.

• Line 365: the authors state that mice that did not show signs of disease were sorted out. What proportion of mice (%) did not react to LPS? It would be useful to state this number in the methods section.

• It is not fully clear to me if male or female or both were used for the principal experiments, please specify. If females were used, please describe how menstruation cycle was taken into account.

Reviewer #2:

General assessment:

The study investigated transient coupling between EEG and fMRI during resting state in 15 elderly participants using the previously established Hidden Markov Model approach. Key findings include: 1) deviations of the hemodynamic response function (HDR) in higher-order versus sensory brain networks, 2) Power law scaling for duration and relative frequency of states, 3) associations between state duration and HDR alterations, 4) cross-sectional associations between HDR alterations, white matter signal anomalies and memory performance.

The work is rigorously designed and very well presented. The findings are potentially of strong significance to several neuroscience communities.

Major concerns:

My enthusiasm was only somewhat mitigated by methodological issues related to the sample size for cross-sectional reference and missed opportunities for more specific analysis of the EEG.

1) Statistical power analysis has been conducted prior to data collection, which is very laudable. Nevertheless, n=15 is a very small sample for cross-sectional inference and commonly leads to false positives despite large observed effect sizes and small p-values (it takes easily up to 200 samples to detect true zero correlations). On the other hand, the within-subject results are far more well-posed from a statistical view, hence, more strongly supported by the data.

Recommendations:

• The issue should be non-defensively addressed in a well-identified section or paragraph inside the discussion. The sample size should be mentioned in the abstract too.

• The authors could put more emphasis on the participants as replication units for observations. For the theoretical perspective, the work by Smith and Little may be of help here: https://link.springer.com/article/10.3758/s13423-018-1451-8. In terms of methods, more emphasis should be put on demonstrating representativeness for example using prevalence statistics (see e.g. Donnhäuser, Florin & Baillet https://doi.org/10.1371/journal.pcbi.1005990)

• Supplements should display the most important findings for each subject to reveal representatives of the group averages.

• For state duration analysis (boxplots) linear mixed effect models (varying slope models) may be an interesting option to inject additional uncertainty into the estimates and allow for partial pooling through shrinkage of subject-level effects.

• Show more raw signals / topographies to build some trust for the input data. It could be worthwhile to show topographic displays for the main states reported in characteristic frequencies. See also next concern.

2) The authors seem to have missed an important opportunity to pinpoint the characteristic drivers in terms of EEG frequency bands. The current analysis is based on broadband signals between 4 and 30 Hz, which seems untypical and reduces the specificity of the analysis. Analyzing the spectral drivers of the different state would not only enrich the results in terms of EEG but also provide a more nuanced interpretation. Are the VisN and DAN-states potentially related to changes in alpha power, potentially induced by spontaneous opening and closing of the eyes? What is the most characteristic spectral of the DMN state? ... etc.

Recommendations:

• Display the power spectrum indexed by state, ideally for each subject. This would allow inspecting modulation of the power spectra by the state and reveal the characteristic spectral signature without re-analysis.

• Repeat essential analyses after bandpass filtering in alpha or beta range. For example, if main results look very similar after filtering 8-12 one can conclude that most observations are related to alpha band power.

• While artifacts have been removed using ICA and the network states do not look like source-localized EOG artifacts, some of the spectral changes e.g. in DAN/VisN might be attributed to transient visual deprivation. This could be investigated by performing control analysis regressing the EOG-channels amplitudes against the HMM states. These results could also enhance the discussion regarding activation/deactivation.

Reviewer #2:

In this paper, Fiscella and colleagues report the results of behavioral experiments on auditory perception in healthy participants. The paper is clearly written, and the stimulus manipulations are well thought out and executed.

In the first experiment, audiovisual speech perception was examined in 15 participants. Participants identified keywords in English sentences while viewing faces that were either dynamic or still, and either upright or rotated. To make the task more difficult, two irrelevant masking streams (one audiobook with a male talker, one audiobook with a female talker) were added to the auditory speech at different signal-to-noise ratios for a total of three simultaneous speech streams.

The results of the first experiment were that both the visual face and the auditory voice influenced accuracy. Seeing the moving face of the talker resulted in higher accuracy than a static face, while seeing an upright moving face was better than a 90-degree rotated face which was better than an inverted moving face. In the auditory domain, performance was better when the masking streams were less loud.

In the second experiment, 23 participants identified pitch modulations in auditory speech. The task of the participants was considerably more complicated than in the first experiment. First, participants had to learn an association between visual faces and auditory voices. Then, on each trial, they were presented with a static face which cued them which auditory voice to attend to. Then, both target and distracter voices were presented, and participants searched for pitch modulations only in the target voice. At the same time, audiobook masking streams were presented, for a total of 4 simultaneous speech streams. In addition, participants were assigned a visual task, consisting of searching for a pink dot on the mouth of the visually-presented face. The visual face matched either the target voice or the distracter voice, and the face was either upright or inverted.

The results of the second experiment was that participants were somewhat more accurate (7%) at identifying pitch modulations when the visual face matched the target voice than when it did not.

As I understand it, the main claim of the manuscript is as follows: For sentence comprehension in Experiment 1, both face matching (measured as the contrast of dynamic face vs. static face) and face rotation were influential. For pitch modulation in Experiment 2, only face matching (measured as the contrast of target-stream vs. distracter-stream face) was influential. This claim is summarized in the abstract as "Although we replicated previous findings that temporal coherence induces binding, there was no evidence for a role of linguistic cues in binding. Our results suggest that temporal cues improve speech processing through binding and linguistic cues benefit listeners through late integration."

The claim for Experiment 2 is that face rotation was not influential. However, the authors provide no evidence to support this assertion, other than visual inspection (page 15, line 235): "However, there was no difference in the benefit due to the target face between the upright and inverted condition, and therefore no benefit of the upright face (Figure 2C)."

In fact, the data provided suggests that the opposite may be true, as the improvement for upright faces (t=6.6) was larger than the improvement for inverted faces (t=3.9). An appropriate analysis to test this assertion would be to construct a linear mixed-effects model with fixed factors of face inversion and face matching, and then examine the interaction between these factors.

However, even if this analysis was conducted and the interaction was non-significant, that would not necessarily be strong support for the claim. As the canard has it, "absence of evidence is not evidence of absence". The problem here is that the effect is rather small (7% for face matching). Trying to find significant differences of face inversion within the range of the 7% effect of face matching is difficult but would likely be possible given a larger sample size, assuming that the effect size found with the current sample size holds (t = 6.6 vs. t = 3.9).

In contrast, in experiment 1, the range is very large (improvement from ~40% for the static face to ~90% for dynamic face) making it much easier to find a significant effect of inversion.

One null model would be to assume that the proportional difference in accuracy due to inversion is similar for speech perception and pitch modulation (within the face matching effect) and predict the difference. In experiment 1, inverting the face at 0 dB reduced accuracy from ~90% to ~80%, a ~10% decrease. Applying this to the 7% range found in Experiment 2 would predict that inverted accuracy would be ~6.3% vs. 7%. The authors could perform a power calculation to determine the necessary sample size to detect an effect of this magnitude.

Other Comments

When reporting the effects of linear effects models or other regression models, it is important to report the magnitude of the effect, measured as the actual values of the model coefficients. This allows readers to understand the relative amplitude of different factors on a common scale. For experiment 1, the only values provided are imputed statistical significance, which are not good measures of effect size.

The duration of the pitch modulations in Experiment 2 are not clear. It would help the reader to provide a supplemental figure showing the speech envelope of the 4 simultaneous speech streams and the location and duration of the pitch modulations in the target and distracter streams.

If the pitch modulations were brief, it should be possible to calculate reaction time as an additional dependent measure. If the pitch modulations in the target and distracter streams occurred at different times, this would also allow more accurate categorization of the responses as correct or incorrect by creation of a response window. For instance, if a pitch modulation occurred in both streams and the participant responded "yes", then the timing of the pitch modulation and the response could dissociate a false-positive to the distractor stream pitch modulation from the target stream pitch modulation.

It is not clear from the Methods, but it seems that the results shown are only for trials in which a single distracter was presented in the target stream. A standard analysis would be to use signal detection theory to examine response patterns across all of the different conditions.

In selective attention experiments, the stimulus is usually identical between conditions while only the task instructions vary. The stimulus and task are both different between experiments 1 and 2, making it difficult to claim that "linguistic" vs. "temporal" is the only difference between the experiments.

At a more conceptual level, it seems problematic to assume that inverting the face dissociates linguistic from temporal processing. For instance, a computer face recognition algorithm whose only job was to measure the timing of mouth movements (temporal processing) might operate by first identifying the face using eye-nose-mouth in vertical order. Inverting the face would disrupt the algorithm and hence "temporal processing", invalidation the assumption that face inversion is a pure manipulation of "linguistic processing".

Reviewer #2:

This paper reports on a very interesting and potentially highly important finding - that so-called "sleep learning" does not improve relearning of the same material during wake, but instead paradoxically hinders it. The effect of stimulus presentation during sleep on re-learning was modulated by sleep physiology, namely the number of slow wave peaks that coincide with presentation of the second word in a word pair over repeated presentations. These findings are of theoretical significance for the field of sleep and memory consolidation, as well as of practical importance.

Concerns and recommendations:

1) The authors' results suggest that "sleep learning" leads to an impairment in subsequent wake learning. The authors suggest that this result is due to stimulus-driven interference in synaptic downscaling in hippocampal and language-related networks engaged in the learning of semantic associations, which then leads to saturation of the involved neurons and impairment of subsequent learning. Although at first the findings seem counter-intuitive, I find this explanation to be extremely interesting. Given this explanation, it would be interesting to look at the relationship between implicit learning (as measured on the size judgment task) and subsequent explicit wake-relearning. If this proposed mechanism is correct, then at the trial level one would expect that trials with better evidence of implicit learning (i.e. those that were judged "correctly" on the size judgment task) should show poorer explicit relearning and recall. This analysis would make an interesting addition to the paper, and could possibly strengthen the authors' interpretation.

2) In some cases, a null result is reported and a claim is based on the null result (for example, the finding that wake-learning of new semantic associations in the incongruent condition was not diminished). Where relevant, it would be a good idea to report Bayes factors to quantify evidence for the null.

3) The authors report that they "further identified and excluded from all data analyses the two most consistently small-rated and the two most consistently large-rated foreign words in each word lists based on participants' ratings of these words in the baseline condition in the implicit memory test." Although I realize that the same approach was applied in their original 2019 paper, this decision point seems a bit arbitrary, particularly in the context of the current study where the focus is on explicit relearning and recall, rather than implicit size judgments. As a reader, I wonder whether the results hold when all words are included in the analysis.

4) In the main analysis examining interactions between test run, condition (congruent/incongruent) and number of peak-associated stimulations during sleep (0-1 versus 3-4), baseline trials (i.e. new words that were not presented during sleep) are excluded. As such, the interactions shown in the main results figure (Figure D) are a bit misleading and confusing, as they appear to reflect comparisons relative to the baseline trials (rather than a direct comparison between congruent and incongruent trials, as was done in the analysis). It also looks like the data in the "new" condition is just replicated four times over the four panes of the figure. I recommend reconstructing the figure so that a direct visual comparison can be made between the number of peaks within the congruent and incongruent trials. This change would allow the figure to more accurately reflect the statistical analyses and results that are reported in the manuscript.

5) In addition to the main analysis, the authors report that they also separately compared the conscious recall of congruent and incongruent pairs that were never or once vs. repeatedly associated with slow-wave peaks with the conscious recall in the baseline condition. Given that four separate analyses were carried out, some correction for multiple comparisons should be done. It is unclear whether this was done as it does not seem to be reported.

Reviewer #2:

This paper uses a clever application of the well known Simultaneous Localization and Mapping model (+ replay) to the neuroscience of navigation. The authors capture aspects of the relationship between EC-HPC that are often not captured within one paper/model. Here online prediction error between the EC/HPC systems in the model trigger offline probabilistic inference, or the fast propagation of traveling waves enabling neural message passing between place and grid cell representing non-local states. The authors thus model how such replay - i.e. fast propagation of offline traveling waves passing messages between EC/HP - leads to inference and explains the function of coordinated EC-HP replay. I enjoyed reading the paper and the supplementary material.

First, I'd like to say that I am impressed by this paper. Second, I see my job as a reviewer merely to give suggestions to help improve the accessibility and clarity of the present manuscript. This could help the reader appreciate a beautiful application of SLAM to HPC-EC interactions as well as the novelty of the present approach in bringing in a number of HPC-EC properties together in one model.

1) The introduction is rather brief and lacks citations standard for this field. This is understandable as it may be due to earlier versions having been prepared for NeurIPS. It may be helpful if the authors added a bit more background to the introduction so readers can orient themselves and localize this paper in the larger map of the field. It would be especially helpful to repeat this process not only in the intro but throughout the text even if the authors have already cited papers elsewhere, since the authors are elegantly bringing together various different neuroscientific concepts and findings, such as replay, structures, offline traveling waves, propagation speed, shifter cell, etc. A bigger picture intro will help the reader be prepared for all the relevant pieces that are later gradually unfolded.

It would be especially helpful to offer an overall summary of the main aspects of HPC-EC literature in relation to navigation that will later appear. This will frontload the larger, and in my opinion clever narrative, of the paper where replay, memory, and probabilistic models meet to capture aspects of the literature not previously addressed.

2) The SLAM (simultaneous localization and mapping) model is used broadly in mobile phones, robotics, automotive, and drones. The authors do not introduce SLAM to the reader, and SLAM (in broad strokes) may not be familiar to potential readers. Even for neuroscientists who may be familiar with SLAM, it may not be clear from the paper which aspects of it are directly similar to existing other models and which aspects are novel in terms of capturing HPC/EC findings. I would strongly encourage an entire section dedicated to SLAM, perhaps even a simple figure or diagram of the broader algorithm. It would be especially helpful if the authors could clarify how their structure replay approach extends existing offline SLAM approaches. This would make the novel approaches in the present paper shine for both bio & ML audiences.

Providing this big picture will make it easier for the reader to connect aspects of SLAM that are known, with the clever account of traveling waves and other HPC-EC interactions, which are largely overlooked in contemporary models of HPC-EC models of space and structures. It is perhaps also worth to mention RatSLAM, which is another bio-inspired version of SLAM, and the place cell/hippocampus inspiration for SLAM.

D Ball, S Heath, J Wiles, G Wyeth, P Corke, M Milford, "OpenRatSLAM: an open source brain-based SLAM system", in Autonomous Robots, 34 (3), 149-176, 2013

3) At first glance, it may appear that there are many moving parts in the paper. To the average neuroscience reader, this may be puzzling, or require going back and forth with some working memory overload to put the pieces together. My suggestion is to have a table of biological/neural functions and the equivalent components of the present model. This guide will allow the reader to see the big picture - and the value of the authors' hard work - in one glance, and be able to look more closely at each section more closely and with the bigger picture in mind. I believe this will only increase the clarity and accessibility of the manuscript.

4) The authors could perhaps spend a little more time comparing previous modeling attempts at capturing the HP-EC phenomena and traveling through various models, noting caveats of previous models, and advantages and caveats of their model. This could be in the discussion, or earlier, but would help localize the reader in this space a bit better.

5) Perhaps the authors could briefly clarify where merely Euclidean vs. non-euclidean representations would be expected of the model, and whether they can accommodate >2D maps, e.g. in bats or in nonspatial interactions of HPC-EC.

6) The discussion could also be improved by synthesizing the old and the new, the significant contribution of this paper and modifications to SLAM, as well as a big picture summary of the various phenomena that come together in the HPC-EC interactions, e.g. via traveling waves.

Reviewer #2:

The authors present a work related to the survey of the bacterial community in the Cam River (Cambridgeshire, UK) using one of the latest DNA sequencing technologies using a target sequencing approach (Oxford Nanopore). The work consisted in a test for the sequencing and analysis method, benchmarking some programs using mock data, to decide which one was the best for their analysis.

After selecting the best tool, they provide a family level taxonomy profiling for the microbial community along the Cam river through a 4-month window of time. In addition to the general and local snapshots of the bacterial composition, they correlate some physicochemical parameters with the abundance shift of some taxa.

Finally, they report the presence of 55 potentially pathogenic bacterial genera that were further studied using a phylogenetic analysis.

Comments:

Page 6. There is a "data not shown" comment in the text:

"Benchmarking of the classification tools on one aquatic sample further confirmed Minimap2's reliable performance in a complex bacterial community, although other tools such as SPINGO (Allard, Ryan, Jeffery, & Claesson, 2015), MAPseq (Matias Rodrigues, Schmidt, Tackmann, & von Mering, 2017), or IDTAXA (Murali et al., 2018) also produced highly concordant results despite variations in speed and memory usage (data not shown)."

Nowadays, there is no reason for not showing data. In case the speed and memory usage was not recorded, it is advisable to rerun the analysis and quantify these variables, rather than mentioning them and not report them.

Or what are the reasons for not showing the results?

Figure 2 is too dense and crowded. In the end, all figures are too tiny and the message they should deliver is lost. That also makes the footnote very long. I would suggest moving some of the figure panels, maybe b), c) and d), as separate supp. figures.

Figure 3 has the same problem. I think there is too much information that could be moved as supp. mat.

In addition to Figure 4, it would be important to calculate if the family PCA component contribution differences in time are differentially significant. In Panel B, is depicted the most evident variance difference but what about other taxa which might not be very abundant but differ in time? you can use the fitFeatureModel function from the metagenomeSeq R library and a P-adjusted threshold value of 0.05, to validate abundance differences in addition to your analysis.

Page 12-13. In the paragraph:

"Using multiple sequence alignments between nanopore reads and pathogenic species references, we further resolved the phylogenies of three common potentially pathogenic genera occurring in our river samples, Legionella, Salmonella and Pseudomonas (Figure 7a-c; Material and Methods). While Legionella and Salmonella diversities presented negligible levels of known harmful species, a cluster of reads in downstream sections indicated a low abundance of the opportunistic, environmental pathogen Pseudomonas aeruginosa (Figure 7c). We also found significant variations in relative abundances of the Leptospira genus, which was recently described to be enriched in wastewater effluents in Germany (Numberger et al., 2019) (Figure 7d)."

Here it is important to mention the relative abundance in the sample. Please, discuss that the presence of DNA from pathogens in the sample, has to be confirmed by other microbiology methodologies, to validate if there are viable organisms. Definitively, it is a big warning finding pathogen's DNA but also, since it is characterized only at genus level, further investigation using whole metagenome shotgun sequencing or isolation, would be important.

This phrase is used in the abstract , introduction and discussion, although not exactly written the same:

"Using an inexpensive, easily adaptable and scalable framework based on nanopore sequencing..."

I wouldn't use the term "inexpensive" since it is relative. Also, it should be discussed that although is technically convenient in some aspects compared to other sequencers, there are still protocol steps that need certain reagents and equipment that are similar or the same to those needed for other sequencing platforms. Probably, common bottlenecks such as DNA extraction methods, sample preservation and the presence of inhibitory compounds should be mentioned and stressed out.

Page 15: "This might help to establish this family as an indicator for bacterial community shifts along with water temperature fluctuations."

Temperature might not be the main factor for the shift. There could be other factors that were not measured that could contribute to this shift. There are several parameters that are not measured and are related to water quality (COD, organic matter, PO4, etc).

"A number of experimental intricacies should be addressed towards future nanopore freshwater sequencing studies with our approach, mostly by scrutinising water DNA extraction yields, PCR biases and molar imbalances in barcode multiplexing (Figure 3a; Supplementary Figure 5)."

Here you could elaborate more on the challenges like those mentioned in my previous comment.

Reviewer #2:

In this work Chatzikalymniou et al. use models of hippocampus of different complexities to understand the emergence and robustness of intra-hippocampal theta rhythms. They use a segment of highly detailed model as a bridge to leverage insights from a minimal model of spiking point neurons to the level of a full hippocampus. This is an interesting approach as the minimal model is more amenable to analysis and probing the parameter space while the detailed model is potentially closer to experiment yet difficult and costly to explore.

The study of network problems is very demanding, there are no good ways to address robustness of the realistic models and the parameter space makes brute force approaches impractical. The angle of attack proposed here is interesting. While this is surely not the only approach tenable, it is sensible, justified, and actually implemented. The amount of work which entered this project is clear. I essentially accept the proposed reasoning and the hypotheses put forward. The few remarks I have are rather minor, but I think they merit a response.

1) l. 528-530 "This is particularly noticeable in Figure 9D where theta rhythms are present and can be seen to be due to the PYR cell population firing in bursts of theta frequency. Even more, we notice that the pattern of the input current to the PYR cells isn't theta-paced or periodic (see Figure 10Bi)."

This is a loose statement. When you look at the raw LFP theta is also not apparent (e.g. Figure 9.Ei or Fi). What happens once you look at the spectrum of the activity shown in 10.Bi? Do you see theta or not?

2) l. 562 "This implies that the different E-I balances in the segment model that allow LFP theta rhythms to emerge are not all consistent with the experimental data, and by extension, the biological system."

This is speculative. We do not know how generic the results of Amilhon et al. are. They showed what you can find experimentally, not what you cannot find experimentally. I agree with the statement from l.581, though : "Thus, from the perspective of the experiments of Amilhon et al. (2015) theta rhythm generation via a case a type pathway seems more biologically realistic ..."

3) There are several problems with access to code and data provided in the manuscript.

l. 986, 1113 - osf.io does not give access<br> l. 1027 - bitbucket of bezaire does not allow access l. 1030 - simtracker link is down l. 1129, 1141 - the github link does not exist (private repo?)

4) l. 1017 - Afferent inputs from CA3 and EC are also included in the form of Poisson-distributed spiking units from artificial CA3 and EC cells.

Not obvious if Poisson is adequate here - did you check on the statistics of inputs? Any references? Different input statistics may induce specific correlations which might affect the size of fluctuations of the input current. I do not think this would be a significant effect here unless the departure from Poisson is highly significant. Any comments might be useful.

5) l. 909 - "Euler integration method is used to integrate the cell equations with a timestep of 0.1 msec."

This seems dangerous. Is the computation so costly that more advanced integration is not viable?

Reviewer #2:

This manuscript asked the question of how axons vs dendrites are lost by the live-imaging cortex of rTg4510 tau transgenic mice. Overall, this manuscript is well-done and well-written, and confirms previous findings. However, there are a number of key controls missing from the experimental data (please see below). Statistical analyses are satisfactory (with some caveats, please see below).

Figures 1+2 replicate previous findings also in rTg4510 (Crimins et al., 2012; Jackson et al., 2017; Kopeikina et al., 2013); Figures 3+4 (Ramsden et al., 2005; SantaCruz et al., 2005; Spires et al., 2006; Crimins et al., 2012; Kopeikina et al., 2013; Helboe et al., 2017; Jackson et al., 2017). The novelty here are the differing patterns of bouton and spine turnover shortly before axons and dendrites, respectively, are lost, which is a finding uniquely enabled by 2-photon. Thus, findings in Fig. 5/6 should be highlighted and solidified. Further, the manuscript lacks mechanistic insight.

It is not clear how the authors ensure that the perceived loss of spines/boutons/dendrites/axons is not due to bleaching or loss of the GFP signal. Please validate loss of spines/boutons and actual synapses using fixed tissue imaging or electron microscopy on a separate cohort of mice.

Did the authors control for gliosis after the repeated imaging (very short after viral injection and cranial window implant on the same site)? Could it be that the repeated imaging itself on a damaged tissue induces blebbing on the already more vulnerable spines in the tau mice? Please show Iba1 and GFAP with and without doxycycline administration should be included in supplemental along with area staining quantification. Transgenic mice without manipulation (viral injection/cranial window/2P imaging) should also act as a control to ensure no gliosis is observed.

rTg4510 transgene insertion: Gamache et al. recently showed that the integration sites of both the CaMKIIα-tTA and MAPT-P301L transgenes impact the expression of endogenous mouse genes. The disruption of the Fgf14 gene in particular contributes to the pathological phenotype of these mice, making it difficult to directly ascribe the phenotypes seen in the manuscript to MAPT-P301L transgene overexpression. Although this limitation is acknowledged in the discussion, the T2 mice employed in this paper (Gamache et al., 2019) would be suitable controls to better evaluate the contribution of tauP301L alone on the neuropathology and disease progression observed in the authors' experiments, at least in fixed synapse imaging.

Reviewer #2:

The paper titled "Brain Network Reconfiguration for Narrative and Argumentative Thought" sought to uncover the common neural processing sequences (time-locked activations and deactivations; inter-subject correlations and inter-subject functional connectivity) underlying narrative and argumentative thought. In particular, the study aimed to provide evidence that would help adjudicate between two current theories: the Content-Dependent Hypothesis (narrative argumentative) and the Content-Independent Hypothesis (narrative = argumentative). In order to assess these possibilities they tested participants in an fMRI scanner as they listened to validated narrative and argumentative texts. Each text condition was directly compared to resting state and scrambled versions of the texts. Across a range of interesting analyses that focus on how each participant's brain synchronized with other participants' brains throughout the same narrative and argumentative texts, they primarily found support for the content-dependent hypothesis with a few differences and commonalities across text conditions. Relative to the scrambled conditions, listening to narrative texts was more associated with default mode activity across participants and listening to argumentative texts only activated a common network of superior fronto-parietal control regions and language regions. Argumentative texts did not differ much from scrambled versions of the same text. These patterns reveal themselves in both ISC and ISFC data. Overall, I feel like this paper is really well written and is a novel approach to distinguishing the neural processes between similar, but different types of thought. At times the manuscript loses touch with its primary brain coordination metrics (ISC and ISFC), describing the findings more like a GLM or functional connectivity study.

Comments:

Introduction:

1) The introduction is very clearly written and uses a wonderful variety of sentence structure. Well done!

2) While the writing is beautiful, a few sentences are less easy to comprehend than others. For example the use of outstands in line 36 is a bit difficult to parse on first read. Consider simplifying the language some.

3) There seems to be an opportunity to discuss this work and its findings in a broad context of narrative or argumentative self-generated internal thought (not based on listening to texts). For instance, I think there could be a few sentences tying this work to studies of autobiographical memory retrieval or mind wandering (for argumentation perhaps studies of the cognitive and neural processes behind complex decision making). This is captured to some extent in the introduction and discussion, but I think it could go further with citations beyond those just associated with listening to various types of text.

4) Appreciate the thorough discussion of hypotheses and background.

5) It is not necessary, but it might be interesting to show some basic functional connectivity analyses of the individual participant activations in supplemental analyses (no ISC or ISFC).

Methods:

1) Please clarify how the ISFC analysis can be directional in any way? Does unidirectional mean that you're just taking one value for each pairwise connection Cij?

Results:

1) To what extent is there a concern that participants would still try to stitch together the scrambled narratives even if they are less coherent? Was this even possible given the nature of the stimuli?

2) In line 125 and throughout the authors should consistently remind the reader that 'engagement' in this case means that there were consistent and correlated increases in the bold response across participants. This differs in some ways to task engagement in event-related GLM studies.

3) The language throughout should reflect consistent involvement across participants at particular time points in each of the narratives vs the argumentative.

4) It seems like argumentative is more similar to the scrambled in many ways. Might it be that argumentative texts are just less coherent and structured than narrative texts?

5) It seems clear that the neural processing of argumentative texts (64 distinct edges) were very different from the narrative texts (2348 distinct edges), but that the current contrasts did not clearly and consistently distinguish argumentative thought from the scrambled argument conditions. A discussion of the analyses that might be necessary to better elucidate the dynamics of processing for argumentative thought would be helpful.

Discussion:

1) Were there any neural differences between the narrative vs argument scrambled-texts? This might reveal any differences in the processing of the scrambled texts for each condition and might help shine light on features of the scrambled argument condition that contributed to the overall lack of distinction relative to the narrative vs scrambled narrative conditions.

2) Throughout the results from ISC and ISFC findings are convolved with the findings from univariate or GLM results from prior studies. Please compare and contrast how ISC and ISFC findings might relate to univariate or GLM findings early in the discussion.

3) Related to point 2 in the introduction, please also cite studies from autobiographical memory retrieval studies that also show the frontoparietal control system working as information is iteratively accumulated and updated over long temporal windows (St. Jacques et al., 2011; Inman et al., 2018; Daselaar et al., 2008).

4) Please reconsider how the ISC findings are discussed as 'activation'. While the BOLD activity of these areas are certainly coordinated across participants at similar points in the text, I feel like the term activation fits best with studies that convolve the brain activity with an HRF. In particular, from what I understand ISC, a common decrease in BOLD activity across participants at the same time in a read text would also lead to activity or 'activation' of that area in an ISC analysis. This seems counterintuitive. The 2nd paragraph of the discussion describes ISC and ISFC well in terms of what it shows across a sample (synchronization of fluctuations in BOLD activity across participants for the same stimuli). "Activity" may capture this, but please consider some more nuanced ways to refer to these ISC and ISFC findings.

Figures:

1) Please double check the box plots in figure 1a for Scene Construction. Another method of displaying this likert rating data might be helpful. While appreciating the attempt to display the individual data points, the simple main points get somewhat obscured by all of the information in the graph.

2) Overall, I appreciate the attention to detail in all of the figures and the completeness of the data visualization with several useful supplemental figures.

Reviewer #2:

General assessment:

This manuscript presents an improved methodology for extracting distinct early auditory evoked potentials from the EEG response to continuous natural speech, including a novel method for obtaining simultaneous responses from different frequency bands. It is a clever approach and the first results are promising, but more rigorous evaluation of the method and critical evaluation of the results is needed. It could provide a valuable tool for investigating the effect of corticofugal modulation of the early auditory pathway during speech processing. However, the claims made of its use investigating speech encoding or clinical diagnosis seem too speculative and unspecific.

General comments:

1) Despite repeated claims, I don't think a convincing case is made here that this method can provide insight on how speech is processed in the early auditory pathway. The response is essentially a click-like response elicited by the glottal pulses in the stimulus; it averages out information related to dynamic variations in envelope and pitch that are essential for speech perception; at the same time, it is highly sensitive to sound features that do not affect speech perception. What reason is there to assume that these responses contain information that is specific or informative about speech processing?

2) Similarly, the claim that the methodology can be used as a clinical application is not convincing. It is not made clear what pathology these responses can detect that current methods ABR cannot, or why. As explained in the Discussion, the response size is inherently smaller than standard ABRs because of the higher repetition rate of the glottal pulses, and the response may depend on more complex neural interactions that would be difficult to quantify. Do these features not make them less suitable for clinical use?

3) It needs to be rigorously confirmed that the earliest responses are not contaminated or influenced by responses from later sources. There seems to be some coherent activity or offset in the baseline (pre 0 ms), in particular with the lower filter cut off. One way to test this might be to simulate a simple response by filtering and time shifting the stimulus waveforms, adding these up plus realistic noise, and applying the deconvolution to see whether the input is accurately reproduced. It might be useful to see how the response latencies and amplitudes correlate to those of conventional click responses, and how they depend on stimulus level.

4) The multiband responses show a variation of latency with frequency band that indicates a degree of cochlear frequency specificity. The latency functions reported here looks similar to those obtained by Don et al 1993 for derived band click responses, but the actual numbers for the frequency dependent delays (as estimated by eye from figures 4,6 and 7) seem shorter than those reported for wave V at 65 dB SPL (Don et al 1993 table II). The latency function would be better fitted to an exponential, as in Strelcyk et al 2009 (equation 1), than a quadratic function; the fitted exponent could be directly compared to their reported value.

5) The fact that differences between narrators leads to changes to the ABR response is to be expected, and was already reported in Maddox and Lee 2018. I don't understand why it needs to be examined and discussed at such length here. The space devoted to discussing the recording time also seems very long. Neither abstract or introduction refers to these topics, and they seem to be side-issues that could be summarised and discussed much more briefly.

L142-144. Is it possible to apply the pulse train regressor to the unaltered speech response? If so, does this improve the response, i.e. make it look more similar to the peaky speech response? It would be interesting to know whether improvement is due to the changed regressor or the stimulus modification or both.

L208 -211. What causes the difference between the effect of high-pass filtering and subtracting the common response? If they serve the same purpose, but have different results, this raises the question which is more appropriate.

L244. This seems a misinterpretation. The similarity between broadband and summated multiband responses indicates that the band filtered components in the multiband stimulus elicited responses that add linearly in the broadband response. It does not imply that the responses to the different bands originate from non-overlapping cochlear frequency regions.

L339-342. Is this measure of SNR appropriate, when the baseline is artificially constructed by deconvolution and filtering? Perhaps noise level could be assessed by applying the deconvolution to a silent recording instead? It might also be useful to have a measure of the replicability of the response.

Reviewer #2:

General assessment of the work:

In this manuscript Higgs and colleagues test the hypothesis that imprinted gene expression is enriched in the brain, and that identifying specific brain regions of enrichment will aid in uncovering physiological roles for imprinted pathways. The authors claim that the hypothesis that imprinted genes are enriched in key brain functions has never been formally/systematically tested. Moreover, they suggest that their analysis represents an unbiased systems-biology approach to this question.

In our assessment the authors fail to meet these criteria on several major grounds. Firstly, there are multiple instances of methodological bias in their analysis (detailed below). Secondly, the authors claim that their findings are validated by similar test results in 'matched' datasets. However, throughout the authors appear to have avoided identifying individual imprinted genes that are enriched in their analysis (they can be found in a minimally annotated supplementary file). Due to this it is impossible to judge to what extent there is agreement between matched datasets and between levels of the analysis. For these reasons the analysis appears arbitrary rather than systematic, and lacks rigor. Consequently we do not feel that the work of Higgs and colleagues goes beyond previous systematic reports of imprinting in the brain (for example, Gregg, 2010, Babak 2015, in ms reference list).

Numbered summary of substantive concerns:

1) Imprinted genes that were identified as enriched are not clearly named or listed

-The authors use two or more independent datasets at each level to "strengthen any conclusions with convergent findings" (p4 ln96). By this the authors mean that both datasets pass the F-test criteria for enrichment. However, they should show which imprinted genes are allocated to each region, and clearly present the overlap. Are the same genes enriched in the two datasets? Similarly, are the same genes that are enriched in, e.g. the hypothalamus the same genes that are enriched in the ARC?

-The authors discuss how their main aim of identifying expression "hotspots" helps inform imprinted gene function in the brain. An analysis of the actual genes is therefore crucial (and the assumed next step after identifying the location of enrichment).

-The authors allocate parental expression enrichment to the brain regions but do not state why they do this analysis.

-Are imprinted genes in the same cluster co-expressed, as might be expected?

2) Selection of datasets needs to be more clearly explained (i.e. a selection criteria)

-Their reason for selection "to create a hierarchical sequence of data analysis" - suggests that there could be potential bias in their selection based on previous knowledge of IG action in the brain.

-A selection criteria would explain the level of similarity between datasets, which is important before datasets are systematically analyzed

3) The study is more like a set of independent analyses of individual datasets (rather than one systematic/meta-analysis)

-Each dataset was individually processed (filtered and normalized) following the original authors' procedure, rather than processing all the raw datasets the same way.

-"A consistent filter, to keep all genes expressed in at least 20 cells or (when possible) with at least 50 reads" (p7 ln115), our emphasis - which filter was used? This should be consistent throughout.

-Two different cut-offs were used to identify genes with upregulated expression, making the identification of enriched genes arbitrary (p7 para2).

-Some datasets contain tissues from various time-points and sexes, but there is no clarification if all the data was included in the analysis. (e.g. the Ximerakis et al. dataset was originally an analysis of young and old mouse brains). This is particularly difficult to interpret when embryonic data is likened to adult data, which is in no way equivalent.

-The cell-type and tissue-type identities were supplied by the dataset authors, based on their original clustering methods. This can be variable, particularly at the sub-population level.

4) These differences make it hard to draw connections between the findings from each dataset

-In some levels, the authors compare two datasets for a "convergence" of IG over-expression. Yet the above differences between datasets and analyses makes them difficult to compare. (e.g. the comparison of hypothalamic neuronal subtypes with enriched IG expression between two datasets in level 3.a.2 is quite speculative).

-More generally, the authors draw connections between their findings from each level, but the lack of consistency between analyses may not justify these connections.

5) Hence, the study does not lead to a definitive set of findings that is new to the field

-The above reasons suggest that this is not an objective set of data about IG expression in the brain, but rather evidence of certain hotspots for targeted analysis. However, these hotspots were already known.

-A systematic analysis of raw data using fewer datasets, that then includes and discusses the imprinted genes, may lead to novel findings and a paper with a clearer narrative.

Reviewer #2:

The authors describe the development and use of a D-Serine sensor based on a periplasmic ligand binding protein (DalS) from Salmonella enterica in conjunction with a FRET readout between enhanced cyan fluorescent protein and Venus fluorescent protein. They rationally identify point mutations in the binding pocket that make the binding protein somewhat more selective for D-serine over glycine and D-alanine. Ligand docking into the binding site, as well as algorithms for increasing the stability, identified further mutants with higher thermostability and higher affinity for D-serine. The combined computational efforts lead to a sensor for D-serine with higher affinity for D-serine (Kd = ~ 7 µM), but also showed affinity for the native D-alanine (Kd = ~ 13 uM) and glycine (Kd = ~40 uM). Molecular simulations were then used to explain how remote mutations identified in the thermostability screen could lead to the observed alteration of ligand affinity. Finally, the D-SerFS was tested in 2P-imaging in hippocampal slices and in anesthetized mice using biotin-straptavidin to anchor exogenously applied purified protein sensor to the brain tissue and pipetting on saturating concentrations of D-serine ligand.

Although presented as the development of a sensor for biology, this work primarily focuses on the application of existing protein engineering techniques to alter the ligand affinity and specificity of a ligand-binding protein domain. The authors are somewhat successful in improving specificity for the desired ligand, but much context is lacking. For any such engineering effort, the end goals should be laid out as explicitly as possible. What sorts of biological signals do they desire to measure? On what length scale? On what time scale? What is known about the concentrations of the analyte and potential competing factors in the tissue? Since the authors do not demonstrate the imaging of any physiological signals with their sensor and do not discuss in detail the nature of the signals they aim to see, the reader is unable to evaluate what effect (if any) all of their protein engineering work had on their progress toward the goal of imaging D-serine signals in tissue.

As a paper describing a combination of protein engineering approaches to alter the ligand affinity and specificity of one protein, it is a relatively complete work. In its current form trying to present a new fluorescent biosensor for imaging biology it is strongly lacking. I would suggest the authors rework the story to exclusively focus on the protein engineering or continue to work on the sensor/imaging/etc until they are able to use it to image some biology.

Additional Major Points:

1) There is no discussion of why the authors chose to use non-specific chemical labeling of the tissue with NHS-biotin to anchor their sensor vs. genetic techniques to get cell-type specific expression and localization. There is no high-resolution imaging demonstrating that the sensor is localized where they intended.

2) Why does the fluorescence of both the CFP and they YFP decrease upon addition of ligand (see e.g. Supplementary Figure 2)? Were these samples at the same concentration? Is this really a FRET sensor or more of an intensiometric sensor? Is this also true with 2P excitation? How does the Venus fluorescence change when Venus is excited directly? Perhaps fluorescence lifetime measurements could help inform what is happening.

3) How reproducible are the spectral differences between LSQED and LSQED-T197Y? Only one trace for each is shown in Supplementary Figure 2 and the differences are very small, but the authors use these data to draw conclusions about the protein open-closed equilibrium.

4) The first three mutations described are arrived upon by aligning DalS (which is more specific for D-Ala) with the NMDA receptor (which binds D-Ser). The authors then mutate two of the ligand pocket positions of DalS to the same amino acid found in NMDAR, but mutate the third position to glutamine instead of valine. I really can't understand why they don't even test Y148V if their goal is a sensor that hopefully detects D-Ser similar to the native NMDAR. I'm sure most readers will have the same confusion.

it happened again in 2016

It is not enough by only understanding the discipline, because discipline is skill that should be show by actions.

In this statement Krishna explaining the honor of participation in the battle than death, because if Arjuna do not participate in the battle then it will be a big shame for the rest of his life.

In my view Indian people believes to the life after death, but what it means the adjective of certain for birth and death?

Arjuna is kinda confused with Krishna's speech. although Arjuna is not agree with Krishna in some parts, but still why he keep asking for his guide?

Krishna believe that fighting against Bhishma and Drono is a big sin for him. because they do not deserve to be killed instead they deserve to worship.

1169 proteins

174 genomes

1442 genomes

This is the Svelte version of this example: https://codesandbox.io/s/reactivity-react-responds-to-changing-props-forked-d2j44?file=/src/Label.js

They even named the main file react.js so when converting/migrating components from React you could (at least some of the time, perhaps) simply leave some of the imports as-is:

import {createHooks, useRef} from './react';

The Republican party will never stop claiming the media is bias, so I am surprised they are claiming they have resolved this issue. I would think they would want to keep acknowledging it as an issue.

"The President has been regulating to death a free market economy" - it's interesting how much this preamble throws Trump under the bus

"our enemies no longer fear us and our friends no long trust us" - I guess the democrats and republicans agree on this.

"This platform is optimistic because the American people are optimistic." This is completely unsupported by everything stated before it.

"covenant" "Creator" "God-given natural resources" "prepared to deal with evil in the world" show religious tone