Reviewer #1:

The authors provide interesting evidence on the properties of CSF-contacting neurons, referred to as 'CSFcNs' in their manuscript, using 2 photon calcium imaging in mice.

Their work relies on calcium imaging using 2 photon microscopy in slices of the mouse spinal cord. The authors observed calcium transients with two different amplitudes and propose that these transients reflect the activation of different voltage dependent calcium channels (T and L).

Although the work is of interest, there are throughout the manuscript numerous issues: -shortcuts and oversimplified assumptions (calcium transients do not equal spikes!) (see title of Figure 2, 3) -the massive ignorance of the relevant literature for this small field on CSF-cNs in mice. In particular, but not only, the authors should know and refer to the work of Orts Dell'Immagine, Wanaverbecq, Trouslard who have shown since 2012 that CSF-cN in mice are chemosensory cells whose spontaneous activity is driven by the channel PKD2L1.

Major comments

1) The authors assume that calcium transients equal to firing (Figure 2) or calcium spikes (Figure 3) but these are far from being the same. No deconvolution algorithm can use calcium transients to infer spiking with better than 70% accuracy.

In the recordings of the Wanaverbecq group, spontaneous firing in slices was 0.4Hz in control and 0.1Hz in PKD2L1 KO. The authors find here calcium transients occurring at 0.16Hz (n = 63 cells), suggesting that some of the sparse firing activity is missed by the authors.

Since calcium transients reflect spiking but not in a linear manner, a calibration is necessary via cell attached or loose patch recordings in order to infer on CSF-cN spiking, or perforated patch to validate the evidence for calcium spikes.

2) This assumption of calcium = firing does not hold in cells that have an input resistance of GOhms and whose activity has been shown to be driven by the opening of the channel PKD2L1 (Orts Del Immagine et al Neuropharmacology 2016). In particular, observations of the TTX insensitive calcium transients may be due to the PKD2L1 channel.

=> The authors need to combine recordings with perforated Patch Clamp together with the 2P calcium imaging in order to tackle the question of the role of the channel openings in the generation of the different calcium transients observed in WT or KO for PKD2L1.

From introduction to discussion, the authors should properly cite the work of the Wanaverbecq group as well as other groups in the field, whose contributions were relevant and ignored.

3) Activation leading to calcium spikes (K+, ATPergic, Cholinergic inputs, ...) was done without blockage of the neurotransmission in the slices and could therefore originate from indirect sources, including activation of metabotropic receptors presynaptically.

The authors need to solve these issues.

4) In Figure 7, there are diverse responses that the authors should better illustrate. Many cells appear to not respond for multiple stimuli tested : what is the rational criterion to define that a cell responded or not? Can the authors quantify the proportion of cells responding? Did the author take into account the high level of spontaneous activity? Can the negative dip in response possibly from a motion artifact in panel G and H?

Reviewer #1:

I'm quite enthusiastic about the care the authors have taken in designing this cutting edge hybrid environment, and the effort they've gone through to describe it in detail. I believe that this endeavor has great merit, and that seeing the advancements in animal welfare and experimentation should be of interest to the general reader. However, at present, the stated interpretations are not fully justified by the results, and this must be addressed.

The manuscript should be amended and updated in one of two possible ways: the interpretations of the scientific result here should be tamped down significantly, or additional evidence should be presented for some of the claims in the originally submitted manuscript. I am confident that the authors should be able to carry out either of these to a satisfying degreen.

Major issues:

1) Throughout the manuscript, stating that the third monkey learned the task "merely by observing two other trained monkeys" is misleading. The naive monkey may have learned very important details about the cognitive testing set-up from observation. But the third monkey learned the task of a unique behavioural shaping paradigm that included -but was not limited to- watching trained monkeys. The authors trained the third monkey on the cognitive task in the absence of the other monkeys, and do not show that the third monkey learned the specific cognitive task from watching other monkeys. Over-interpreting the anecdotal observations here hinders obfuscates what is novel and notable in this manuscript.

2) The authors repeatedly state that the third monkey learned the task faster than the previous two monkeys. It is quite difficult to parse exactly what the authors mean by this, and exactly what the data is that supports that claim.

The authors go on to state that M2 learned the "task structure" faster than M1/M3. However, "task structure" is not defined, so it is difficult for a reader to know precisely what was learned faster under social observation. Furthermore, the data showing that M2 learned the task structure faster than M1/M3 is not clear, and it is not known how M1/M3 learned the task structure in isolation. Description of which training steps may be aided by observation of trained monkeys must be clarified. The authors allowed M2 to observe M1 and M3 during initial familiarization of the experimental set-up, but it seems that observation may not have aided M2 in learning the complex same-different task at all.

Even though M2 may have learned the task structure faster than M1/M3, these observations are anecdotal and should not be over-interpreted. If there is a clear difference in the time to learn basic task structure, it may be due to social observation, but the authors should not favor that interpretation without considering alternatives as well. E.g., monkeys have widely varying personalities (see e.g. Capitanio 1999, Am J Primatology), and this has important implications for the curiosity, exploration behavior, and likelihood to accept and complete new challenges in training. To what extent could the differences in learning rate also be explained by these differences across these 3 monkeys? To what extent does the different training regimen in the task explain differences in learning rate across monkeys (e.g. M2 got two days of repeating correction trials, which significantly alters learning rates)?

3) There is a vast literature in ethological settings where the gaze of nonhuman primates has been tracked using noninvasive methods that the authors do not acknowledge. Instead, authors state that most infrared eye trackers require head restraint (line 32), though this is demonstrably not the case. For review, see Hopper et al. 2020, Behav Res Methods.

4) Some important details for introducing monkeys to the testing apparatus during Tailored Automated Training should be described. For example, were animals water-restricted, or on any sort of fluid restriction when TAT began? How did the authors entice the animals to initially explore the testing apparatus?

Reviewer #1:

General Assessment:

The work presented by Knight et al. in "Major genetic discontinuity and novel toxigenic species in Clostridioides difficile taxonomy" is of excellent quality and spans several of the themes of eLife. The manuscript provides a thorough and robust examination of publicly available C. difficile genomes, to deliver a much-needed update of C. difficile phylogeny, in particular the cryptic clades of C. difficile. However, there are some further clarifications could be included to confirm if the cryptic clades of C. difficile, and the 26 unclassified STs (which seemingly form 4 distinct clusters) should indeed be assigned to the Clostridioides genus, distinct from both C. mangenotii and C. difficile.

Specific comments:

Lines 96-97 and Figure 2: Figure 2 suggests the 26 unclassified STs form at least 4 distinct clusters, yet these STs are classified as outliers. Could you please comment on why these are considered outliers? Or do these STs represent new cryptic clades? C-IV, C-V etc.? And do these unclassified STs also fit into the criteria for the novel independent Clostridioides genomospecies?

Lines 161-162; Table 1: C. mangenotii is referred to as Clostridioides mangenotii on lines 161-162, but has been listed as Clostridium mangenotii in table 1. Was this intentional? Or should this be Clostridioides mangenotii as C. difficile is also listed as Clostridioides difficile?

Figure 6: Many of the numbers and symbols on the figure are difficult to see e.g. Figure 6A the values listed above each data point are extremely small. Can these values/symbols be increased?

Lines 224-225: Given that C. difficile strains lacking tcdA and tcdB can still cause infections, consider rephrasing "indicating their ability to cause CDI".

Figure 7: As with Figure 6, many of the numbers and symbols on the figure are difficult to see. Can these values/symbols be increased?

General comments:

Were the unclassified STs included in the species wide ANI analyses in Figure 3? If similar analyses were performed for these STs and given the clusters that are presented in Figure 2 would this support the idea that they may also fit into the criteria for the novel independent Clostridioides genomospecies?

Similarly, were these same unclassified STs included in the BactDating and BEAST analyses? Or the pairwise ANI and 16S rRNA value comparisons in Figure 5? Or the pangenome and toxin gene analysis also presented in Figures 6 and 7? And would this add further strength to the idea that these "outliers" could be the first typed representatives of additional genomospecies?

Lastly, your conclusions are a little too on the fence. You have presented sufficient evidence to suggest that the cryptic clades of C. difficile likely represent novel independent Clostridioides genomospecies, but dilute out the importance of this throughout the discussion and conclusions. Although controversial, the evidence provided gives credence to these claims, and the text should be changed to reflect this.

Reviewer #1:

In the study by Buus et al., the authors set out to address an important need to understand how oligo-conjugated antibodies should be optimally utilized in droplet-based scRNA-seq studies. These techniques, often referred to as CITE-seq, complement techniques such as flow cytometry and mass cytometry yet also further extend them by the ability to jointly measure intra-cellular RNA-based cell states together with antibody-based measurements. As is the case with flow cytometry, manufacturers provide staining recommendations, yet encourage users to titrate antibodies on their specific samples in order to derive a final staining panel. Based on the ability to stain with hundreds of antibodies jointly, few studies to date have assessed how the antibodies present in these pre-made staining panels respond to a standard titration curve. In order to address this point, this study tests two dilution factors, staining volume, cell count, and tissue of origin to understand the relationships between signal and background for a commercially available antibody panel. They arrive at the general recommendation that these panels could be improved, grouping various antibodies into distinct categories.

This study is of general interest to the scRNA-seq and CITE-seq communities as it draws attention to this important aspect of CITE-seq panel design. However, it would stand to be substantially improved by not only providing suggestions but also testing at least one, if not more, of their suggestions from Supplementary Table 2, and preferably performing experiments using more technical replicates or biological replicates. As it stands now, the study is largely based on one PBMC and one lung sample, that were stained once with each manipulation as far as can be gathered from the Methods.

Major comments:

1) Given the title is improving oligo-conjugated antibody... it would be important to functionally test one of the suggestions. We would suggest a full titration curve of selected antibodies, perhaps one from each of the categories, but if cost is a concern at least two or three antibodies, to identify how titration impacts antibodies, and especially those in categories labeled as in need of improvement. Relatedly, if the idea is that if antibodies (such as gD-TCR) do not have a cognate receptor leading to general background spread, does spiking in a cell that is a known positive in increasing ratios remedy this issue by acting as a target for the antibodies? Does adding extra washes help to remedy these issues of background?

2) Another way of improving these panels is through reducing the costs spent on both staining but perhaps more importantly the sequencing-based readouts. Several times in the manuscript (at line 77 for example or line 277) it is alluded to that the background signal of antibodies can make up a substantial cost of sequencing these libraries. However, no formal data on cost is presented, which would be important to formalize the author's points. It would be important to provide cost calculations and recommendations on sequencing depth of ADT libraries based on variation of staining concentration. Relatedly, in the methods, sequencing platform and read depth for ADT libraries was not discussed, nor is the RNA-seq quality control metrics provided other than a mention of ~5,000 reads/cell targeted. This is important to report in all transcriptomic studies, and especially a methods development study.

3) One of the powerful elements of joint multi-modal profiling, as mentioned in the title, is to be able to measure protein and RNA from a single cell. This study does not formally look at correlation of protein and RNA levels, and whether a decrease in concentration of antibody either improves or diminishes this correlation. This would be important to test within this study to ensure that decreasing antibody levels does not then adversely affect the power of correlating protein with RNA, and whether it may even improve it.

4) How was the lack of antibody binding determined for Category E? CD56 is frequently detected on NK cells in peripheral blood, CD117 should be detected on mast cells in the lung, and CD127 should be found on T cells, particularly CD8+ T cells. From inspecting Figure 1E, it appears as if all three of these markers are detected on small but consistent cell subsets. As the clusters are only numbered and no supplementary table is provided to help the reader in their interpretation, it is difficult to determine if these represent rare but specific binding, or have not bound with any specificity.

5) References: At 14 references, the paper overall could benefit from a more comprehensive citation of related literature including flow cytometry and/or CyTOF best practices for antibody staining and dealing with background, and joint RNA and protein measurement from single cells.

Reviewer #2:

In this paper, Numssen and co-workers focus on the functional differences between hemispheres to investigate the "domain-role" of IPL in different types of mental processes. They employ multivariate pattern-learning algorithms to assess the specific involvement of two IPL subregions in three tasks: an attentional task (Attention), a semantic task (Semantics) and a social task (Social cognition). The authors describe how, when involved in different tasks, each right and left IPL subregion recruits a different pattern of connected areas.

The employed tasks are "well established", and the results confirm previous findings. However, the novelty of the paper lies in the fact that the authors use these results as a tool to observe IPL activity when involved in different domains of cognition.

The methodology is sound, well explained in the method section, the analyses are appropriate, and the results clear and well explained in the text and in graphic format.

However, a solid experimental design is required to provide strong results. To the reviewer's view, the employed design can provide interesting results about functional connectivity, but not about the functional role of IPL in the investigated functions.

I think the study would be correct and much more interesting if only based on functional connectivity data. Note that rewriting the paper accordingly would lead to a thorough discussion about how anatomical circuits are differently recruited based on different cognitive demands and about the variable role of cortical regions in functional tasks. This issue is neglected in the present discussion, and this concept is in disagreement with the main results, suggesting (probably beyond the intention of the authors) that different parts of the right and left IPL are the areas responsible for the studied functions.

Major points:

1) The 3 chosen tasks explore functions that are widespread in the brain, and are not specifically aimed at investigating IPL. The results (see. e.g. fig 1) confirm this idea, but the authors specifically focus on IPL. This seems a rather arbitrary and not justified choice. If they want to explore the lateralization issue, they should consider the whole set of involved areas or use tasks showing all their maximal activation in IPL.

2) The authors aims to study lateralization using an attentional task, considering the violation of a prevision (invalid>valid), a linguistic task, looking for an activation related to word identification (word>pseudoword) and a social task, considering correct perspective taking (false belief>true belief), but they do not consider that in all cases a movement (key press) is required. It is well known that IPL is a key area also for creating motor commands and guiding movements. Accordingly, the lateralization bias observed could be due more to the unbalance between effectors while issuing the motor command, than to a different involvement of IPL regions in the specific tasks functions.

3) Like point 2, the position of keys is also crucial if the authors want to explore lateralization. This is especially important if one considers that IPL plays a major role in spatial attention (e.g. Neglect syndrome). In the Methods, the authors simply say "Button assignments were randomized across subjects and kept identical across sessions", this should be explained in more detail.

4) The authors show to know well the anatomical complexity of IPL, however their results are referred to two large-multiareal-regions. This seems to the reader at odds with all the descriptions related to fig.2. If they don't find any more subtle distinction within these 2 macro-regions, they should at least discuss this discrepancy.

5) The part about Task-specific network connectivity is indeed very interesting, I would suggest to the authors to focus exclusively on this part. (Note that the results of this part seems to confirm that only the linguistic task is able to show a clear lateralization).

Reviewer #1:

The authors have performed a rare feat in the study of the posterior parietal cortex, which is to achieve a functional parcellation of this crucial area on the basis of its response during a diverse set of tasks. The variety of tasks and the analytical approach married to it are very strong and lead to a division that agrees well with data from patients with lesions and studies in homologous areas of non-human primates.

Readers are encouraged to note the analytical approach, with particular regard for the permutation testing that establishes the differences between the tasks in the functional connectivity of the area.

Conceptually, this paper is another strong argument for understanding the broad role of the posterior parietal across tasks and point at the flexibility of its functional response in supporting those roles.

This manuscript lays out a series of fMRI investigations and analyses centered on examining the response of the IPL during three different tasks (attention, semantics, social cognition). The analyses are largely data-driven and examine functional response and connectivity, to make the argument for a functional parcellation of the IPL into at least two distinct subregions. The manuscript is well-written and the analyses well described. There are some concerns about the analyses that dampen enthusiasm slightly and a lack of consideration of the associated literature in non-human primates, but these problems seem imminently correctable.

The analyses begin with a data-driven cluster analysis across an anatomically constrained IPL ROI, searching for cluster solutions that efficiently parcellate IPL on the basis of the response of voxels across the three tasks. This analysis is fine, but does constrain the average activity in the identified clusters to differ across the tasks. That makes the univariate activation in 3b a bit circular and hard to interpret. Either the error bars should be removed and a note added that the univariate activity is purely descriptive or the univariate data should be displayed from a slice of the data that did not contribute to the derivation of the clusters. The strongest version of this analysis would hold out entire participants.

The predictive coding analysis is potentially informative but the details were a bit unclear. In the one versus rest analysis the strongest test would be to build the model on the data from n-1 participants and then test it on the trials of the held-out participant. If this was not done, some justification for not doing it would be in order.

Finally, the authors should also consider integrating some of the non-human primate literature as it only strengthens their case. In the human literature the IPL has proved a tough nut to crack, but the single unit physiology has revealed strong differences in the homologous areas of macaque, some of which directly map onto the division argued for here.

Reviewer #1:

Xiao et al describes a kinetic model of enhance-promoter interactions, which the authors use to explain the changes in transcription levels upon disruption of genomic contacts within topologically associated domains (TADs). The model uses the law of mass action to describe activity of promoters and enhancers, which are proposed to be able to accommodate multiple transcription activation tags. The authors use the model to explain the nonlinear relationship between the genomic contact frequencies within TADs and their corresponding transcription rates. They recapitulate the superlinear relationship between the changes in genomic contact probabilities and transcription rates within TADs observed in their recent experiments (Mateo et al, 2019). Inspired by the futile cycle of cell signaling, their model incorporates multiple tagging of promoters allowing for transient amplification of transcription rates.

Conceptually, this work is interesting and the model suggests possible reconciliation of seemingly contradictory experimental observations reported earlier.

However, the manuscript in its current form fails to substantiate many of its claims.

Here are my major concerns:

1) The presentation of the model is unclear. It is currently present in the text, lines 110-122, in pure qualitative description. Authors define only rates in the text; definitions of other model parameters are not present. For example, E and a are not specifically defined in the text or Methods section. Since both terms "enzyme" and "enhancer" are being used and in fact "enzyme tagging" and "enhancer tagging" occur simultaneously in the model, it is not possible to say for sure when do authors call which one in the model and thus the methods section can be interpreted in different ways. Moreover, the cartoon is missing a legend confirming, which molecular player is which. The figure caption mentions only green triangles being the tags, but no other parts of the cartoon are being explained. Taken together, this makes it very difficult to verify the mechanics of the model.

• The authors should provide a detailed technical description of their model directly in the text, including description of their parameters, list their constitutive equations and identify all parameters in their cartoon Fig. 1C.
• Axes labels in all figures should be expressed in the parameters/variables of the model (as in Fig. 6C-D) directly connecting to inputs/outputs of the model.

2) Due to the lack of description, in many sections it is not clear what are the specific inputs and outputs of the model (e.g. Fig. 2).

3) The Methods section describes the chemical kinetics of the suggested reactions and the insulation score calculations. But it is not clear how do these inform each other, how are contact-frequency maps chosen/computed and cross-referenced with the local E-P kinetics?

4) In the Methods section, it appears that in lines 577-580 of the model description, the mass is not conserved.

5) In 587-588, the index of k is 2(n+1), which equals to 2n+2, but then in the next line the following assumption is made 2n+1 → n+1

6) The authors make assumptions that their kinetic considerations hold for n>2. What is the evidence?

7) The authors observe hysteresis in median transcription rate as a function of enhancer contact frequency. However, the presented violin plots suggest a presence of two states, one with low and one with high transcription rates. In the intermediate regime of enhancer contact frequency, where authors report hysteresis, the violin plots show bimodal distributions suggesting coexistence of these two states. This would suggest that the system exists in and switches between two distinct states with a discontinuous transition, instead of a continuous hysteretic behavior as suggested by the median behavior.

8) The language of the paper is often not technically precise with qualifiers missing, which could lead to ambiguities and misinterpretations. Here are some examples:

• *p. 1, line 10, "difference in contact across TAD borders is usually less than twofold"
• *p. 1, line 17, "results from recent cohesion disruption"
• *p. 2, line 71, "A simple model of hypersensitivity to changes in contact frequency"

9) On p. 13, line 483, authors define Ostwald ripening as given by weak multivalent interactions; however, Ostwald ripening is a thermodynamic process. In addition, they propose that liquid condensates become larger due to Ostwald ripening, but there are also other processes that may occur, such as coalescence of condensates, which would also lead to larger condensates.

10) At the beginning of the Discussion section authors state they will propose future experiments in each section. However, in some of the sections it is not clear what specifically authors are proposing. These suggestions should be made clearer.

Reviewer #1:

This paper investigates the modulation of spatial signals in higher order visual areas. A number of the findings are novel and interesting, including that signals in higher visual areas are not more influenced by spatial position that signals in V1, that this modulation is not a general feature of the entire visual circuit (i.e. LGN boutons in L4 of V1, as well as LGN units, show very little spatial modulation, and that spatial modulation decreases when mice are watching a replay of tunnel traversals. Overall, I think this paper provides new insight regarding position coding in visual systems. However, there are some points that should be addressed.

1) The imaging data is from mice with different genetic backgrounds, as well as a mixture of gcamp6f and 6s. In addition, different reward protocols were used for different mice. Although the authors state in the methods that none of these factors impact their results, it would be good to include some quantifications to this effect (e.g. they could show the distribution of SMI for 6f data vs 6s data). While I don't expect the major observations to change if it turns out that some of these factors have as systematic effect, it could affect portions of the results where the dataset is split up - for example in the comparison between different higher visual areas, and the observation that spatial modulation appears to vary with receptive field location.

2) The authors state that it is to be expected that LGN neurons respond more strongly in the first half of the corridor due to contrast adaption mechanisms. However, I did not see any quantification that could support this statement?

3) When looking at the spatial modulation index, the authors switch between using median (e.g. Fig 1 and 2) and mean (Fig 4), t-test and rank-sum - and sometimes there is missing information regarding which (mean or median) they are reporting. The authors need to include more detail regarding these statistics.

4) It was not clear to me if the authors are only imaging from layer 2/3 or if they also attempted to image deeper layers.

5) Throughout the paper, the authors use 'firing rate' to refer to deconvolved calcium signal. Although this is stated in the methods, this wording can be misleading, especially since the paper also contains extracellular recordings of spiking activity.

6) It was not clear to me how the dotted lines (e.g. Fig 1 b) were calculated.

Reviewer #1:

This manuscript reports the results of two timing experiments. The experimental paradigm asks participants to judge the time of target items in an unfilled interval between two landmark stimuli. In experiment 1, there is one item that must be judged. In experiment 2, there are two items to be judged. The basic empirical result is that relative order judgments in experiment 2 are more accurate than one might expect from the absolute timing judgments of experiment 1. A model is presented.

My overall reaction is that this paper does not present a sufficiently noteworthy empirical result. I can't imagine that there is a cognitive psychologist studying memory who would be surprised by the finding that relative order judgments in the second experiment are more accurate than one might expect from the absolute judgments in experiment 1. On the encoding side, in these really short lists (with no secondary task), there is nothing preventing the participant from noting and encoding the order as the items are presented (not unlike the recursive reminding). On the retrieval side, we've known for a very long time that judgments of serial position use temporal landmarks (see for instance a series of remarkable studies by Hintzman and colleagues circa 1970).

Methodologically, this paper falls short of the standards one would expect for a cognitive psychology paper. There are basically no statistics or description of the distribution of the effect across participants. Although I'm pretty well-convinced that the basic finding (distributions in experiment 2 are different from experiment 1), I could not begin to guess at an effect size. The model is not seriously evaluated. The bimodal distributions are a large qualitative discrepancy that is not really discussed.

Although the title of the paper invites us to understand these results as telling us something about episodic memory, the empirical burden of this claim is not carried. Amnesia patients (and animals with hippocampal lesions) show relatively subtle differences in timing tasks. There is no evidence presented here, nor literature review, to convince the reader of this point.

Reviewer #1:

This study examines MEG activity in a picture categorization task (decide living or non-living) in a sample of 18 patients with semantic variant PPA, compared to 18 controls. As svPPA is a rare (but scientifically informative) disorder, the sample size is impressive, and given that relatively few MEG studies exist in PPA at all, this is an interesting dataset. The authors show differences in engagement of oscillatory activity, specifically increased low-gamma ERS in occipital cortex and increased beta ERD in the superior temporal gyrus. The authors interpret this as reflecting increased engagement of / reliance on early perceptual mechanisms for completing the task, as opposed to semantic identification of the picture.

Major concerns:

1) My biggest methodological issue with this paper relates to a very old debate in neuroimaging that still comes up all the time: the choice of statistical threshold. Using a high threshold prevents false positives, but may also lead to false negatives, and I fear that is the case here, with the high threshold contributing to an unrealistic impression of spatial specificity in MEG. It is obvious from the average responses in both groups that these oscillatory responses are widespread through the brain. Indeed the alpha and beta responses are significant in the majority of cortical voxels. This basic property of the responses should be presented clearly and prominently in the paper - I don't think it's appropriate to put it in supplementary information where only a minority of readers will even see it. The authors then use what I think is an extremely high and conservative statistical threshold to contrast differences between the two groups. P<.005 uncorrected is a highly conservative threshold already, even before cluster-thresholding is added (although with data as smooth as MEG beamforming solutions, cluster-thresholding is unlikely to change anything). Basically this makes the only the strongest part of the activation survive, and it is valid to conclude that a significant group difference exists there (protected from Type 1 error), but this can give a false impression of the difference is specific to that region. I think a more realistic characterization of the results would involve measuring differences in the strength of the responses between groups on a broader level, possibly the sensors or in large ROIs - and not ROIs pre-selected to show a dramatic difference by first searching the whole brain for the most significant effects - that is the classic "double-dipping" fallacy in neuroimaging.

2) Similarly, the ERD/ERS in each frequency band is treated as a separate entity, ignoring the fact that these bands are arbitrary and frequency is a continuous quantity. This matters because much is made of the fact that PPA participants exhibited greater ERS in the low-gamma range, and that this was correlated with reaction time. Supplementary figure 1 shows that both groups had strong occipital ERS in the high-gamma range, but only PPA showed it in the low gamma range as well. This suggests that the ERS in the PPA group may simply have been shifted to a lower frequency range. A more fulsome characterization of these group differences via time-frequency analysis and/or power spectral analysis would help clarify what is going on here.

3) It is surprising that PPA participants only exhibited increased MEG responses compared to controls - assuming that both gamma ERS and beta ERD can be interpreted as increased neural activation, which is a reasonable assumption based on the literature. No decreases in the PPA group are found, and thus the observed increases can be plausibly attributed to compensatory processes as framed by the authors. However, I am concerned about the role of certain analysis choices in producing this data pattern. In particular, the authors state (line 611): "To remove potential artifacts due to neurodegeneration or eye movement (lacking electrooculograms), we masked statistical maps using patients' ATL atrophy maps (see section MRI protocol and analyses), as well as a ventromedial frontal mask."

It is not clear whether this masking was done in group space from average atrophy maps, or on an individual level. In either case, I don't think this is well justified. I don't know any physical mechanism by which tissue undergoing neurodegeneration can be said to generate an artifactual signal. Atrophied tissue still contains living neurons with ionic currents; these are real signals not artifacts, and furthermore, atrophy is a continuous process with tissue further from the epicenter also undergoing similar neurodegenerative mechanisms. Atrophied tissue may well generate electromagnetic signals that are different from healthy tissue, and such differences should be included in this paper. I think that there may be regions of hypoactivation as well as hyperactivation in this PPA group. If the hypoactivation localizes to atrophied tissue and the hyperactivation to other regions, that will bolster the case that we are seeing compensatory processes, but it isn't certain with half the story masked. I also don't really see statistical masking of the frontal region as a valid solution to eye movement artifacts. The authors would have to present evidence that the region that they masked corresponds to the region potentially affected by eye movements. However, many studies have found that beamforming already does a pretty good job of removing ocular artifacts from estimated brain signals, except for very close to the eyes.

4) The correlation with reaction time in the occipital cortex is consistent with the idea that the ERS there may reflect compensatory overreliance on perceptual information, but it isn't conclusive. The authors suggest that PPA patients are able to categorize the stimuli correctly based on visual features, but are unable to name them. What about testing for correlations with the out-of-scanner behavioural measures that established that the patients have a naming deficit? It would strengthen the case if atrophy or hypoactivation (see comment above) correlated with the naming deficit.

Reviewer #1:

Perez-Ortega and colleagues performed rigorous experiments to determine if the activity of neurons in the visual cortex is similar across days, in particular comparing spontaneous activity in the absence of visual stimuli across days, which was previously not examined to my knowledge. The paper claims that evoked ensembles are more stable than spontaneous ensembles, but more convincing quantitative analyses are required to support these claims.

Major Comments:

1) There is only one mention of prior work with multi-day imaging in the visual cortex (Ranson 2017). Another related study to cite and compare your results to would be Jeon, ..., Kuhlman 2018 (and I think a comment about how similar/different your results are from this study + Ranson would be useful for the reader). I would also recommend mentioning that there are studies that have observed differences in evoked activity across learning in V1 (e.g. Poort, Khan et al 2015; Henschke, Dylda et al 2020). Do you think there was adaptation across days to the stimulus that you repeated?

2) Some GCaMP6f mice have aberrant cortical activity (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5604087/). In the raw data (Fig 1F) it doesn't look present, but it would be useful to show more time and sort the neurons by their first PC weights perhaps to see the activity structure.

3) The approach of 3 plane imaging taking the maximum projection seems useful for tracking cells across days. There is a claim that some cells are no longer found / no longer active. Based on Fig 1G it appears there may have been some Z-movement from day 10 to day 46. This Z movement may explain some of the lost active cells. As a sanity check I would recommend plotting the Z-plane on which the cells were maximally active on day 1 vs the Z-plane on which the cells were maximally active on day n.

4) There is an emphasis on analyzing the data as ensembles but I think this may be missing other slow, gradual changes. The definition of stable is at least 50% of neurons were preserved across days. However, the fitting procedure of finding ensembles may produce different ensembles even if those neurons are still correlated to each other. I would recommend two possible additional analyses: 1) compare the correlation matrices for common neurons across days (unless there are too few neurons for this); 2) look at changes in single neuron statistics across days. For 2) this may include reliability of neural responses to the visual stimuli, the weights of the neuron onto the first principal component of spontaneous activity, or the correlation of a neuron with running speed. I think these results may solidify your ensemble result (evoked-related statistics change less across time).

Reviewer #1:

This study presents a detailed and focused study of the structural basis for a regulation strategy used by a human iron-sulfur cluster biosynthesis system, elucidated by artificial installation of new amino acids into a bacterial system that lacks the allosteric elements of the human enzyme. The work includes quaternary structure analysis and activity assays of variant bacterial proteins. It is performed competently and supports the conclusions. But the focus may be too narrow for a general audience. To bring the work over the bar, the authors could test whether installing the bacterial residues into human NFS1 restores activity without frataxin (inactivated in the human genetic disorder Friedrich's Ataxia). Furthermore, some elements of the study could be presented more clearly/rigorously to communicate the significance of the work to a general audience. These suggestions are listed below.

1) It would be useful for an unfamiliar reader to include a diagram of the bacterial and human iron-sulfur cluster biogenesis pathway. It would also be helpful to depict the mechanism of the IscS/NFS1 cysteine desulfurase reaction - essentially a picture to go along with the description of the PLP-dependent transformations described in paragraph 2.

2) In the first paragraph of the results section - I would be interested to see more details about the selection of the three residues targeted for mutagenesis. For example, did the authors inspect the interfaces of existing crystal structures of these complexes? Did they create sequence alignments for multiple eukaryotic/prokaryotic cysteine desulfurases and select sites conserved in bacterial proteins but not eukaryotic ones? More description of the experimental or bioinformatics basis for selecting these three sites would be important for convincing the reader that the basis for this work is sound.

3) The structural basis for the dimer interaction and the enhanced activity isn't completely clear - how do the changed interactions enhance the enzyme activity? A good description of the different quaternary forms and why they are more/less active is given on page 4-5 - but perhaps another link could be made between the exact residues targeted for substitution and the features of the system important for catalysis.

4) On page 10, the authors describe changes in IscS quaternary structure as a function of concentration. What is the estimated copy number or concentration inside the cell? Which concentration ranges would be most physiologically relevant?

5) Addition of any helper protein appears to increase the proportion of variant IscS dimer and activity. Is there any reason to believe that this phenomenon is simply a crowding effect? If the same amount of an unrelated protein is added - does the activity/dimer fraction change compared to variant IscS alone?

6) I found the color scheme in Figure 1 hard to follow - could the authors keep the subunit colors consistent and use text labels directly on the figure panels for the subunits and forms (open, ready, etc). I also don't think the "Clash!!" labels are necessary. A more effective approach might be to use zoomed-in insets for each clash.

7) In Figures 4-6 - could the authors include a more complete description of the error bars? What kind of error is shown? Are the replicates different experiments done on different days? These presentations might also benefit from showing the actual data points on top of the bars/error bars.

Reviewer #1:

Dingens et al. report a timely complementary study to map neutralizing and binding responses in polyclonal rabbit sera induced by immunization with the BG505 SOSIP Env trimer. Neutralizing responses are mapped using libraries of replication-competent HIV expressing all mutants of the BG505 Env, an approach developed in the Bloom laboratory. Binding responses were mapped using an EM-based method, EMPEM, developed in the Ward laboratory. The Env mutations that affect neutralization of the autologous BG505 strain in the BG505-SOSIP-immunized animals were largely known from other studies, as were the binding (not necessarily neutralizing) responses - the strength of this study is the combination of the two approaches. It is especially useful that the complex datasets have been deposited on-line where they can be interactively explored, including mapping onto Env trimer and monomer structures. Although results were anticipated, it is very nice to directly compare the neutralization epitopes to the binding epitopes determined by EMPEM. This is a well-written and beautifully illustrated paper.

Reviewer #1:

The manuscript by Badhiwala et al. is an interesting study using the emerging model system Hydra, which has many advantages for studying the entire nervous system of an animal during simple behavior. Some of the foundational neuroscience papers in this field have only come out in the past few years, and new studies such as the one here, might have the potential to contribute to an important early literature. Despite clear reasons for enthusiasm, the many shortcomings in this work greatly diminished my enthusiasm and support for this study. Although I appreciate building the microfluidic devise with simultaneous pan-neuronal imaging, the nature of the new biological insights provided here seems quite limited and easily predicted based on prior studies in hydra and other model systems. Moreover, the crude nature of some experiments inhibits my ability to make fair judgement of potential findings.

Major concerns:

1) The pressurized stimulation of the hydra appeared to be specific to the center of the body. The authors don't mention why this region was chosen, which seems critical to this study. Relatedly, why didn't they test multiple areas across the hydra with this system? Might we expect to see different sensorimotor behaviors, and thus different neural outputs?

2) The authors reference a recent single cell study characterizing multiple neuronal cell types in hydra. This work would greatly benefit by using some cell-type resolution studies to determine the functional nature of the neurons being activated as opposed to solely using pan-neuronal GCAMP imaging. If they can put GCAMP in all neurons, why not put it in specific subsets of neurons based on cellular identity? This point becomes more salient because a major take-home from this paper is that the spontaneous behavior and firing patterns is nearly identical to the stimulus evoked patterns, except for an apparent increase in firing rate. The true nature of the mechanosensory response might be revealed with cell-type specific experiments.

3) Although the authors reference whole animal imaging, they focus imaging analysis on peduncle and hypostomal nerve rings, despite the videos showing calcium activity in other areas throughout the body. Moreover, are the authors certain their pan-neuronal genetic strategy equally samples neurons throughout the body? In other words, is the apparent increase in activity in the nerve ring over other areas driven by a technical artifact of these neurons being labeled better?

4) While I appreciate the resection studies to get at "loss-of-function" experiments, this approach seems rather crude, and potentially confounding to clear interpretation. Exactly which neurons are killed and to what extent, and how many, if any began to regenerate throughout this process? My alarm here is raised especially in light of the author's surprising finding that "footless" animals show that the aboral nerve ring is not required for spontaneous or mechanosensory responses. What if residual activity from neurons not ablated is driving this response?

Reviewer #1:

The authors investigated the importance of visual and vestibular sensory cues and the underlying motion dynamics to the accuracy of spatial navigation by human subjects. A virtual environment coupled with a 6-degrees of motion platform, as described in prior studies, allowed precise control over sensory cues and motion dynamics. The research builds on previous work in several important ways: 1) the authors demonstrate that reliance on vestibular cues leads to an undershooting of trajectories to hidden goal locations, 2) manipulation of the underlying motion dynamics (the time constant) during navigation alters the accuracy of trajectories particularly when subjects are reliant on vestibular cues, 3) probabilistic models were used to demonstrate that path integration errors can be explained by mis-estimates of the underlying motion time constants, and 4) time constant estimates were improved when visual cues were available. Overall, the analyses are appropriate, the conclusions are judicious, and the authors provide an important contribution to understanding the sensory mechanisms underlying human spatial navigation.

1) Some minor methodological clarifications: how many trials were performed per subject? How many of the trials were performed in each condition (visual, vestibular, combined)?

2) The study tested performance by both male and female subjects. Could the authors comment as to whether sex differences were observed across performance measures? Perhaps sex can be indicated in some of the scatter plots.

3) Figure 2A. It would be helpful if the authors identified the start-point of the trajectory and also provided more explanation of the schematic in the caption.

4) Figure 2B-C. It would be helpful if the authors could expand this section to show some example trajectories and the relationship between examples and plotted data points. This could be done by presenting measures (radial distance, angular eccentricity, grain) for each example trajectory.

5) Because the range of sampled time-constants can vary across subjects, it would be nice to show plots as in Figure 3B for each subject (i.e., in supplementary material).

6) Discussion. The broader implications of the findings from the models are not sufficiently discussed. In addition, some comparison could also be made to other recent efforts to model path integration error (e.g., PMC7250899).

Reviewer #1:

This manuscript by Gould et al presents highly novel data which is logically presented and is likely to have both clinical and fundamental implications. Of relevance to the bone field, it defines a new mechanism by which one of the most important clinical targets for the treatment of osteoporosis is endogenously regulated. Beyond bone, I am not aware of any other examples of stimulus-directed acute lysosomal degradation of a secreted canonical Wnt antagonist as a mechanism to provide rapid de-repression. What seems lacking is a careful analysis of the physiological consequences of the acute degradation of sclerostin.

1) A landmark paper which convinced many in the field that sclerostin down-regulation is necessary for osteoanabolic responses to loading was based on a transgenic model from the Bellido lab (Tu et al, Bone, 2012). In that study, expression of Sost from the DMP-1 promoter precluded its transcriptional and protein-level down-regulation at late time points. That was sufficient to largely prevent bone gain following loading. Several other groups interpreted this as indicating Sost transcript regulation is required for bone's adaptation to loading, calling into question the physiological relevance of transient post-translational degradation described here. Can the authors reconcile that study with their own?

2) One way the authors attempt to demonstrate in vivo relevance is through western blotting of mechanically loaded mouse ulnas, showing previously-undocumented acute reductions in lysate sclerostin levels. It is standard practice in the field to quantify sclerostin positive osteocytes histologically, rather than by western blotting. This is because mechanical loading can rapidly increase blood flow to the limb (even in this study, the authors implicate the vasodilator NO) as well as having inflammatory effects, diluting the proportion of osteocyte-specific proteins in the lysate. Demonstrating protein-level sclerostin down-regulation specifically in osteocytes rapidly following loading would be a major addition to this study.

3) A long-stranding, reproducible finding which has always been very perplexing is that the largest transcriptomic responses to osteogenic mechanical loading occur very quickly, within an hour of loading, before Sost is down-regulated. Even in UMR106 cells in vitro, B-catenin is stabilised before Sost is down-regulated following exposure to substrate strain. The current findings may explain this temporal discrepancy. The authors should responses to sclerostin degradation such as quantifying Wnt target genes to provide physiologically-relevant readouts of their findings.

4) Figure 3 shows co-localisation of endogenous or ever-expressed sclerostin with lysosomal markers. Does this co-localisation change following FSS or PTH?

5) It is not clear whether early lysosomal degradation which transiently decreases sclerostin is triggered by the same mechanoresponsive pathways which subsequently down-regulate its RNA levels, or whether the two responses are distinct. Can the authors clarify this? For example, does Sost decrease in the BafA1-treated cells 8 hours after FSS or PTH treatment?

6) Discussion "that the rapid and transient nature of sclerostin degradation may be critical to the precise anatomical positioning of new bone formation following an anabolic stimulus" is very unclear. How do the authors propose that lysosomal sclerostin degradation produces regionalised responses to a greater degree than the previously-reported transcriptional mechanisms?

7) The evidence of lysosomal involvement in sclerostin down-regulation is largely based on pharmacological compounds of limited selectivity. A degree of genetic evidence is indirectly provided by the Gaucher cell line, but this is based on a single patient line. Can the authors provide direct genetic evidence that lysosomal function is necessary for sclerostin down-regulation, and ideally for bone formation?

8) References to previous studies which described mechanisms and relevance of Sost down-regulation are sparse. For example, see previous implications of NO signalling from the Vanderschueren lab (Callewaert et al, JBMR, 2010), protein-level down-regulation of sclerostin in the context of ageing from the Price lab (Meakin et al, JBMR, 2014) relevant to the discussion in the current manuscript, as well as work from the Ferrari lab on sclerostin regulation following both PTH and mechanical loading (e.g. Bonnet et al, JBC 2009; Bonnet et al, PNAS 2012).

Reviewer #1:

In this study, Feilong and colleagues showed that hyper-aligned fine-grained cortical connectivity profiles can be used to strongly predict general intelligence in individual participants. This is an important study demonstrating the utility of previously developed connectivity hyperalignment and highlighting the behavioral importance of fine-grained connectivity which is typically ignored in more standard functional connectivity analysis.

1) How does the bootstrapping handle the family structure in the data? More details are needed.

2) The authors mentioned that "the code for performing hyperalignment and nuisance regression was adapted from PyMVPA". One of the most important contributions of this study is the impressive demonstration of prediction performance improvement using hyperalignment and fine-grained connectivity profiles. Therefore, it is important that the adapted code and code utilized for the current study be made publicly available. While connectivity hyperalignment code from the previous study is available in PyMVPA, my experience is that it is not easy to use. If no code from the current study is made available, I believe it will be very difficult to replicate this study.

Reviewer #1:

The manuscript by Allio et al. tries to justify that roadkill can be a useful source for genomic sequencing and even genome assembly level data. The authors cover all aspects of using this resource, from a new protocol to extract DNA, through generating a hybrid short- and long-read genome assembly and to various applications, showing that this data can be used in phylogenomic and population genomic analyses. Although I think that the manuscript is useful in highlighting how this resource can be analysed, it covers a lot of different topics and covers them in varying depth, which makes it difficult to follow and understand the real importance of the different sections.

Major comments:

-Overall, this manuscript left me a bit confused about what is the main scope. It covers a lot of different topics from the laboratory-end of the spectrum, e.g. protocol used to get good DNA out of roadkills and how to assemble these genomes with a hybrid genome assembly, and crossing into a phylogenomic analyses making taxonomic suggestions and an analyses of the complete carnivora group, plus a demographic analyses showing the changes of population size over time.

I was left with an impression that the authors tried to cover a lot of different topics but did not go deep enough in any of those. As a consequence, the results section ends up sounding somewhat shallow, while the discussion takes up a lot of space.

What I would suggest if this manuscript is indeed to serve as a roadmap to roadkill genomics, is to add a figure showing the pipeline and then adjust the structure of the manuscript accordingly. For example, one box in the figure would correspond to one heading in the results/methods, where the DNA analyses is explained - reasoning why a special protocol is needed, what is the main difference to existing methods, how does the yield compare to other methods, etc.

And then the different topics explored in this manuscript could be shown as different examples of the application - taxonomic questions on intra-/inter-species level, higher level taxonomic analyses (of the whole Carnivora), population genomic analyses, etc. Highlighting this as examples of the potential use of the roadkill genomes would make it understandable why this paper is trying to cover aardwolf and bat-eared fox genomics from so many ends.

-Even though showing that roadkill samples can be useful for analysing particular species for which obtaining samples is difficult in other ways, I'm missing a discussion of how difficult it is to obtain roadkill samples and what are the ramifications. Can this approach be generally applied due to legislation reasons, do you need permits, do you find enough roadkill to rely on this source or do you only see it as an opportunistic sampling scheme?

-Genome assembly is not exactly my field of expertise; therefore, I would like the authors to better explain how their hybrid, short- and long-read genome assembly approach is novel. My impression was that such hybrid assemblies are now a rather common and well-established practice. But a lot of space is dedicated to explaining this topic in the introduction and again in the discussion, which to me is something obvious and reads more like a review than a research article. But maybe I'm missing something obvious here, in which case I'd like the authors to make it clearer.

Reviewer #1:

The evidence that sumoylation of K68 in the PIE-1 zinc finger protein is important for HDA-1 type 1 histone deacetylase association and sumoylation seems reasonable, and, is important because as shown in the co-submitted paper HDA-1 sumoylation leads to its association with MEP-1 and LET-418/NuRD complex thus accelerating H3K9ac deacetylation, and silencing gene expression.

The evidence that PIE-1 is needed for sumoylation of HDA-1, presumably through association of PIE-1 with the UBC-9 SUMO E2, is reasonable. However, several aspects of the authors' model remain unclear, and there is an absence of biochemical assays to establish the role of sumoylated PIE-1 in HDA-1 sumoylation, and the effects of sumoylation on HDA-1 HDAC activity.

1) How sumoylation of K68 in PIE1 affects its function was not worked out. Can the deleterious effect of the K68R mutation on PIE-1 function be reversed by generating a SUMO-PIE-1 fusion, as was done for HDA-1 in the co-submitted paper? K68 maps to the N-terminal side of ZF1 in the PIE-1 protein in what appears to be an unstructured region. Does the SUMO residue play a role in the interaction of PIE-1 with HDA-1? Are the zinc fingers required for PIE-1 interaction with HDA-1 or UBC-9? No zinc finger mutations were tested. Does HDA-1 have a SIM that would allow it to interact selectively with sumoylated PIE-1? Another possibility is that the PIE-1 SUMO moiety is important because it interacts with the non-covalent SUMO-binding site on the backside of UBC-9 (Capill and Lima, JMB 369:606, 2007), which might stabilize the interaction. The backside interaction of SUMO with UBC-9 is proposed to promote UBC-9-mediated sumoylation of target proteins with SUMO consensus sites that are directly recognized by UBC-9. In this scenario, SUMO-PIE-1 would in effect be acting as an E3 SUMO ligase for HDA-1 by serving as a recruitment "factor". In this regard, the authors could test biochemically whether recombinant PIE-1 or K68SUMO-PIE-1 stimulates sumoylation of HDA-1 by UBC-9, using recombinant WT and KKRR mutant HDA-1 as substrates. These issues deserve discussion.

2) What is the SUMO E3 ligase that sumoylates PIE-1? Is it possible that through association with UBC-9, perhaps through its zinc fingers, PIE-1 is sumoylated in cis within a PIE-1/UBC-9 complex?

3) In many places, including the title, the authors make the claim that PIE-1 promotes sumoylation and activation of HDA-1. While it is clear that PIE-1 does increase sumoylation of HDA-1, in a manner requiring K68, and that H3K9ac levels are decreased as a result, the authors do not provide any direct evidence that this process increases HDA-1 catalytic activity, as is implied in the title and elsewhere. As indicated in the review of the co-submitted paper, this would need to be established by carrying out an HDAC assay on control and sumoylated HDA-1 in vitro. Instead of enzymatic activation, it is possible that the PIE-1 interaction and HDA-1 sumoylation results in relocalization of HDA-1 within the nucleus to facilitate more efficient H3K9ac deacetylation.

Reviewer #1:

The evidence that sumoylation of HDA-1, a type 1 HDAC, plays a key role in establishing transcriptional silencing of piRNA-regulated genes in C. elegans is quite convincing. The genetic analysis demonstrating that the SUMO pathway is involved in piRNA silencing is strong, and the mutational evidence that this involves sumoylation of two Lys in the tail of HDA-1 is reasonable. Likewise, the finding that HDA-1 sumoylation promotes association with NuRD complex components and association of MEP-1, an HDA-1 interactor, with chromatin regulators is convincing. In addition, the evidence that HDA-1 sumoylation increases H3K9ac deacetylation in vivo, leading to negative regulation of hundreds of target genes, and plays a role in the inherited RNAi pathway is solid.

While the overall conclusion provides an interesting advance in understanding mechanisms of piRNA-mediated gene silencing in C. elegans, the paper is lacking any biochemical analysis of the effects of sumoylation on HDA-1 activity and its association with other transcriptional regulators.

1) The authors mapped two sumoylation sites close to the C terminus of HDA-1, K444 and K459, based on extremely weak homology with two established sumoylation sites in human HDAC1 that are reported to be important for transcriptional repression (N.B. the authors should indicate here that David et al. reported that K444/476R HDAC1 had reduced transcriptional repression activity in reporter assays.). While the two human sites conform to the sumoylation site consensus, ψKXE, neither K444 nor K459 in HDA-1 fits this consensus (possibly one could argue that K444 is in an inverted motif). The fact that the KKRR mutant HDA-1 is no longer sumoylated is consistent with these two Lys being sumoylated, but it would be reassuring to have direct MS evidence that K444 and K459 are indeed sumoylated, which could be achieved using a SUMO Thr91Arg mutant that generates a GlyGly stub upon trypsin digestion, among other methods.

2) It remains unclear how sumoylated HDA-1 is recognized by MEP-1 for assembly into the NuRD complex. Does MEP-1, or another NuRD subunit, have a SIM that could facilitate direct interaction of MEP-1 and sumoylated HDA-1?

3) As the authors discuss, it is surprising that the HDA-1(KKRR)::SUMO protein, which in effect is a constitutively sumoylated form of HDA-1 that will interact constitutively with MEP-1/NuRD, does not have more deleterious effects on the organism, since according to the data in Figure 2B, the stoichiometry of endogenous HDA-1 sumoylation was extremely low. Of course, low sumoylation stoichiometry, which is a general issue with sumoylation studies, means that only a very small fraction of the HDA-1 endogenous population will be able to engage with the silencing complexes at any one time. This point is also worth discussion.

4) Page 5: Here, and elsewhere, the authors claim that sumoylation of the two C-terminal Lys activates HDA-1 histone deacetylase activity, but provide no direct evidence for this statement. There are no HDAC assays, and it is unclear how C-terminal SUMO residues distant from the catalytic domain would alter its enzymatic activity, unless there is a SIM motif in HDA-1 that might allow for intramolecular interaction with SUMO residues at the tail leading to a conformation change. Did the authors check for a SIM motif in HDA-1? The fact that adding SUMO to the C-terminus rather than one or both of the two Lys would also have to be taken into account in determining bow sumoylation might "activate" HDA-1. To demonstrate that sumoylation activated HDA-1 in vitro deacetylation assays would need to be carried out comparing the activities of unmodified and sumoylated HDA-1. Instead of enzymatic activation, it is possible that the PIE-1 interaction and HDA-1 sumoylation results in relocalization of HDA-1 within the nucleus to facilitate more efficient H3K9ac deacetylation.

Reviewer #1:

In this manuscript, Soucy and colleagues present a novel innervated system which they use to model the effects of prenatal nicotine and opioid exposure. Using the system they provide potentially interesting insights on how prenatal nicotine and opioid exposure could impact release of catecholamines. However, following careful review of the manuscript,I recommend that the authors provide substantial additional data and evidence to support the biological relevance of their findings.

Major points:

1) A main pillar of this manuscript is the assumption that the adrenal medulla is innervated. To substantiate their claims the authors cite books/book chapters, rather than citing convincing primary evidence. In fact, other than old EM images showing vesicular densities akin to synapses, I have not found published images of convincing axonal arborization in the adrenal medulla - if such images exist the authors should at least try to reproduce them for internal consistency of their study. This is particularly relevant if they wish to draw parallels between in vitro and in vivo systems. As this is a major pillar upon which this research stands, the lack of supporting histological evidence, which could be easily done, undermines the validity of this manuscript. Presenting primary evidence (i.e. not a textbook diagram) is essentia.

2) Multiple experiments lack appropriate controls. See comments on Figure 2B, 2D, Supplementary Figure 2.

Reviewer #1:

The authors report a model about the confidence-effort tradeoff; explaining how subjects invest effort depending on how confident they want to be in their decision (and how costly this is). They fit their model to behavioural data and report qualitative similarities between model and data.

I find this an interesting model, with interesting links between timely topics of interest, such as confidence, effort, and cost optimisation. But I have several requests for clarification.

Major Comments:

Line 274: Without loss of generality: what does it mean here? I guess that with a different cost function, not all conclusions remain the same?

The model assumes that it is "rewarding" to choose the correct (highest-value) option (B = R*P). But is this realistic? If the two options have approx the same value, then R should be small (it doesn't matter which one you choose); if the options have different values, it is important to choose the correct one. Of course, the probability P_c continuously differentiates between the two options, but that is not the same as the reward. Can the predictions generalise toward a more general R that depends on value difference?

In Figure 2, I guess that the important quantity to decide is a standardised delta-mu (similar to d' in signal detection theory). It might be useful to also plot that (essentially combining the current two plots). Or alternatively, plot P_c(z), which relates more directly to the theory.

The section Probabilistic model fit is unclear. Are the MCD variables y the 5 variables mentioned above? Do different y's share the same alpha, beta, gamma? Are different transformation parameters a and b fitted for each y? Is estimation done per subject? It is mentioned that VBA is used, but what distribution is approximated exactly using VBA? Is it a mean-field approximation, optimised with gradient descent? Is the goal function a posterior across the 5 parameters? It would also be good then to have an intuition on the estimated model parameters (e.g., their standard error or Bayesian equivalent). Is there an estimate of model fit (in addition to checking qualitative predictions)? Figure S3 is a good start (and I think it is worth putting in the main MS), but it would be nice, for example, to see model comparisons where one or more parameters are restricted.

Figure 4, 5, 6 should be better annotated. I have a hard time trying to fill in what is plotted exactly (eg, scale of the color bar). Why are the data grouped in percentiles? Also in Figure 4 legend, I guess that "beta" is not used as the MCD model parameter? Please avoid overloading definitions.

Figure 7: It seems that "spreading" of alternatives occurs in the model only for alternatives that are initially close together? Is this consistent with their discussion around equation (14)? (I may be overlooking something; if so, consider making this more explicit.)

I find it a really interesting feature of the model that it can explain spreading of alternatives from a statistical perspective. So I think it's worth commenting on it in the Discussion. For example, does the current model capture trends in the literature? To what extent is the effect (also in empirical data) dependent on initial value differences?

Reviewer #1:

This paper attempts to explain perinatal risk factors and the associated risk of developing pediatric asthma in the mid-childhood and early teenage years. The authors found that some maternal characteristics such as atopy, BMI, race/ethnicity and demographics such as newborn sex, and birth characteristics such as birthweight, gestational age, and mode of delivery were associated with risks of subsequent asthma development in the pediatric population. The paper then goes on to demonstrate the differences in immune response during the different time frames of pregnancy. Throughout the majority of the pregnancy, fetal hematopoiesis generates mostly lymphoid and erythroid lineages. Towards term, the immune cells are predominantly neutrophils and monocytes. Pre-term is characterized primarily by lymphocytes. It was seen during term deliveries that the myeloid response produces several cytokines that shift CD4+ T- cells away from the Th2 response. Enhanced production of IFN gamma by leukocytes stimulation early in life is associated with reduced susceptibility to infections. However, the author states that these findings do not extend to asthma diagnosis in childhood.

Major comments:

I would have liked the paper to readjust the introduction; a lot of emphasis is placed on IFN/infection/asthma, but after this fact, it seems neglected going forward and the paper explores another topic. Instead, the paper's focus was on determining the biological nature, serologically, with a granulocytic luminal marker (PGLYRP-1) and a membrane-bound marker (sIL6Ra) and its association to pediatric asthma.

The take-home message for the paper - that there appears to be an inverse relationship between serum levels of PGLYRP-1 and overall risk for pediatric asthma - should be explored in relation to the whether a therapeutic role for such proteins is possible since they can accurately predict risk factors for disease and assess pulmonary function. Other proteins, like the sIL6Ra, have no association with disease predictability and have no association with predicting pulmonary outcomes. This should be explored/explained in greater detail.

Minor comments:

As part of the validation efforts of the study - the rationale for using three different cohorts to assess pediatric asthma risk was not clearly explained.

One of the main findings of the analysis was the conclusion that patients with higher levels of myeloid cells in their CBMCs are at lower risk of developing pediatric asthma, and vice versa. Furthermore, CBMC neutrophil abundance was negatively associated with the number of risk factors. (patients with more risk factors, as mentioned above, were found to have lower levels of neutrophils in their CBMC, and more at risk of pediatric asthma). This was further elucidated with measuring CBMC plasma levels of PGLYRP-1 with levels of mRNA and correlating it with risk of developing pediatric asthma. Increased levels of mRNA for the PGLYRP-1 protein was associated with an increased serum concentration of the protein. However, this was inversely correlated with risk factors. Patients with reduced risk factors for development of pediatric asthma were found to have increased levels of the protein and its mRNA.

The measurement and correlation of PGLYRP-1 (present in neutrophil specific granules) and sIL6Ra (derived from neutrophils, but not present in granules) to pediatric asthma at mid-childhood and early-teen years was determined. There were two follow-up points where asthma outcomes and pulmonary function by way of the FEV1/FVC ratio was determined. It was found that increased levels of PGLYRP-1 were significantly associated with current asthma at mid-childhood. However, there was no association between levels at the early-teen follow-up.

In terms of correlations between each protein level and pulmonary function - the sIL6Ra protein was NOT associated with the FEV1/FVC ratio or a bronchodilator response at either age group. However, it was found that increased levels of PGLYRP-1 were associated with an INCREASED FEV1/FVC ratio (not indicative of asthma) and reduced odds of developing pediatric asthma at each age group.

This analysis makes sense as increased production of neutrophil granules, PGLYRP-1, serves a protective effect against infection, reducing incidence of disease states. The paper, however, should explore the rationale behind the no-response to the sIL6Ra protein. In terms of understanding, since this protein is NOT associated with neutrophilic granules, it can be inferred, that is it may not have a role in protecting against infection. However, this could have been explored in more detail in the paper.

Reviewer #1:

A very interesting paper testing the biological embedding model in a wild long-lived mammal using an impressive dataset. However, the results for immature orphans are not entirely straight forward. The effect on the HPA axis is in the opposite direction to humans and there seems to be no significant increase in cortisol compared to non-orphans overall - it depends on time since maternal loss. The paper would be improved by communicating this more clearly and discussing exactly why this pattern may be different to that in humans. Some of the evolutionary ideas discussed in the paper also need to be more clearly conveyed or thought through.

Substantive concerns:

1) There are important sections in the introduction (L125-128 particularly) and discussion (L403-409) about the evolution of the HPA response and differences between humans and other mammals that are unclear. Greater detail on the evolutionary logic being used, the precise hypotheses being suggested and references to back the ideas up are required (further details in minor comments).

2) Table2/Model 1a doesn't directly test whether orphans have higher cortisol than non-orphans (or no p-value reported in table 2) and CIs in table 1 suggest that there is not a significant difference. Therefore, categorical statements that orphans have higher cortisol levels don't seem to be entirely justified. However, model 1B demonstrates that cortisol declines with years since maternal loss and figure 3 supports the idea that orphans do have higher cortisol than non-orphans in the first 2 years following maternal loss but that this declines to levels similar to those of non-orphans after 2 years. Could a statistical test be run to back this up? Perhaps instead of using a binary variable for orphan status (yes/no) it could be analysed as categories (orphaned within 2 years, orphaned more than 2 years ago, not orphaned as an immature) which could be used to directly test this and back up statements e.g. recently orphaned immatures had higher cortisol levels than non-orphans. A broader concern is why likelihood ratio tests have been used to calculate p values (and for only some of the predictors) rather than reporting the output from the models themselves. Could you explain what the benefit of this is over reporting values from the actual models and/or also provide the model outputs?

3) The effect on cortisol slopes found in this study is in the opposite direction to that in humans. This is discussed in some detail but is lacking clarity in places and I think it would help to make this difference more obvious - it is really a key finding of the paper not a secondary point. The expected pattern is very nicely set out in the introduction so it would be good to format the discussion so there is a paragraph that outlines exactly how the results differ from hypothesized:

(a) that the effect on cortisol slopes is in the opposite direction

(b) that only the cortisol levels of recently orphaned immatures are significantly different to non-orphan immatures and then brings in the ideas discussed about why these differences may be present. I think this would really help communicate the findings more clearly, bringing the discussion more inline with what is set out in the introduction.

Reviewer #1:

This is overall a well written and methodologically sound study researching how educational achievement can be predicted using genomic data when the sample is stratified to those without and those with diagnoses of common psychiatric disorders. I think that it is a very important study area, the study is well powered using a fantastic representative sample and offers some insights into aetiology of associations between psychiatric traits and educational achievement.

I suggest some minor adjustments for the authors to consider, mainly addressing the conclusions and implications of the findings. I also recommend some clarifications in the methods and the results sections; these suggestions might require some very modest additional analyses and rethinking/rewording some of the conclusions.

• The major issue I have is that you discuss family SES as a purely environmental factor throughout the manuscript. However, we know that this is not the case and that there is substantial heritability for SES. It follows from what SES composite is made out of, in your case parental education and occupation, both of which are highly heritable (as you rightly note in the manuscript yourself). This needs to be addressed and discussed throughout the manuscript.

• The major conclusion in the manuscript, even if you acknowledge that this is speculation, is that the attenuation of the association between EA-PGS and school grades after correcting for SES can be explained by genetic nurture. I agree, this can be one of the explanations, however, here you also control (partially) for transmitted genes, that is educationally related genetic variants present in both generations (so without genotyped trios here you cannot distinguish between direct and indirect genetic effects). In addition, this attenuation can also be explained by gene and environment correlation (not only passive which is addressed by genetic nurture hypothesis) but also active and evocative rGE. In addition, in your design, you need to consider assortative mating. I suggest directly addressing this in the manuscript.

• I also think that you should address that you are dealing with diagnosed disorders only. It is a great strength of the paper, and you are using a fantastic resource, but we know that these disorders are quantitative traits and your study does not allow to take that into account, so there are possibly individuals with high ADHD symptoms are included in the control group; similarly, you cannot take into account the symptom severity. In terms of symptom level data, I see you have referenced Selzam et al., 2019 paper that, among other things, related EA-PGS to ADHD symptoms and vice versa, and also controlled for SES.

• In the introduction, you rightly state that individual differences are explained by genetic and environmental factors and the interplay between them, however, I suggest rephrasing it, because "much of the variance can be explained" is incorrect, all of the individual differences can be explained by the combination of these factors.

• You report low rG between schizophrenia and E1, can you specify how this was calculated

• You state that your prediction in the control sample is lower than the other studies and offer a possible solution of the inclusion or exclusion of 23andMe data in the summary statistics, please note that other studies have not used 23ndme statistics either (for example TEDS publications). You also discuss genetic heterogeneity; I think that the difference can be explained by both genetic and environmental heterogeneity. What is the rG between EA in your sample and GWAS sample?

• I think that the conclusion that the impact of low EA-PGS is comparable to the impact of ADHD is too strong, your data does not support this strong conclusion. I suggest rephrasing it, especially as we're not aware of the associated mechanisms. Note that people with ADHD in your sample also have lower EA-PGS compared to control conditions. In addition, symptom severity of ADHD varies greatly.

• I also do not agree with the statement that having wealthy parents does not boost the performance as much for children with ADHD as compared to children without for the reasons mentioned above.

• I think that you have fantastic data, and you have data available about how many of your participants have multiple diagnoses. I suggest adding a stratified group with multiple diagnoses to the analyses, that is adding groups with 2, 3 or 4 and more psychiatric diagnoses and checking their polygenic score prediction to EA.

• I suggest making it clearer what covariates were used in every analysis (you say first that you added psychiatric diagnoses as covariate among the usual covariates, but later only that covariates were included 'as before', I assume you did not include diagnoses in later analyses, but this is not clear). In addition, it is not clear to me why you control for psychiatric diagnoses in the first set of analyses, I would have wanted to see full results without this covariate.

Overall, this is a beautiful study and it was a pleasure to read/review it.

Terapi Oksigen Hiperbarik (HBOT) semakin sering digunakan di berbagai bidang medis, perawatan, dan praktik kesehatan. Menjadi intervensi penting dengan mekanisme tindakan yang tidak dipahami dengan baik. Terapi Oksigen Hiperbarik adalah salah satu metode p engobatan yang dilakukan dengan menyediakan 100% oksigen murni yang dihirup oleh pasien di ruangan khusus dengan udara bertekanan tinggi. Tekanan udara yang meningkat pada ruang Hiperbarik menyebabkan paru pasien menyerap lebih banyak oksigen daripada bias anya, yang dapat membantu menyembuhkan berbagai penyakit. Diharapkan adanya kajian ilmiah, ulasan dan diskusi tentang terapi heperbaric dan pencarian literatur tentang penggunaannya dapat bermanfaat bagi tim medis baik perawat, dokter, pekerja kesehatan la innya dan masyarakat, sehingga mereka dapat meningkatkan pengetahuan, berdasarkan fisiologi, patologi, fisika, farmakologi, manfaat, indikasi dan perawatan tentang terapi hiperbarik sehingga dapat diterapkan dalam berbagai bidang yang diperlukan.

Ruang Hiperbarik Ruang hiperbarik dapat terdiri dari dua jenis: tunggal atau ganda. Sementara tekanan terjadi di tempat duduk tunggal melalui oksigen dan peningkatan tekanan bersifat sistemik, ruang multiplace diberi tekanan dengan udara dan oksigen disuplai kepada pasien melalui masker, helm, atau tabung endotrakeal, tergantung kasusnya. (Gill & Bell, 2004)

Indikasi Terapi Oksigen Hiperbarik Penting untuk mengetahui indikasi terapi hiperbarik. Indikasi meliputi penyakit dekompresi, emboli udara, keracunan karbon monoksida, cedera, anemia kehilangan darah akut, abses intrakranial, luka bakar termal, fasciitis nekrotikans, gas gangren, dan kehilangan pendengaran akut.

Indikasi Terapi Oksigen Hiperbarik menurut (Mathieu et al., 2017) Keracunan karbon monoksida (CO) Keracunan karbon monoksida dapat terjadi ketika seseorang menghirup gas karbon monoksida yang menyebabkan penyerapan oksigen oleh darah terganggu. Terapi oksigen hiperbarik dapat mengatasi kondisi ini dengan cara menghilangkan karbon monoksida dari dalam darah dengan pemberian oksigen murni bertekanan tinggi. • Merekomendasikan HBOT dalam pengobatan keracunan CO (rekomendasi Tipe 1, bukti Level B). • Merekomendasikan 100% oksigen segera diterapkan pada orang yang keracunan CO sebagai pengobatan pertolongan pertama (rekomendasi Tipe 1, bukti Level C). • Merekomendasikan HBOT untuk setiap orang yang keracunan CO yang disertai dengan adanya perubahan kesadaran, tanda- tanda klinis gangguan neurologis, jantung, pernapasan atau psikologis dan tingkat karbokshaemoglobin pada saat masuk rumah sakit • Merekomendasikan HBOT pada wanita hamil yang keracunan CO apa pun gejala klinis mereka dan tingkat karboksihemoglobin saat masuk rumah sakit (rekomendasi Tipe 1, bukti Level B). • Sebaiknya merawat pasien dengan keracunan CO minor baik dengan oksigen normobarik 12 jam atau HBOT (rekomendasi Tipe 3, bukti Level B). • Tdak merekomendasikan perawatan dengan pasien tanpa gejala HBOT yang terlihat lebih dari 24 jam setelah akhir paparan CO (rekomendasi Tipe 1, bukti Level C).

Penyakit Dekompresi (DCI) Penyakit dekompresi merupakan kondisi yang terjadi pada saat aliran darah di dalam tubuh terhambat, dikarenakan perubahan tekanan udara. Perubahan tekanan ini dapat terjadi akibat penerbangan, menyelam, atau hal lain yang mengakibatkan terjadinya perubahan tekanan udara secara drastis. Perubahan tekanan udara di luar tubuh yang tiba-tiba dapat menyebabkan timbulnya gelembung udara di dalam pembuluh darah atau emboli. Terapi oksigen hiperbarik dapat mengecilkan gelembung di dalam pembuluh darah akibat perubahan tekanan. 186 p-ISSN: 2083-0840: E-ISSN: 2622-5905 Volume 11, Nomor 2, Desember 2019 • Merekomendasikan HBOT dalam pengobatan DCI (Rekomendasi Tipe 1, bukti Level C). • Merekomendasikan 100% normobarik oksigen pertolongan pertama (rekomendasi Tipe 1, bukti Level C). • Merekomendasikan resusitasi cairan intravena dengan larutan kristaloid yang tidak mengandung glukosa (Rekomendasi Tipe 1, bukti Level C). • Merekomendasikan tabel terapi kompresi HBOT⁄ (Tabel Perawatan Angkatan Laut AS 6 atau helium / oksigen (Heliox) Comex Cx30 atau yang setara) untuk pengobatan awal DCI (Rekomendasi Tipe 1, bukti Level C). • Merekomendasikan tabel pengobatan HBOT yang sesuai untuk manifestasi residual DCI (rekomendasi Tipe 1, bukti Level C). • Merekomendasikan penggunaan heparin dengan berat molekul rendah untuk profilaksis trombosis vena dalam untuk kasus DCI yang lumpuh atau lumpuh (rekomendasi Tipe 1, bukti Level C). • Menyarankan penggunaan tabel lignocaine (lidocaine) dan rekompresi Heliox untuk DCI neurologis yang serius (rekomendasi Tipe 2, bukti Level C). • Menyarankan tenoxicam oral (atau NSAID serupa) untuk kasus DCI yang dipilih dengan tepat (Rekomendasi Tipe 2, bukti Level B).

FISIOLOGIS, DAN FARMAKOLOGIS GAS HIPERBARIK 194 Di permukaan oksigen plasma adalah 3 ml/l. Jaringan saat istirahat membutuhkan sekitar 60 ml oksigen per liter aliran darah (dengan asumsi perfusi normal) untuk mempertahankan metabolisme seluler yang normal, meskipun persyaratan bervariasi di antara jaringan. Pada tekanan 3 atmosfer (304 kPa) oksigen terlarut mendekati 60 ml/l plasma, yang hampir mencukupi untuk memasok kebutuhan oksigen total istirahat dari banyak jaringan tanpa kontribusi dari oksigen yang terikat dengan hemoglobin. Ini memiliki keuntungan dalam situasi seperti keracunan karbon monoksida atau anemia berat di mana sulit melakukan crossmatching atau keyakinan agama mencegah transfusi darah (Leach et al., 1998).

Fungsi HBOT Secara umum dapat dibagi menjadi dua jenis efek, fisiologis dan farmakologis, kadang terjadi tumpang tindih. Oksigen dapat dianggap sebagai unsur alami yang penting untuk kehidupan, dan sebagai obat yang digunakan untuk mengubah patologi penyakit. HBOT menggunakan oksigen sebagai obat dan oleh karena itu, memiliki protokol dosis yang tepat, indeks terapi, dan efek samping yang perlu dipahami agar dapat digunakan dengan aman dan efektif

Efek Fisiologis Dalam kondisi normal di permukaan laut, udara terdiri dari sekitar 21% oksigen yang menghasilkan tekanan oksigen alveolar (PAO2) sekitar 100 mmHg. Dalam kondisi ini, hemoglobin plasma hampir seluruhnya jenuh, dan oksigen plasma terlarut minimal.Oleh karena itu, dengan asumsi konsentrasi hemoglobin 12 g/dL, kandungan oksigen darah gabungan dalam seluruh darah adalah sekitar 16,2 mL O2/dL. Dalam kondisi hiperbarik yang menghirup oksigen 100% pada 3 atmospheric absolut (ATA), nilai PAO2 meningkat menjadi sekitar 2280 mmHg; dan menurut hukum Henry, kandungan oksigen gabungan dalam darah lengkap meningkat menjadi 23,0 mL O2 / dL. Peningkatan 42% dari baseline ini hampir seluruhnya berasal dari peningkatan oksigen yang terlarut dalam plasma. Peningkatan pasokan oksigen dan tekanan oksigen arteri membentuk dasar HBOT (Lambertsen, 1988; Oh et al., 2008; Rothfuss & Speit, 2002)

Terapi Oksigen hiperbarik fungsi HBOT sangat kompleks. Akan mengurangi ukuran gelembung gas dalam cairan (darah). Sehingga meningkatkan kapasitas pembawa oksigen darah melalui peningkatan konsentrasi oksigen plasma menjadi sekitar 7%. Adanya bakteriostatik dan bakteriosidal pada tekanan dan oksigenasi yang lebih tinggi. Oksigen hiperbarik akan meningkatkan neovaskularisasi arteri dan mengurangi edema jaringan, yang akan menghambat berbagai eksotoksin seperti racun alfa dan beta yang terkait dengan infeksi nekrotikans. Pengobatan hiperbarik akan meningkatkan difusi oksigen lebih lanjut dalam jaringan dengan jarak sekitar empat kali jarak perfusi normal. Sehingga akan menyebabkan terjadi difusi oksigen dari lingkungan yang kaya oksigen ke lingkungan oksigen yang buruk seperti dengan luka iskemik dan anggota badan. Hukum Boyle adalah dasar untuk efektivitas dalam penyakit dekompresi dan emboli udara. Permukaan terlalu cepat dari penyelaman bawah laut yang dalam akan menghasilkan presipitasi gelembung nitrogen dalam darah. Ini akan menghasilkan persendian yang sangat menyakitkan, tikungan, dan bahkan kematian. (Fife et al., 2016; Jones & Wyatt, 2019). Tujuan pengobatan adalah untuk mencegah pembentukan gelembung nitrogen sehingga berkurang ukurannya dan kembali larut. Hal yang sama berlaku untuk perawatan emboli udara. Peningkatan tekanan yang diberikan oleh terapi medis hiperbarik akan mengurangi gelembung gas tersebut.

BAHAYA DAN KONTRAINDIKASI Terapi oksigen hiperbarik kontraindikasi mutlak untuk perawatan hiperbarik adalah pneumotoraks yang tidak diobati. Kontraindikasi relatif lainnya adalah jika pasien menggunakan agen kemoterapi tertentu seperti Adriamycin dan Cisplatinum atau Antabuse. Masalah lain yang menjadi perhatian adalah pasien berventilasi, pasien dengan hipertensi yang tidak terkontrol, dan penderita diabetes. Masalah dengan pasien berventilasi adalah varian dalam volume udara dan tekanan dan masalah barotrauma. Gula darah serum sering jatuh saat menyelam. Oleh karena itu, disarankan untuk memastikan glukosa serum pada pasien dengan diabetes berada pada sisi yang tinggi sebelum menyelam (Cho et al., 2018). Efek samping negatif dari menerima O2 bertekanan, akan terjadi cedera stres oksidatif, kerusakan DNA, metabolisme seluler, pengaktifan koagulasi, disfungsi endotel, neurotoksisitas akut, dan toksisitas paru, gangguan metabolisme sel, mengaktifkan koagulasi, disfungsi endotel

Definisi Terapi Oksigen Hiperbarik (HBOT)

Terapi Oksigen hiperbarik adalah suatu terapi dengan pemberian oksigen konsentrasi 100% dan tekanan lebih dari 1 atmosfer absolut (ATA), yang di lakukan di ruang udara bertekanan tinggi/ruang hiperbarik dengan tekanan lebih dari 1 atmosfer. Tujuan terapi oksigen hiperbarik untuk perawatan dan pengobatan beberapa penyakit seperti emboli intravaskuler, dekompresi, infeksi aneorob, dan keracunan CO.

Ruang Hiperbarik

Ruang hiperbarik dapat terdiri dari dua jenis : tunggal atau ganda, perbedaan tunggal dan ganda

Indikasi Terapi Oksigen Hiperbarik

Pada umumnya pusat hiperbarik merawat pasien dengan kondisi non alergi seperti penyembuhan luka yang buruk , cedera radiasi yang tertunda, osteomielitis kronis dan flap. Menurut UHMS indikasi terapi oksigen hiperbarik adalah: emboli atau keracunan gas karbon monoksida, keracunan sianida, inhalasi asap myostitis, dan mionekrosis klostridial. Cedera;sindrom kompartemen, dan iskemia perifer akut lainnya. Penyakit dekompresi; Peningkatan penyembuhan pada luka; Anemia kehilangan darah yang banyak; Abses intrakranial; Infeksi jaringan lunak nekrotikans; Osteomielitis refraktori; Flap dan cangkok kulit (terganggu); Cedera radiasi (jaringan lunak dan nekrosis tulang); Luka bakar termal.

Dasar Fisiologis Terapi Oksigen Hiperbarik

Efek HBOTdidasarkan pada regulasi gas, dan efek fisiologis dan biokimia dari hiperoksia.Hukum Boyle menyatakan bahwa pada suhu konstan, tekanan dan volume gas berbanding terbalik. Ini adalah dasar untuk semua terapi hiperbarik. Hukum Boyle menjelaskan tentang hubungan tekanan gas dan volume gas. Tekanan gas berbanding terbalik dengan volume gas. Bila tekanan semakin besar maka volume akan semakin kecil. Prinsip ini digunakan pada kasus-kasus penyakit dekompresi dan emboli gas. Pada penyakit dekompresi, terjadi gelembung-gelembung nitrogen (nitrogen bubbles) sehingga terjadi penyumbatan pembuluh darah akibat gelembung ini.

Mekanism HBOT

Prinsip dari terapi oksigen hiperbarik adalah membantu tubuh untuk memperbaiki jaringan yang rusak dengan meningkatkan aliran oksigen ke jaringan tubuh. Terapi oksigen hiperbarik akan menyebabkan darah menyerap oksigen lebih banyak akibat peningkatan tekanan oksigen di dalam paru-paru yang dimanipulasi oleh ruangan hiperbarik. Dengan konsentrasi oksigen yang lebih tinggi dari normal, tubuh akan terpicu untuk memperbaiki jaringan yang rusak lebih cepat dari biasanya. Terapi oksigen hiperbarik (HBOT) memberikan oksigen di bawah tekanan untuk meningkatkan kadar oksigen jaringan.Oksigen diberikan 2-3 kali lebih tinggi dari tekanan atmosfer, dan didistribusikan di sekitar area yang terinfeksi;sehingga memungkinkan terjadinya proses penyembuhan alami tubuh dan memperbaiki fungsi jaringan.

Fisiologis Dan Farmakologis Gas Hiperbarik

Dalam kondisi normal di permukaan laut, udara terdiri dari sekitar 21% oksigen yang menghasilkan tekanan oksigen alveolar (PAO2) sekitar 100 mmHg.Dalam kondisi ini, hemoglobin plasma hampir seluruhnya jenuh, dan oksigen plasma terlarut minimal.Oleh karena itu, dengan asumsi konsentrasi hemoglobin 12g/dL, kandungan oksigen darah gabungan dalam seluruh darah adalah sekitar 16,2 mL O2/dL.Dalam kondisi hiperbarik yang menghirup oksigen 100% pada 3 atmospheric absolut (ATA), nilai PAO2 meningkat menjadi sekitar 2280 mmHg;dan menurut hukum Henry, kandungan oksigen gabungan dalam darah lengkap meningkat menjadi 23,0 mL O2 / dL.Peningkatan 42% dari baseline ini hampir seluruhnya berasal dari peningkatan oksigen yang terlarut dalam plasma.Peningkatan pasokan oksigen dan tekanan oksigen arteri membentuk dasar HBOT. HBOT telah terbukti meningkatkan produksi faktor pertumbuhan endotel vaskular (VEGF), varian faktor pertumbuhan turunan trombosit (PDGF), dan faktor pertumbuhan fibroblast (FGF) sebagian melalui modulasi nitrat oksida.VEGF dan PDGF bertanggung jawab untuk merangsang pertumbuhan kapiler dan granulasi luka, dan melakukannya dengan mengubah jalur pensinyalan yang mengarah pada proliferasi dan migrasi sel.FGF memainkan peran yang sama dalam angiogenesis, tetapi juga menginduksi perkembangan saraf, organisasi keratinosit, dan proliferasi fibroblast di lokasi luka yang mengarah ke granulasi dan epitelisasi.Oksigen juga memiliki efek antibakteri di lokasi luka.Ketika neutrofil dan makrofag memasuki lingkungan ini untuk membunuh bakteri dan menghilangkan bahan nekrotik, mereka mengkonsumsi oksigen dalam jumlah besar.Oksigen kemudian digunakan oleh sel-sel ini untuk membuat hidrogen peroksida, anion superoksida, asam hidroklorat, dan radikal hidroksil.

Kontraindikasi Hiperbarik

Efek samping negatif dari menerima O2 bertekanan, akan terjadi cedera stres oksidatif, kerusakan DNA, metabolisme seluler, pengaktifan koagulasi, disfungsi endotel, neurotoksisitas akut,dan toksisitas paru, gangguan metabolisme sel, mengaktifkan koagulasi, disfungsi endotel, neurotoksisitas akut dan toksisitas paru. Risiko potensial dan rasio risiko-manfaat dari oksigen hiperbarik sering kurang ditekankan dalam uji coba terapeutik.Efek sampingnya sering ringan dan reversibel tetapi bisa parah dan mengancam nyawa.Secara umum, jika tekanan tidak melebihi 300 kPa dan lamanya pengobatan kurang dari 120 menit, terapi oksigen hiperbarik aman.

A.Definisi Terapi oksigen hiperbarik (HBOT) Terapi Oksigen Hiperbarik (HBOT) adalah suatu terapi dengan pemberian oksigen konsentrasi 100% dan tekanan lebih dari 1 atmosfer absolut (ATA), yang dilakukan di ruang udara bertekanan tinggi/ruang hiperbarik dengan tekanan lebih dari 1 atmosfer (Atm). Regimen HBO (hiperbarik oksigen) menggunakan tekanan 1,5 hingga 2,5 Atm untuk durasi 30 hingga 90 menit, yang dapat diulang beberapa kali. Waktu antara dan jumlah total sesi berulang sangat bervariasi. Tujuan terapi oksigen hiperbarik untuk perawatan dan pengobatan beberapa penyakit seperti emboli intravaskular, penyakit dekompresi, infeksi anaerob, keracunan CO (Shahriari, Khooshideh, & Heidari, 2014).

B.Ruang Hiperbarik Ruang hiperbarik dapat terdiri dari dua jenis: tunggal atau ganda. Sementara tekanan terjadi di tempat duduk tunggal melalui oksigen dan peningkatan tekanan bersifat sistemik, ruang multiplace diberi tekanan dengan udara dan oksigen disuplai kepada pasien melalui masker, helm, atau tabung endotrakeal, tergantung kasusnya. (Gill & Bell, 2004)

C. Indikasi Terapi Oksigen Hiperbarik Penting untuk mengetahui indikasi untuk terapi hiperbarik. Indikasi meliputi penyakit dekompresi, emboli udara, keracunan karbon monoksida, cedera, anemia kehilangan darah akut, abses intrakranial, luka bakar termal, fasciitis nekrotikans, gas gangren, dan kehilangan pendengaran akut. Kondisi tersebut perlu mendapat perawatan terapi oksigen hiperbarik. Pada umunya pusat hiperbarik merawat pasien dengan dengan kondisi non- alergi seperti penyembuhan luka yang buruk, cedera radiasi yang tertunda, osteomielitis kronis dan flap. Sangat penting bagi tim medis yang merawat untuk mengenali indikasi hiperbarik yang muncul. (Chen et al., 2019)

D. Indikasi Terapi Oksigen Hiperbarik menurut (Mathieu et al., 2017) Keracunan karbon monoksida (CO) Merekomendasikan HBOT dalam pengobatan keracunan CO (rekomendasi Tipe 1, bukti Level B). • Merekomendasikan 100% oksigen segera diterapkan pada orang yang keracunan CO sebagai pengobatan pertolongan pertama (rekomendasi Tipe 1, bukti Level C). • Merekomendasikan HBOT untuk setiap orang yang keracunan CO yang disertai dengan adanya perubahan kesadaran, tanda- tanda klinis gangguan neurologis, jantung, pernapasan atau psikologis dan tingkat karbokshaemoglobin pada saat masuk rumah sakit (rekomendasi Tipe 1, bukti Level B). • Merekomendasikan HBOT pada wanita hamil yang keracunan CO apa pun gejala klinis mereka dan tingkat karboksihemoglobin saat masuk rumah sakit (rekomendasi Tipe 1, bukti Level B). • Sebaiknya merawat pasien dengan keracunan CO minor baik dengan oksigen normobarik 12 jam atau HBOT (rekomendasi Tipe 3, bukti Level B). • Tdak merekomendasikan perawatan dengan pasien tanpa gejala HBOT yang terlihat lebih dari 24 jam setelah akhir paparan CO (rekomendasi Tipe 1, bukti Level C)

Fraktur terbuka dengan crush injury

• Merekomendasikan HBOT dalam pengobatan fraktur terbuka dan/ atau dengan crush injury (Rekomendasi Tipe 1, bukti Level B). • Merekomendasikan aplikasi awal HBOT setelah fraktur terbuka parah karena dapat mengurangi komplikasi seperti nekrosis jaringan dan infeksi. Cedera Gustilo 3B dan 3C dianggap sebagai indikasi untuk HBOT dan cedera yang kurang parah harus dipertimbangkan untuk perawatan ketika terdapat faktor risiko terkait host atau cedera (rekomendasi Tipe 1, bukti Level B). • Menyarankan bahwa HBOT dapat memberikan manfaat pada crush injury dengan luka terbuka tanpa fraktur, di mana viabilitas jaringan berisiko atau di mana ada risiko infeksi yang signifikan (rekomendasi Tipe 2, bukti Level C). • Sebaiknya memberikan HBOT untuk crush injury/ cedera tertutup di mana viabilitas jaringan secara klinis dinilai berisiko (rekomendasi Tipe 3, bukti Level C). • Sebaiknya memberikan HBOT untuk crush injury/ cedera tertutup di mana ada potensi sindrom kompartemen, tetapi yang tidak memerlukan fasciotomi dan dimungkinkan untuk memantau kemajuan dan respons terhadap pengobatan baik secara klinis atau melalui tekanan kompartemen atau pemantauan oksigenasi (Rekomendasi Tipe 3, bukti Level C). • Merekomendasikan bahwa pusat HBOT yang merawat crush injury harus memiliki peralatan untuk pengukuran oksimetri transkutan (TCOM) di bawah tekanan karena ini memiliki nilai prediksi dalam beberapa situasi (Rekomendasi Tipe 1, bukti Level B

D. Radionekrosis/lesi yang disebabkan oleh radiasi • Merekomendasikan HBOT dalam pengobatan osteoradionekrosis mandibula (Rekomendasi Tipe 1, bukti Level B). • Merekomendasikan HBOT untuk pencegahan osteoradionekrosis mandibula setelah pencabutan gigi (rekomendasi Tipe 1, bukti Level B). • Merekomendasikan HBOT dalam pengobatan sistitis radiasi hemoragik (Rekomendasi Tipe 1, bukti Level B). • Merekomendasikan HBOT dalam pengobatan proktitis radiasi (rekomendasi Tipe 1, bukti Level A). • Menyarankan HBOT dalam pengobatan osteoradionekrosis tulang selain mandibula (Rekomendasi Tipe 2, bukti Level C). • Menyarankan HBOT untuk mencegah kehilangan implan osseointegrasi pada tulang yang diradiasi (Rekomendasi Tipe 2, bukti Level C). • Menyarankan HBOT dalam pengobatan radionekrosis jaringan lunak (selain sistitis dan proktitis), khususnya di daerah kepala dan leher (rekomendasi Tipe 2, bukti Level C). • Sebaiknya menggunakan HBOT untuk mengobati atau mencegah lesi yang diinduksi radio dari laring (Rekomendasi Tipe 3, bukti Level C). • Sebaiknya menggunakan HBOT dalam pengobatan lesi yang diinduksi radio dari sistem saraf pusat (Rekomendasi Tipe 3, bukti Level C).

E. Penyakit Dekompresi (DCI)

Penyakit dekompresi merupakan kondisi yang terjadi pada saat aliran darah di dalam tubuh terhambat, dikarenakan perubahan tekanan udara. Perubahan tekanan ini dapat terjadi akibat penerbangan, menyelam, atau hal lain yang mengakibatkan terjadinya perubahan tekanan udara secara drastis. Perubahan tekanan udara di luar tubuh yang tiba-tiba dapat menyebabkan timbulnya gelembung udara di dalam pembuluh darah atau emboli.

F. DASAR FISIOLOGIS TERAPI OKSIGEN HIPERBARIK

Efek HBOT didasarkan pada regulasi gas, dan efek fisiologis dan biokimia dari hiperoksia. Hukum Boyle menyatakan bahwa pada suhu konstan, tekanan dan volume gas berbanding terbalik. Ini adalah dasar untuk semua terapi hiperbarik. Hukum Boyle menjelaskan tentang hubungan tekanan gas dan volume gas. Tekanan gas berbanding terbalik dengan volume gas. Bila tekanan semakin besar maka volume akan semakin kecil. Prinsip ini digunakan pada kasus-kasus penyakit dekompresi dan emboli gas. Pada penyakit dekompresi, terjadi gelembung-gelembung nitrogen (nitrogen bubbles) sehingga terjadi penyumbatan pembuluh darah akibat gelembung ini.

Oksigen yang ditangkap dengan bernapas juga bervariasi selama perawatan di ruang hiperbarik, karena, selama penurunan ke kedalaman, tekanan oksigen intraalveolar meningkat; Ini terjadi sebagai respons fisiologis yang merespons hukum Boyle dan hukum Dalton. Hukum Boyle menyatakan bahwa, pada suhu konstan, tekanan gas berbanding terbalik dengan volumenya, sementara hukum Dalton menyatakan bahwa dalam campuran gas setiap elemen memberikan tekanan yang sebanding dengan fraksinya dari total volume; hukum-hukum ini menjelaskan efek dari tekanan parsial oksigen dan intraalveolar tersedia. (Balestra et al., 2016).

G. MEKANISME HBOT

Reactive Oxygen Species (ROS) Prinsip dari terapi oksigen hiperbarik adalah membantu tubuh untuk memperbaiki jaringan yang rusak dengan meningkatkan aliran oksigen ke jaringan tubuh. Terapi oksigen hiperbarik akan menyebabkan darah menyerap oksigen lebih banyak akibat peningkatan tekanan oksigen di dalam paru￾paru yang dimanipulasi oleh ruangan hiperbarik. Dengan konsentrasi oksigen yang lebih tinggi dari normal, tubuh akan terpicu untuk memperbaiki jaringan yang rusak lebih cepat dari biasanya. Terapi oksigen hiperbarik (HBOT) memberikan oksigen di bawah tekanan untuk meningkatkan kadar oksigen jaringan. Oksigen diberikan 2-3 kali lebih tinggi dari tekanan atmosfer, dan didistribusikan di sekitar area yang terinfeksi; sehingga memungkinkan terjadinya proses penyembuhan alami tubuh dan memperbaiki fungsi jaringan. HBOT juga merangsang kaskade transduksi sinyal dengan meningkatkan oksigen reaktif dan spesies nitrogen, maka jaringan akan melepaskan prostaglandin, oksida nitrat, dan sitokin yang menunjukkan respons patofisiologis terhadap luka, pembedahan, dan infeksi. HBOT diketahui sebagai terapi untuk mengobati penyakit dekompresi, gangren, atau keracunan karbon monoksida. (Al-Waili & Butler, 2006; Gandhi et al., 2018).

ROS dipandang berbahaya karena potensinya menyebabkan kerusakan pada lipid, protein, dan DNA (Alfadda & Sallam, 2012), tetapi secara ilmiah ROS sangat penting dalam pensinyalan dan pengaturan sel, contoh, dalam sel endotel, ROS adalah penyebab utama dari banyak patologi vaskular, seperti disfungsi endotel diabetes dan hiperpietik, di sisi lain, angiogenesis dan vasorelaxasi yang bergantung pada endotelium berada di bawah kendali redoks. Karena sifatnya yang aktif dan berumur pendek, ROS harus dihasilkan di kompartemen subseluler yang tepat yang dekat dengan molekul yang dimodifikasi dalam proses pensinyalan dan pengaturan sel yang bergantung pada ROS. (Craige, Kant, & Keaney Jr, 2015).

H. FISIOLOGIS, DAN FARMAKOLOGIS GAS HIPERBARIK

Di permukaan laut konsentrasi oksigen plasma adalah 3 ml/l. Jaringan saat istirahat membutuhkan sekitar 60 ml oksigen per liter aliran darah (dengan asumsi perfusi normal) untuk mempertahankan metabolisme seluler yang normal, meskipun persyaratan bervariasi di antara jaringan. Pada tekanan 3 atmosfer (304 kPa) oksigen terlarut mendekati 60 ml/l plasma, yang hampir mencukupi untuk memasok kebutuhan oksigen total istirahat dari banyak jaringan tanpa kontribusi dari oksigen yang terikat dengan hemoglobin. Ini memiliki keuntungan dalam situasi seperti keracunan karbon monoksida atau anemia berat di mana sulit melakukan crossmatching atau keyakinan agama mencegah transfusi darah (Leach et al., 1998).

Fungsi HBOT Secara umum dapat dibagi menjadi dua jenis efek, fisiologis dan farmakologis, kadang terjadi tumpang tindih. Oksigen dapat dianggap sebagai unsur alami yang penting untuk kehidupan, dan sebagai obat yang digunakan untuk mengubah patologi penyakit. HBOT menggunakan oksigen sebagai obat dan oleh karena itu, memiliki protokol dosis yang tepat, indeks terapi, dan efek samping yang perlu dipahami agar dapat digunakan dengan aman dan efektif. (Kahle & Cooper, 2019; Maslova & Klimova, 2012)

I.FUNGSI/MANFAAT (HBOT)

Terapi Oksigen hiperbarik fungsi HBOT sangat kompleks. Akan mengurangi ukuran gelembung gas dalam cairan (darah). Sehingga meningkatkan kapasitas pembawa oksigen darah melalui peningkatan konsentrasi oksigen plasma menjadi sekitar 7%. Adanya bakteriostatik dan bakteriosidal pada tekanan dan oksigenasi yang lebih tinggi. Oksigen hiperbarik akan meningkatkan neovaskularisasi arteri dan mengurangi edema jaringan, yang akan menghambat berbagai eksotoksin seperti racun alfa dan beta yang terkait dengan infeksi nekrotikans. Pengobatan hiperbarik akan meningkatkan difusi oksigen lebih lanjut dalam jaringan dengan jarak sekitar empat kali jarak perfusi normal. Sehingga akan menyebabkan terjadi difusi oksigen dari lingkungan yang kaya oksigen ke lingkungan oksigen yang buruk seperti dengan luka iskemik dan anggota badan. Hukum Boyle adalah dasar untuk efektivitas dalam penyakit dekompresi dan emboli udara. Permukaan terlalu cepat dari penyelaman bawah laut yang dalam akan menghasilkan presipitasi gelembung nitrogen dalam darah. Ini akan menghasilkan persendian yang sangat menyakitkan, tikungan, dan bahkan kematian. (Fife et al., 2016; Jones & Wyatt, 2019)

J.BAHAYA DAN KONTRAINDIKASI Terapi oksigen hiperbarik

kontraindikasi mutlak untuk perawatan hiperbarik adalah pneumotoraks yang tidak diobati. Kontraindikasi relatif lainnya adalah jika pasien menggunakan agen kemoterapi tertentu seperti Adriamycin dan Cisplatinum atau Antabuse. Masalah lain yang menjadi perhatian adalah pasien berventilasi, pasien dengan hipertensi yang tidak terkontrol, dan penderita diabetes. Masalah dengan pasien berventilasi adalah varian dalam volume udara dan tekanan dan masalah barotrauma. Gula darah serum sering jatuh saat menyelam. Oleh karena itu, disarankan untuk memastikan glukosa serum pada pasien dengan diabetes berada pada sisi yang tinggi sebelum menyelam (Cho et al., 2018). Efek samping negatif dari menerima O2 bertekanan, akan terjadi cedera stres oksidatif, kerusakan DNA, metabolisme seluler, pengaktifan koagulasi, disfungsi endotel, neurotoksisitas akut, dan toksisitas paru, gangguan metabolisme sel, mengaktifkan koagulasi, disfungsi endotel, neurotoksisitas akut dan toksisitas paru. (Chen et al., 2019).

Alasan mengapa HBOT tidak boleh diberikan pada interval yang jauh lebih sering dan dalam sesi yang lebih lama adalah potensi risiko keracunan oksigen (Körpınar & Uzun, 2019) Risiko oksigen hiperbarik; Bahaya kebakaran; Komplikasi fatal yang paling umum. Fitur umum; Claustrophobi, Miopia yang dapat dibalik, Kelelahan, Sakit kepala, Muntah. Barotrauma; Kerusakan telinga, Kerusakan sinus, Telinga tengah yang pecah, Kerusakan paru-paru. Toksisitas oksigen; Otak, Kejang, Psikologi. Paru-paru, Edema paru, perdarahan, Toksisitas paru, Gagal pernafasan (mungkin tidak dapat dikembalikan ketika terjadi fibrosis topulmoner). Penyakit dekompresi; Penyakit dekompresi, Pneumotoraks, Emboli gas. (Chen et al., 2019; Leach et al., 1998; Thom, 2009; Stephen R Thom, 2011).

Reviewer #1:

General Assessment:

I found the studies to be well motivated and thoughtfully designed to disentangle competing interpretations in the extant literature on visual perception in ASD. The first two experiments provided compelling evidence that prior choices affect perceptual decision making in ASD, but the outcome of the response invariant condition suggests that the authors' interpretation goes beyond the data.

Substantive Concerns:

"In summary, we found here that individuals with ASD demonstrated an increased influence of recent prior choices on perceptual decisions (vs. controls),..." is the major finding in the paper, quoted here in the concluding paragraph. It seems, however that the data support a narrower (and potentially less interesting) conclusion that individuals with ASD demonstrated an increased influence of recent button presses/motor responses, as the finding which forms the basis of the summary went away when different keys were used to report prior vs. test responses (i.e., in the response invariant condition). I understand that the authors present these data as challenges to theories of attenuated priors in ASD, but they seem to sidestep the issue that these data make their general conclusion more complicated.

For completeness, it would be helpful to present some information on the stimulus values for the test stimuli, as these were set individually using a staircase. Where did these staircases converge? Were there group differences?

Reviewer #1:

In this manuscript, the authors show they can accomplish imaging in complex specimens using 3- and 4-photon excitation, deeper in the specimen than comparable optics can accomplish with 2-photon excitation laser scanning microscopy. This is a clear advantage for imaging optically hostile specimens such as cultured organoids or spheroids, or in challenging in vivo settings. I am excited about these findings, but I am not at all supportive of the current version of the manuscript being used to present these lovely findings.

There are two strong reasons for my opinion:

i. The manuscript presents the findings in a manner that will only be understandable by the readers who are familiar with the topic, and who are likely to already have heard of the capabilities of 3- and 4-photon excitation to image deeper into specimens.

ii. The results are not presented in a way that the large body of potential readers can understand. They will be unable to grasp the way that the experiments were performed, or understand what the figures are showing, or critically evaluate the results that are presented.

Thus, there is a disconnect between the quality of the work and the quality of the presentation. There are many areas of quantitative imaging and intravital imaging that are well known to those that know about them (or use them), and that are a complete mystery to the vast majority of those that don't know about the tools or use them. The authors must take this as an opportunity to reach the many workers that could benefit from this powerful approach, rather than writing for the group that already knows (and even uses) the approaches presented.

1) Provide needed background and present important things first. The authors should give the reader a clear view into the issues in imaging biological tissues with the longer wavelengths that are used for confocal laser scanning microscopy (CLSM) and for two-photon laser scanning microscopy (TPLSM). There are several factoids presented, all seemingly true, but not presented in an accessible manner. Rather than starting with a mention of the expected temperature rise due to the dramatically higher absorbance by water of 1300nm and 1700nm light, the paper first presents the major absorbance of the light (~2/3 loss) and that this isn't a problem because there is sufficient laser power. For most readers, the need for a larger laser won't be their first question; instead it will be the viability after/during the imaging session. The expected temperature rise, and an indirect mention of burn marks (!), comes at the end of the section.

2) Explain and perform cell viability tests. Calcium imaging for assessing tissue viability is not the technique of choice for most readers, and is presented in a way that assumes general knowledge that simply does not exist. Membrane patency assays using membrane-impermeant DNA dyes, or other live-dead assays are far more common, but not presented in this study. I am not insistent that the authors use any particular assay, but I am insistent that the authors present the need for viability assay(s), teach the reader the principles of the assay(s) used, and present the results in an understandable manner.

3) Present the finding and the figures in an accessible manner. The figures are simply not digestible by the readers who do not perform this sort of work, and the legends do not help sufficiently. For those of us who do perform work of this sort, the figures are not as convincing as they should be, or presented in a way that they can be critically evaluated.

Consider the legend for Figure 1: "Microscopy with simultaneous 2-, 3- and 4 photon processes excited in fluorescent skin tumor xenografts in vivo. Representative images were selected from median-filtered (1 pixel) z-stacks, which were taken in the center of fluorescent tumors through a dermis imaging window. a) Excitation at 1300nm (OPA) in day-10 tumor at 145 μm imaging depth with a calculated 3.3 nJ pulse energy at the sample surface, 24 μs pixel integration time and 0.36 μm pixel size. For calculation of pulse energy at the sample surface see Figure S3. b) Excitation at 1650 nm (OPA) in day-13 tumor at 30 μm depth with a calculated 6.3 nJ pulse energy at the sample surface, 12 μs pixel integration time and 0.46 μm pixel size. c) Excitation at 1650 nm (OPA) in day-14 tumor at 85 μm depth, with a calculated 5.4 nJ pulse energy at the sample surface, 12 μs pixel integration time and 0.46 μm pixel size. Cell nuclei containing a mixture of mCherry and Hoechst appear as green."

If I gave any of the figures and legends to the people in my lab, the half that don't do multiphoton imaging (but that have sat through many lab meetings) would just hand them back to me with quizzical expressions on their faces.

The figures are not as compelling as the results, and defer to the body of the paper to explain what was done or what was shown, and assumes that the average reader remembers the differences between OPO and OPA , for example (which they won't). The power plots showing nJ and mW in Figure 3 are inaccessible to most readers, and not well described.

I should mention that the figures, legends and text are not satisfying for the readers who are familiar with 2-, 3- and 4-photon imaging either. These are fantastic findings, and deserve figures that are as lovely as the results, and are compelling. Some of these issues are due to typos: "Consistently, multiparameter recordings were achieved inside the tumor at 350 μm depth using excitation at 1650 nm and 1300 nm, but 1180 nm (Figure 3b). "

However, the greater problem is that the text doesn't present the findings in a straightforward, convincing fashion and then interpret them. Instead, the conclusion often leads the evidence: "In line with an improved depth range, the signal-to-noise ratio (SNR) of 3PE TagRFP outperformed the SNR of 2PE TagRFP at depths beyond 150 μm (Figure 3c). Because H2B-eGFP expression in HT1080 tumors was very high, 3PE eGFP emission reached the highest SNR."

The legend and figure that it describes should be able to stand on their own, and convince a skeptical reader with the help of the text in the body of the manuscript.

In summary, these are lovely and important results that I am excited about. They are presented in a fashion that will make it difficult for most to appreciate because the body of the paper is not fashioned to teach the reader, and the figures themselves are challenging, and the legends inadequately present what is shown in the figures. Careful expansion and editing should resolve all of these issues and make the manuscript into the presentation these excellent findings deserve.

Reviewer #1:

The manuscript describes the characterization of in total 85 Cryptococcus spp. clinical isolates with regard to virulence phenotypes including a Galleria mellonella infection model for cryptococcosis. The authors determined the melanization kinetics of all strains, measured the whole-cell and extracellular laccase activity, the capsule thickness, and the concentration of the cell wall polysaccharide glucuronoxylomannan. In addition, during macrophage interaction the proportion of Cryptococcus-containing LC3-positive phagosomes for each strain was determined as well as the survival of G. mellonella after infection with selected Cryptococcus strains. Finally, regression analyses were performed to estimate the relationship between the risk of death in crytptococcosis patients and the phenotypes of the isolated Cryptococcus strains. A major finding was that the risk of death in patients with disseminated cryptococcosis increased with the level of extracellular laccase activity and the time for half-maximum melanization in the Cryptococcus isolates. This suggests that the melanization rate, more than the total amount of melanin, impacts the outcome of a Cryptococcus infection.

General assessment:

The study is based on carefully performed experiments. However, the scientific significance of this work is moderate. Melanin and the laccases that are involved in its synthesis are known virulence factors of Cryptococcus spp. for many years and similar studies have already been published elsewhere (e.g. Samarasinghe et al. 2018). The major new finding of the presented work is that the speed of melanization has an impact on the virulence of Cryptococcus spp. rather than total amount of melanin. The shortcoming of the manuscript is that the author's hypothesis is mainly based on regression analyses, but the final proof based on a genetically well-defined background is missing. Therefore, the study only provides little new insight into fundamental mechanisms of Cryptococcus virulence but includes associations with patients and therefore might be more suited for a journal specialized in pathogenic fungi.

Following points should be considered:

1) The authors show the association between faster Cryptococcus melanization and more effective evasion from host immunity. However, the author cannot totally exclude other factors that are associated with host evasion. It would be more appropriate to either create a mutant (e.g. overexpression of LAC1), which showed faster melanization in comparison to a wildtype strain or to perform multilocus sequence typing (including the LAC1 locus) to capture the genetic variation of the clinical isolates and to find come correlations with the speed of melanization. The interesting question is which genetic factors contribute to the difference in the melanization rate.

2) The authors should critically discuss the suitability of their Galleria mallonella infection model. It is a known fact that temperature has an influence on the melanization in Cryptococcus spp.. Laccasse activity is significantly inhibited at temperatures of 37°C and higher. The Galleria model can only be used at lower temperatures.

Reviewer #1:

The present paper addresses the very topical problem of understanding of dynamic switching in central pattern generators. The paper investigates switching between bursting and spiking modes in spinal cord neurons. This is modelled using a multichannel HCO that identifies narrow regions in parameters where the system is bistable. It is argued that neurotransmitters drive invertebrate CPGs to favourable bistable regimes that allow rapid switching from one oscillatory state to another (e.g. foraging to escape) to be enacted by fast electrical stimuli. The paper is generally well-written and does a good job at interpreting observations.

I have two major comments:

1) The authors seem to ignore the switching between phasic and antiphasic oscillatory states, even though this is shown in Fig.1, and more generally between the polyrhythms that would occur in larger inhibitory networks. The latter switching may be at least as relevant to gait generation as the switching from bursting to spiking. Polyrhythms have also been shown experimentally and theoretically to produce robust multistable states that overlap over a wide parameter space. It would therefore be useful if the authors could comment on the relative robustness of spiking/bursting multistability vs polyrhythm multistability.

2) It is argued that an hyperpolarizing Ip pulse will induce a transition from continuous spiking to bursting and conversely a depolarizing pulse induces the reverse transition from bursting to continuous spiking. Transitions are a dynamic process which will depend, among other things, on the timing when the pulse is applied during the heteroclinic cycle. In the absence of more information on the dynamics of the system such claims look over-simplistic.

Reviewer #1:

In this study, the authors investigated whether the morphological and electrophysiological properties of glycinergic interneurons in the spinal ventral horn of GlyT2eGFP SOD1 G93A mice are altered compared with GlyT2eGFP WT mice at P6-P10 (the SOD1 G93A mice is the classic mouse model of amyotrophic lateral sclerosis). Such an investigation has never previously been done. The main body of results relies on a sample of 34 WT and 25 SOD1 patched interneurons located throughout the ventral horn. The authors found that soma sizes of patched interneurons are not significantly different in SOD1 animals than in WT animals but their dendrites are larger. The onset and the peak of persistent inward currents (PICs) are more depolarized in SOD1 interneurons suggesting that they are less excitable than in WT. Immunohistochemistry for Calbindin was performed in a subset of the patched interneurons to identify Renshaw cells (7 cells in WT animals and 6 cells in SOD1 animals). Calbindin positive cells display more depolarized PICs onset and peak in SOD1 than in WT animals. A predictive statistical analysis was then performed in order to include in the Renshaw cells sample cells that were not tested for calbindin. This analysis suggested that the predicted Renshaw cells are less excitable in SOD1 mice than in WT mice whereas the predicted non-Renshaw cells are more excitable. The implications of these findings for the ALS pathophysiology are discussed.

However, a number of major concerns substantially weaken the findings:

1) Morphological properties Texas red allowed the authors to localize the patched cells in the ventral horn, to measure the soma and the dendrites and to investigate whether the patched cells were immunopositive to Calbindin. It appears that the soma volumes of the patched neurons are on average 2-3 times larger than the soma of the general population of GlyT2-GFP neurons in the ventral horn or in lamina IX (Table 1). No explanation is provided for this discrepancy. Does it mean that there is a systematic recording bias towards the largest interneurons ? Alternatively, is there a systematic swelling of the patched cells or a shrinking in the fixed spinal sections? Also, it is not clear what the dendritic parameters are? It is necessary in Figure 2 to show a reconstruction of dendrites in order to figure out which dendritic length, surface and volume are reported in Table 1.

2) Electrophysiological properties The shift in the onset of the persistent inward currents onset is taken as an important indicator of a reduced excitability in SOD1 interneurons. However the measurement of the PIC onset is problematic. It is claimed in the Material and Methods section that "PIC onset was defined as the voltage at which the current began to deviate from the horizontal, leak substracted trace" (lines 374-375), which seems reasonable. However, in Figure 3A, the arrow for the PIC in the SOD1 motor neuron (red trace) does not point to the initial deviation from the horizontal which actually occurred at about -60mV, i.e. close to the PIC onset for the WT motoneuron (blue trace), in contradiction with the authors claim. The arrow points to a second component whose onset appears at a more depolarized voltage. Then the net current is likely to be complex and a pharmacological dissection of the currents at work is required both in WT and SOD1 neurons. Indeed, the net inward current might result from the summation of inward and outward currents. Are they outward currents at work? Are the inward currents Na+ or Ca++ currents? In the absence of such a pharmacological "dissection" it is difficult to fully interpret the data.

3) Identification of the Renshaw cells The authors identified a subset of GlyT2 neurons as Renshaw cells because they expressed Calbindin-D-28K. This sole criteria does not allow a proper identification of Renshaw cells, particularly in P6-P10 mice. Indeed, many non-Renshaw cells in the ventral horn are calbindin-immunopositive during this post-natal maturation period in addition to the Renshaw cells (Siembab et al, J Comp Neurol, 2010). One distinguishing feature of Renshaw cells is that they are excited by recurrent motor axon collaterals. Then, the presence of VACht boutons on the GlyT2 cells would have been an interesting additional identification criteria. However, there is another source of VACht boutons than motor axon terminals in the spinal cord (Zagoraiou et al, Neuron 2009). Since this is an electrophysiological work, the authors had the possibility to unambiguously identify Renshaw cells: the presence of synaptic excitations in response to the stimulation of motor axons in a ventral rootlet (using oblique spinal cord slices, see for instance: Lamotte d'Incamps and Ascher, J Neurosci 2008; Bhumbra et al, J Neurosci 2014). The authors are advised to perform such an electrophysiological identification of Renshaw cells.

4) Statistics and predictive model The number of patched cells identified as "Renshaw cells" on the basis of their Calbindin immunopositivity is low (7 WT and 6 SOD1). Indeed, I do not see any reason why the authors did not repeat the experiments in order to gather a more reasonable number of cells. Statistical analysis was performed on this low cell samples, in order to investigate whether each property under investigation differs or not in WT and SOD1 animals as reported in Table 3 (normality of the distribution was tested for each property and either ANOVA analysis or Kruskall Wallis analysis was performed). The validity of statistics on such low cell samples is questionable. The analysis was then extended to all patched cells using sophisticated random forest and principal components analysis in order to check whether some cells among those not tested for calbindin display enough similarities with the calbindin-positive cells to be considered as putative Renshaw cells. The model predicted that 80% of the 59 patched cells were "Renshaw cells", a percentage astonishingly larger than the percentage of calbindin-positive cells in the ventral horn (65%). This prediction is doubtful since the number of calbindin-positive cells is already higher at P6-P10 than the number of Renshaw cells (see bullet point 3). Nevertheless, the authors made statistics (not shown on the paper) on the basis of this prediction, and they found that the predicted Renshaw cells are less excitable in SOD1 mice than in WT mice whereas the predicted non-Renshaw cells are more excitable.

+1.

Reviewer #1:

This paper shows that Cas 9 mediated homology directed repair can be used to insert a synthetic rescue gene into an essential gene, here mitochondrial Pol-gamma35 was chosen. The insertion is marked by an eyeless-GFP reporter and also contains the gRNA (gene drive) but not the Cas9 (considered as a safe split gene drive). 'Homing' of the eye-GFP is assayed to detect insertion at the homologous locus when Cas9 is present by HDR. The authors show that this works well in the female germline with various tested Cas9 lines (vas, nos, Act5C and ubiq-Cas9). In all cases close to 100% transmission to the homologous locus on the homologous chromosome is achieved when an effective guide RNA is used. Hence, eye GFP transmits ('homes') in a 'super-Mendelian' ratio at the chosen target. A male specific transmission works less well (exuL-Cas9). The reason why it works well appears to be that the chosen target is an essential gene (Pol-gamma35) in which small changes caused by NHEJ that result in homing 'resistant' alleles will be loss of function alleles and hence will not spread in the population. Unfortunately, the authors did not test how the drive could spread in a wild type population (no Cas9 expression). I am also missing a test relevant for pest studies that would achieve the spread of a potentially deleterious or beneficial insertion that could kill a population or make it resistant to a disease.

1) This paper is very hard to read. Sentences are excessively long and complicated. References to the Figures appear not always correct.

2) Figure 1. Genotypes in Figure 1A are unreadable in the print version because of the small font. Are the 2 crossing schemes required that only differ in gRNA1 or gRNA2? The surviving progeny should be quantified as in Fig 1B. Figure 1B shows nos-Cas9 and not act-Cas9 results (several typos in line 148-155). Figure 1C: the incidence of heterozygous, homozygous and 'resistant' cells is schematic and not supported by data, hence questionable if Figure 1C should be shown in results.

3) Figure 2. Genotypes not readable in print. Is it necessary to show schemes of the procedure how transgenic flies were generated and how the Pol-gamma 35 HomeR were made with all chromosomes detailed (Fig 1D)? This could move to the methods as it is standard and we learn not much new.

4) More typos: line 286: Fig2B is the wrong reference; line 295 should read Actin 5C. Figure 4B GGG codes for Gly (not Gla). lines 576 to 592 should refer to Figure 6?

5) Figure 5 - as figures 1+ 2, only readable on the computer.

6) It would be interesting to see how the gene drive would spread if Home R and Cas9 would be introduced in a competitive way into wild type populations. This is similar to Fig 4C, but the only the Home R males or females would carry the Cas9. This would be a more realistic test how the gene drive could spread in a wild population that obviously does not express Cas9.

Reviewer #1:

This paper uses a variety of mouse lines to investigate what retinal circuits control the pupillary light reflex (PLR). Recordings from rods and bipolar cells confirm that the manipulations work as expected - at least at the level of the bipolars. Measurements of the PLR in these mice then are used to draw inferences about the relevant pathways. The main conclusions are that cones contribute little to the PLR across light levels, that signaling in Off retinal circuits contributes little, and that both primary and secondary rod pathways contribute.

I have several concerns about the work as presented:

1) Use of mouse lines. The mouse lines are interpreted as cleanly dissecting different retinal pathways, but this may not be the case. For example, deletion of one pathway may alter signaling in another pathway - either through compensatory effects, or from interactions between the pathways that are missing when one is removed. One way to address this concern would be to record from RGCs to test for such effects. For example, the cone sensitivity in the RGCs in Cx36-/- mice should not be altered. The bipolar recordings are helpful in this regard, but they do not represent the circuit output and hence could miss key interactions or compensation.

2) Interpretation. The results are interpreted in the context of a standard model of retinal circuitry. Yet several aspects of the results suggest that such a model is incomplete. One example mentioned in the text is the possibility of direct RBC to RGC connections. A specific concern in this regard is that it is unclear how the secondary pathway could control the PLR but cones could not - since rod and cone signals are mixed in the secondary pathway. Accounting for the results in the paper would appear to require revisiting our understanding of retinal circuits - but more direct tests of the circuits are needed for such a conclusion.

3) Relation with past work. The paper is short and suffers from short or missing descriptions of related past work. For example, a good deal is known about how signals from the primary and secondary pathways modulate cone bipolar and RGC responses. This is directly relevant to what is expected and unexpected in the present work. Recent work (Lee et al., 2019) also shows a contribution of melanopsin to ipRGC responses at low light levels - but this is mentioned only in passing in the present paper. This work appears highly relevant to the present study.

Reviewer #1:

My general assessment of this work is that it is full of good ideas and presents a novel and general approach to examine lipid remodeling in cells and perhaps subsequent transport of lipids, mainly to mitochondria, but it lacks the scientific rigor necessary to be fully confident that their conclusions firmly support their claims. Often, insufficient information about the methods are provided and the manuscript is hard to follow critically.

More specific comments:

1) I am surprised that acyl-CoAs are transported into cells. I don't know of any precedent for this. Usually fatty acids are imported into cells and then converted to acyl-CoAs as part of the mechanism of import. Could it be that the acyl--CoAs are hydrolysed before uptake only to be reformed inside the cells? I would suggest feeding the NBD-palmitate plus the lysolipids to the cells as a control to see whether this is the case.

2) In fig 1 as an example they choose a region to blow up. As one can see there is a large variation, even in the blowups of mitochondrial labeling and if one looks at the originals the variation is confirmed. How have they chosen these areas? Furthermore, in figure 1 there is quite a bit of label with MLCL outside of the mitochondria, in particular in regions that they did not choose to blow up. What are these structures? Remodeling of MLCL is thought to take place in mitochondria.

3) They speak of transport of lipids from ER to mitochondria, but in fact the demonstration of this is very weak from what they show in the time course in supp fig 1. I am also disturbed by the difference in patterns of the NBD-PA patterns in a and b. They should be the same, but there are problems, maybe focus? I would say anyway that there is no clear evidence that the NBD PA first appears in the ER then goes to mitos. It could be synthesized in both compartments from their data.

4) The product characterization by TLC is insufficient. There are no standards, no characterization. Would they have seen the free NBD-palm by their methods?

5) When they use mutants and find less "transport" the mitochondrial signal as seen by mitotracker is always more diffuse. This indicates to me that there is another problem.

6) In fig 3 the fluorescent pictures do not correspond to what is seen in the quantification. There is more yellow in e than in h.

7) How did they add cholesterol at 50 or 100 micromolar? It is soluble at less than 1 micromolar in aqueous solution. The cholesterol experiments are puzzling. From what we know about StAR protein it recognizes cholesterol not esters. There is no precedent for cholesterol ester transport into mitochondria. Can they rule out that the esters are transported to the surface of the mitochondria and the NBD-Palm cleaved off and transported into the mitochondria?

8) The MAG and DAG experiments are overinterpreted. It could just be a kinetic problem since the MAG gets converted to DAG before TAG

9) They compare to externally added NBD lipids, but we don't know which ones they used. Are they using short chain NBD phospholipids. I could not find this in their manuscript. If they do not have the same NBD-palm in the sn-2 position then the comparison is meaningless.

10) The excitation and emission spectra of their probes are sometimes overlapping. How did they deal with this? Are they sure that they are not seeing FRET?

Reviewer #1:

This study from the Henderson laboratory describes the identification of a hybrid secretion system involved in the acylation and trafficking of a conserved class of bacterial lipoproteins. Spurred by the serendipitous observation of posttranslational modification, Icke et al. identify the AatD protein as the factor responsible for CexE acylation. Combining alignment of conserved sequences and structural data the authors isolate the site of acylation on the CexE polypeptide and identify AatD residues responsible for catalysis Overall this is a strong manuscript, densely packed with supporting data and extremely well written.

My only significant concern is the issue of novelty. Although the authors seem to imply they are the first to report this type of system, they cite a 2020 PLOS Pathogens paper by Belmont-Monroy detailing nearly identical results in Enteroaggregative E. coli. Given the significant amount of overlap between these two manuscripts, it would seem prudent for the authors to spend some time in the introduction and discussion highlighting open questions that this paper addresses.

Reviewer #1:

This is a potentially interesting analysis, but there is a lack of framing, details, and specificity that dampens my enthusiasm for the work.

1) As far as I can tell, the authors do not really demonstrate that "markers of negative emotion and pain" can be down-regulated during self-reassurance". They simply show that regions surviving multiple comparisons change depending on condition, but they don't show data supporting their hypothesis. How much do regions activated during criticism actually change during reassurance? What is the time course of these differences?

2) Behaviorally, the neutral statements from the two "conditions" appeared to have distinct intensity levels. Specifically the "intensity" for neutral trials during criticism blocks appears significantly lower than neutral trials for reassuring blocks. Because of this behavioral effect, within their design it is difficult to identify the cause of the brain changes.

3) How were subjects trained in self-criticism vs. reassurance? Is there any way to confirm that they were in fact doing the "task"? Further, at what point in the 2-week compassion training paradigm were FMRI data collected?

4) Figure 2 is quite confusing to me: (1) the authors refer to brain maps as "neural pain"? I would strongly advise against this as it is very reverse-inferency. I would recommend against using this phrase throughout the paper. (2) How would one interpret the phrase "neural pain during self-reassurance"? Is this emotional > neutral during reassurance?

5) Figure 3 refers to "trial by trial ratings of intensity" but if I am understanding the figure, this is not an accurate description. The authors are reporting the mean across subjects for each condition. It is unclear in fact how much variability there is on a trial-by-trial level within persons for the intensity of each condition. One idea is to use an amplitude modulation analysis to scale FMRI parameter estimates by the intensity rating on a per-trial basis. That would be an interesting analysis, IMO.

6) It is unclear from this paper what was done previously. It appears that the authors examined physiological data (e.g., HRV) in their previous report but don't talk about other measures that were collected here. It would be useful to know the extent to which they buttress the authors findings (or if they do not).

Reviewer #1:

The authors utilize a novel ex vivo system to visualize granulocytes migrating within experimentally induced blood clots. Granulocytes are labeled using CD11b and CD66b and visualized over time using fluorescence microscopy as they move within the ex vivo formed clots, which have been prepared under different anticoagulant conditions to generate varied clot structure. Leukocytes are activated using various agonists and behavior classified into 2 different phenotypes based on the staining pattern of DiOC6 as either diffuse or punctate. The experimental system allows for measure of individual cell velocity and clear images of cells showing changes in cell body structure. The use of cells from WAS patients provides a nice validation of the model system being presented in the study.

1) The authors state that citrated blood results in local fibrin formation and platelet activation; would it not be relevant to compare granulocyte behavior in such a setting to the hiridin or heparin-anticoagulated samples? This could also provide a valuable setting to study platelet-granulocyte interactions.

2) The further elimination of heparin-anticoagulated blood in favor of hirudin is also not clear. How does heparin pre-activate granulocytes, and what experimental evidence is seen by the authors other than an increase in number?

3) Are type A and type B leukocytes defined only by the DiOC6 staining pattern, or also by their velocity? Please clarify in the text.

4) The choice of "leukocyte priming agents" is not clear, in particular myeloperoxidase and lactoferrin. Leukocyte activation caused by these agents should be validated and the rationale more clearly defined (i.e. by referencing previous work that provides the mechanism of binding for these leading to neutrophil activation).

5) Regarding the Annexin V stained smaller structures presented in Figure 4; have the authors ruled out that these could be procoagulant extracellular vesicles from other leukocytes, i.e. by performing a co-staining with a platelet marker for positive identification?

6) Have the fibrinogen (Sigma) and von Willebrand factor (an in-house preparation from an academic lab collaborator) been tested for endotoxin levels prior to use in this system?

Reviewer #1:

General assessment:

Since Precision Oncology is getting important these days, understanding the relationship between cancer type-specific vulnerabilities and their biomarker is a major challenge of personalized therapy. Previously, genomic signatures such as mutation and copy number variation were favorable to predicting cancer vulnerabilities. Dempster et al. presented a systematic comparison of predictions with or without gene expression features using five major screen data sets, suggesting that gene expression would better predict cancer vulnerabilities. Although suggested interpretable models in the last part of the paper are questionable, the main message and the supportive comparisons are clear.

Major comments:

1) RNA expression cannot be separated from cell lineage bias. For example, ESR1 gene is also relatively overexpressed in normal female tissues. I'm wondering how overexpression specific dependency can be separated from the tissue bias.

2) Predicting drug response by expression signature might be risky if there is no clear copy number amplification signature or reasonable causality. Is it possible to find casual features of why a gene is overexpressed?

3) In this paper, the authors presented that EDA2R expression is the top feature of predicting the TP53 dependency and MDM2 inhibitors' response as an example of interpretable models. However, many studies have confirmed MDM2 phenotype depends upon TP53 genomic status. Similarly, the response of MDM2 inhibitors can be explained by TP53 mutational status. I'm curious whether the prediction of MDM2 dependency using EDA2R expression status shows a better prediction than the prediction using TP53 mutational status in statistics.

Reviewer #1:

The study is interesting and does have potential translational relevance. There are some concerns however: (1) in Figure 1 the blood glucose drops independent of food intake is this all related to decreased hepatic glucose output or are there any effects on urine. Was urinary glucose measured? Is there increased glycosuria?; (2) In previous papers you discuss the increased lean body mass when aprosin is not present. There is no body composition data in this study. Was there any body composition differences with the antibody among the different mouse models (e.g DIO vs Nash diet)?; (3) were any changes in lean body mass with the antibodies associated with increases in strength?; (4) several mouse ages are discussed in the Methods section: 12 weeks, 16 weeks, 12 week of high fat diet or 24 week of NASH diet. Not clear from description if mice were matched for age. Please clarify; (5) In Figure 5 there are a number of inflammatory markers which can vary according to the model. What about anti inflammatory markers (cortisol, IL-10 etc) would be helpful to get a better picture of physiologic changes.

Reviewer #1:

This manuscript by Luettgau et al. describes a study of second-order conditioning in humans. The behavioral task involved visual first- (CS1) and second-order cues (CS2) and gustatory outcomes (US). Behavioral results show that subjects preferred both the CS1+ and CS2+ over the CS1- and CS2-, respectively. MVPA shows that the CS1 evokes US representations in the lateral OFC, and that US representations in the amygdala increase over second-order conditioning. This study addresses an important and novel question. However, I have several major concerns regarding the study design and data analysis:

1) I do not see how it would be possible to disentangle responses to the CS1 and CS2 in this task. The delay between the CS2 and CS1 is only 500 ms, which is not long enough to disentangle fMRI responses to the two CS.

2) For the main "reinstatement" analysis, activity was averaged across both CS2 and CS1, and so it is unclear whether reinstatement is driven by the CS1 or CS2. The authors argue that "US reinstatement during SOC could only be faithfully attributed to the respective CS1, but not to CS2, since only CS1 had been directly paired with the US, and CS2 had not previously been experienced." However, this is only strictly true for the very first trial during which the CS2 could have gained full access to the US representation.

3) In this regard, it is unclear why the authors did not use data from the first-order conditioning phase to test for US reinstatement. Although the 4-second delay between CS1 and US is still quite short, TR-wise MVPA could provide evidence that signals are related to the CS1 and not the US itself.

4) Relatedly, the authors perform analyses suggesting that, from early to late phases of second-order conditioning, representations of CS2 in the amygdala became more similar to US representations. Although here they attempt to model fMRI responses to the CS1 and CS2 separately, there is no evidence that this was indeed successful. As I see it, the delay between the two CS is just not long enough to dissociate these responses.

5) Is there evidence for a CS1 evoked reinstatement of the US in the amygdala, and a CS2 evoked reinstatement of the US in the lateral OFC? In theory these signals should exist, but independently testing for activity related to the two CS requires a task design where the two CS are presented in isolation or with long enough delay between them.

Reviewer #1:

This manuscript extends on prior work by the authors (Griffis et al, 2017), which originally reported eccentricity-dependent differences in resting state connectivity between V1 and regions brain wide. This study builds on that work by expanding the pool of participants, using the HCP dataset, as well as also investigating any eccentricity-dependent effects that may emerge with tractography. Interestingly, both measures find that foveal areas in V1 are more strongly connected to frontoparietal networks. The study is interesting, but I have a few remaining points.

1) While during the resting state scans, there was, in theory, no 'task', participants were asked to maintain fixation on the cross in the center of the screen throughout the scan. I think it would be important for the authors to note that there is a possibility that the resting state correlations observed wherein foveal areas were more correlated with frontoparietal regions (and far periphery with DMN areas) could be due to attention directed towards the fixation cross, and away from the periphery. While I acknowledge the authors have no way to test this with this data set, it is possible that if participants had been asked to covertly attend to a ring in their far periphery the entire time instead, the correlations might have been flipped, with frontoparietal connectivity highest in the periphery towards the attended eccentricity. The authors should either explain why this is not a concern, or acknowledge it in the manuscript.

2) Related to the last point, what was the size of the screen used during the connectivity data acquisition? I ask because the far eccentricity bands determined using Benson et al's technique are very eccentric. And if participants had eyes opened and were fixating, was that eccentricity outside the outer edge of the screen? Because then it would be encouraged to be 'unattended', thereby potentially influencing connectivity results.

3) Was there any attempt at replicating these results in extra striate cortex? Are these patterns still there, both in structural and functional connectivity, for V2 or V3?

Reviewer #1:

This paper looks at the mechanism of transcription regulation by the ANTAR domain protein, EutV. ANTAR domain proteins are an evolutionarily widespread family of RNA-binding regulators in bacteria. EutV has been proposed to regulate expression of target genes by binding two RNA loops in a 5' UTR, leading to a change in the RNA structure that modulates premature transcription termination. The current study determines the structure of dimeric EutV bound to an RNA target with two binding sites. Surprisingly, the interactions between the ANTAR domains in each monomer and each of the two RNA loops are incompatible with simultaneous binding of one EutV dimer to both loops. Hence, the authors propose a model in which EutV is "handed off" from one loop to the other as the RNA is transcribed.

The structural information regarding the interaction between the ANTAR domain and RNA is an important advance, although there is very little comparison to previous studies, including a study that identified many of the same residues as being required for RNA binding (reference 33). The evidence that a EutV dimer cannot bind both RNA loops simultaneously is strong, and inconsistent with a previously proposed model of regulation. However, other than the structure, there are no data that support the authors' proposed hand-off model. In fact, as it is drawn in Figure 6D, I don't think the model is possible based on the same structural constraints that prevent simultaneous binding of the EutV dimer to both RNA loops. Without further experiments, I don't think the authors can conclude much about the mechanism other than it being unlikely that a single EutV protein binds both RNA sites simultaneously.

Major comments:

1) Throughout the paper, there is insufficient description of previous work on ANTAR domain proteins. In particular, there is little comparison to published structural data, including modeled RNA-bound structures. There is also very little discussion of the mutagenesis in reference 33 that identified many of the same residues as being required for RNA binding. There is no doubt that the structural work in the current study represents a substantial advance over previous studies, but it is important to describe the similarities and differences to prior work.

2) Discussion, second paragraph. The evidence for a conformational shift in EutV upon phosphorylation is weak. This hypothesis is based on structural modeling from a homologous protein that has only 37% sequence similarity.

3) The structure does appear to rule out the possibility of EutV binding both RNA hexaloops simultaneously, but the hand-off model is still rather speculative, and not supported by any additional experimental data; binding of two EutV dimers to the same nascent RNA would seem just as likely. There is insufficient discussion of how the hand-off model fits with previous mutagenesis studies (e.g. reference 25), and no follow-up experiments designed to test the model. If EutV is unable to bind both hexaloops simultaneously due to spatial constraints, how is it able to transition from one hexaloop to the other, as depicted in Figure 6D? I would expect the same spatial constraints to apply.

permanent magnet excitation

Reviewer #1:

Buskirk et al. examined the evolution of nontransitive fitness effects in yeast. They showed that during evolution in rich glucose medium, a late clone (1000 generations) outcompeted an intermediate clone (300 generations), but lost in direct competition with the ancestor (in a frequency-dependent fashion: late clone when rare loses to ancestor and when abundant outcompetes ancestor). This is due to adaptation in the nuclear genome and intracellular killer virus. Essentially, the ancestor expresses both killing and immunity phenotypes (K+I+), the intermediate clone expresses immunity (K-I+), and the late clone expresses neither (K-I-). This trend is observed in many evolving populations. In the absence of the killing interaction, virus does not affect host fitness. That is, when killing interactions are absent, fitness changes are due to mutations in the nuclear genome. Changes in killing and immunity phenotypes are driven by intracellular competition of viruses where viruses defective in killing and/or immunity have an advantage over functional viruses.

This work demonstrates that evolution may not be a simple linear march of progress. Rather, progresses over short time scales can sometimes lead to a reduction of fitness over the longer time scale due to ecological interactions. I find the work quite interesting, although I also find it a bit incomplete.

What are the nuclear mutations that made intermediate clones more fit than ancestor and late clones more fit than intermediate clones? I think that giving one example for both cases will be helpful.

A schematic summary figure will be helpful.

Reviewer #1:

This is an interesting translational and comprehensive study which examines cellular and genetic mechanisms involved in the diversity of corpus callosum dysgenesis (CCD) phenotypes. Using mouse models and human cohorts with a spectrum CCD, it is found that the extent of aberrant interhemispheric fissure (IHF) remodeling predicts commissure dysgenesis severity. Elegant neuroanatomical experiments show that abnormal proliferation/migration of midline zipper glia (MZG) progenitors underlies aberrant IHF remodeling. Thus, in addition to genetic perturbations linked to aberrant callosal axon guidance in humans and mice (i.e. variants in DCC guidance cue receptor gene), disruption to IHF remodeling also causes CCD. Indeed, an 8-base pair deletion in the DCC receptor ligand, Draxin, which is expressed in MZG, associates with CC malformations in mice. The findings are novel and important to both basic and clinical scientists.

Below are comments and suggestions that need to be addressed:

1) Introduction:

-More detailed information about the BTBR mouse line and the rationale for using the BTBR x C57 mouse cross should be provided.

-The main question addressed in the study should be clearly stated.

2) Methods:

The Statistical analysis section needs to provide a more detailed description of the statistical tests that were used and the reason why these tests were chosen.

3) Results:

In general, the description of the statistical results lacks important details. For example:

-For figure 1, there is very little information about statistical analysis. For figure 1 C, it needs to be explained why a Welsh test was used instead of a one-way ANOVA. The errors on the bars do not seem to correspond to SEM, this needs to be clarified.

-For figures 3 G and H, if the data are presented in single graphs, it is not clear why unpaired t tests or Mann-Whitney tests were conducted (instead of ANOVAs). Why a non-parametric test was used is not explained.

-The description of the findings that prompted the authors to investigate the role of Draxin in CCD needs to be clearer.

-The references to the different panels of Figures 5 and 4 need to be revised in the Results section.

-It is not clear what is the impact of the Draxin deletion to IHF remodeling. There seems to be an effect shown in one of the supplementary figures (in BTRB mice), but there is no discussion in this regard. This is particularly important considering that Draxin is expressed by MZG.

-It seems that the Draxin deletion does not affect HC formation. However, at some point in the Results section it is stated "To investigate how DRAXIN regulates CC and HC formation...". This is confusing. It seems that the effect varies between BTRB mice and the BTRB x C57 cross, but this is not discussed clearly.

-Figure 7 should indicate the mouse genotype on the actual figure to avoid confusion.

-The study by Vosberg et al, 2019 in Annals in Neurology needs to be included when referring to studies linking DCC variance and CC dysgenesis in humans.

Minor Comments:

The organization of the manuscript could be improved to increase its clarity. The authors may want to consider moving the Draxin findings to the last part of the Results.

Reviewer #1:

The authors use a tetracycline controlled gene expression system to compare the effectiveness of two difference promoters to express channelrhodopsin in different populations of retinal neurons with the goal of rescuing visual function in mouse models of photoreceptor degeneration. The expression patterns of two promoters were compared - the first a muscarinic AChR (referred to as M4 in the manuscript) led to expression in a subset of RGCs and a subset of amacrine cells, while the second a 5-HT receptor (5B) led to expression in a subset of RGCs only. In the M4 line, the amacrine cells that were labeled were a subset of starburst amacrine cells located in the INL and did not label the SACs displaced in the GCL. Also, it was a subset of the INL-SACs. To assess the impact of these different expression patterns on vision restoration, mice expression ChR under these two different promoters were treated with MNU to induce PR degeneration. The light responses restored by ChR were assessed with a MEA recordings cortical VEPs and behavior. The M4 promoter had stronger light evoked responses. The authors used pharmacology to assess how the M4 retinal circuit might explain the enhanced light response.

There were several fundamental problems with the manuscript that need to be addressed. These problems range from experimental design, interpretation of findings, some mistakes in description of retina circuits. Moreover, there is no context given comparing these results to the multiple other studies on vision restoration impact on visual-guided behaviors. These problems are listed here:

1) The choice of promoters and expression patterns need to be further explored. The motivation for a particular subtype of mAChRs and 5-HT is not given. Though M4 and 5b drives expression in roughly the same percentage of total RGCs, there is no way to know whether they drive expression in the same subtypes of RGCs. Hence differences in firing patterns are not likely to be fully explained by the fact that M4 promoter also drives expression I a subset of INL-SACs.

2) The observation that M4 drives expression in a subset of OFF SACs was quite intriguing. Though there are ways to distinguish ON from OFF SACs, this is the first example of which I am aware that a subset of OFF-SACs is labeled. Does this mean only a subset of OFF-SACs have mAChRs? Or was this reflective of the partial express induced by Tet? It is worth the authors quantifying the percent of OFF-SACs labeled in the M4 mouse line.

3) The observation that they are able to rescue the OKR result in MNU treated mice using the M4-promoter is impressive. Again, the authors conclude that this is due to presence of ChR in INL-SACs but it could be they also have ChR expression in direction selective ganglion cells themselves. Hence the rescue is impressive, it is difficult to interpret. Also, this important behavior is confined to a supplemental figure.

4) The authors conclude that M4-driven expression of ChR rescues the OKR in MNU-treated mice and not rd-mice because the rd mice have a "thinner INL" and therefore may have a depletion of INL-SACs. This appears to be an easy test for the authors using immunofluorescence.

5) The authors do some pharmacology to test whether SACs are the basis of the larger sustained response observed in M4 vs 5B . However, the assumptions/interpretations for these experiments are based on some mistakes regarding retinal circuits. SACs release GABA and acetylcholine. However, the pharmacology they do is quite limited. Namely they use TPMPA, which blocks GABA-C receptors which are found on a subset of bipolar cell terminal and by no means represent the major source of GABAergic signaling in retina which is via GABA-A and GABA-B receptors. Similarly, the authors assess impact of ACh release by using atropine, which blocks muscarinic receptors but not nicotinic ACh receptors. Finally, the authors use MFA, a blocker of gap junctions, which does have clear impact on sustained responses. However, SACs are not thought to be gap junction coupled to anything. So, it is more likely MFA is acting via RGC-RGC gap junction coupling or having an off-target effect. Much more needs to be done to have a complete understanding of the circuits that mediate the ChR-mediated light responses.

6) 226-227 - what is the conclusion - results suggest not due entirely to gene transfer? This needs further explanation.

7) Comparison of light induced responses in MNU vs non MNU treated rather confusing. Authors should consider revising this point.

Reviewer #1:

Santos and Sirota developed a novel Tetrode-based Amperometric ChOx (TACO) sensor. This multichannel configuration can simultaneously measure the ChOX activity (COA) and O2 in the same brain spot. Using the TACO sensor in freely-moving and head-fixed rodents, they found that COA and O2 dynamics following locomotion in active state and hippocampal sharp-wave/ripple (SWR) complexes during quiescence state. It's interesting that the COA signal can be calibrated by subtraction of the pseudo-sentinel from the Ch-sensing sites signal the TACO sensor. However, the COA signal is confounded by phasic O2 fluctuations, so, the authentic changes in COA are interfered by O2-evoked enzymatic responses. This question isn't addressed in this paper.

Major concerns:

1) The author found that the COA readout is confounded by phasic O2 fluctuations in in vitro and in vivo experiments. These results cast doubt on the validity of the authentic cholinergic response in freely-moving or head-fixed rodents. These findings seem to be generalized to other oxidase-based biosensors, although the author has some discussion on how to address this question. However, we can't get authentic cholinergic dynamic in vivo by TACO biosensor if we didn't clear the biosensor O2 dependence. So, the author should try to address this question.

2) The author should demonstrate how to calibrate moving artificial signals in freely-moving rodents.

3) Concerns on the selectivity. Figure 1E shows the TACO sensor also responses to dopamine and ascorbate. The author should demonstrate the selectivity of TACO sensor on different monoamines at different concentrations.

Reviewer #1:

Using a simulation approach, the authors investigate the impact of removing group members likely to possess key social or ecological information on the topology of elephant social networks in order to better understand how poaching pressure may influence their resilience and functionality. Removals were based on three metrics thought to correlate with an individual's knowledge (age, degree, betweenness centrality) and compared to random removals for both an empirical network and virtual networks. Whereas targeted removals based on age had relatively limited impact on networks characteristics, removal of socially central individuals led to less integrated networks with potential consequences for the spread of adaptive information.

The manuscript was generally clear and well-written. The introduction nicely laid out the rationale for this study and the authors do a nice job walking the reader through the steps of the simulation (how the networks were constructed, how deletions were performed, etc.). I also appreciated the discussion given to the limitations of their approach, such as the lack of network restructuring in response to removals.

1) My main critique is that I believe the authors should be more cautious in attributing functional meaning to their network metrics, particularly given that data was unavailable to allow them to simulate a transmission process. For example, at L461-463, it is stated that targeted removal of individuals with high betweenness decreased the speed of information flow, but what was actually found was that values for weighted diameter increased. Put another way, weighted diameter provides an indication of how rapidly information could potentially flow, but not whether it in fact does so. The actual dynamics of information flow are going to depend on the nature of the information and how it is transmitted among individuals, as the authors note in the discussion (L627-640). I believe that the results should be reworded to focus more on what was actually found (i.e. changes in network metrics), with the potential functional relevance of those changes then examined in the Discussion.

2) In addition, I couldn't see if this was addressed anywhere, but is there empirical evidence to suggest that the mature elephants that possess high-quality information are those characterized by high degree or betweenness?

Thank you for the interesting read!

Reviewer #1:

The manuscript from Quiroga and colleagues reports a function for the mechanosensor Piezo 1 in myocyte fusion. The manuscript concludes via a series of in vitro experiments that Piezo 1 knockdown results in decreased myotube formation.

While overall the manuscript reports some potentially interesting observations, the main conclusion seems preliminary and the work would benefit from substantial additional validations in multiple models to strengthen the tie between myomaker and Piezo1 functions.

Major Comments:

1) siRNA reduces gene expression in a transient manner and it is unclear for how long there is significant silencing of Piezo1 RNA during differentiation. Therefore, a more consistent model that expresses consistent amounts of Piezo1 might be beneficial. Importantly, a more stable mutant form of Piezo 1 (generated with CRISPR/Cas9) was generated in a previous study (Tsuchiya et al, 2018, ref. 17). The long-term consequences of differentiation/fusion of myogenic cells following loss of Piezo 1 expression in the Tsuchiya study reached opposite conclusions to the current study. These findings raise concerns that are not clearly addressed in the present study. While the authors attempt to explain the opposite findings by the use of a different Piezo 1 silencing model, it is difficult to reconcile with the present data the very opposite findings.

2) Figure 3A and C have duplicated images showing siRNA of Piezo 1 in EDL and Soleus. The correct images need to be inserted.

3) Quantification of proteins levels downstream of Piezo silencing should be corroborated by western blot analyses. These include data presented in Figures 2 and 3.

4) In Figure 4, it would be helpful to include a graph illustrating the amount of Piezo1 silencing and the corresponding decrease in Myomaker expression.

5) In Figure 6, expression of myomaker and myomixer should be monitored following administration of Yoda1. If Yoda1 increases fusion at low concentrations, the fusion genes should be upregulated in expression.

6) In Figure 7 the myotube width should also be accompanied by quantifications of numbers of nuclei fused in the myotubes. This data will address whether cell fusion changes following Yoda1 treatment.

7) While the present work explores the function of Piezo 1 in myogenesis in vitro, no experiments address a potential parallel function of Piezo1 in vivo. Supporting data using injured/regenerating muscle should strengthen the overall message.

8) Figure 9 proposes an interesting hypothesis linking Piezo 1 to FSHD. However, the hypothesis is not supported by experimental data and remains rather exploratory in its current form.

Reviewer #1:

Taken collectively, the findings described in the manuscript provide a new perspective on how LAP2alpha influences the state of A-type lamins. By extension, one impact of the findings is that they provide a mechanism by which A-type lamin state is distinct within the nucleoplasm and at the nuclear lamina. The authors also arrive at some additional insights that are valuable. For example, the data supporting the initial peripheral localization of what is argued to be pre-lamin A during processing rather than filament assembly was interesting and, although indirect, largely convincing. I would encourage the authors to address the fact that this work drives a reinterpretation of their prior findings early in the paper. I also have some concern that the impact of the findings is somewhat narrow.

Major points:

1) Given that a major focus of the paper is to explain conflicting results with (the same group's) prior published data on the effect of LAP2alpha depletion, it would have helped to lay this out more clearly from the outset of the paper. As written, the reader is confused until arriving at Figure 3. I appreciate that resolving this conflict leads to a new perspective - namely that LAP2alpha influences the state of the lamin assembly in a way that disrupts its detection by the N18 antibody, but structuring the manuscript to get to this point as quickly as possible would improve its accessibility.

2) I found the plots in Fig. 1A and B confusing. Can the authors clarify how the measurements are achieved - through ROIs for the entire nucleoplasm/periphery? How do they capture the diffuse versus focal signal within the nucleoplasm? There is also some concern that the nucleoplasmic signal may simply be too low to detect robustly at early time points (leading to an increase at later time points as the protein accumulates). Line profiles (which are useful in Fig. 3) would be very helpful if used more broadly for assessing the data particularly for Figure 1.

3) Related to Figure 1 - the results for the deltaK32 mutant is essential for the interpretation and should be included in the primary figures.

4) The authors make no comment on the functionality of the mEos-tagged lamin A/C CRISPR lines. However, the comment suggesting that some clones could have altered nuclear morphology (line 225) raises some questions. How did the authors interpret this? Were these clones in which there were indels in some lmnA alleles affecting the levels? Or is this a consequence of the fusion? How do the authors explain the relatively low expression level of the mEos fusion relative to the untagged? If the MDFs are diploid, presumably we would expect this to be one allele tagged and one allele untagged. Given that the expression ratio is very different from this, could the tagged lamin A/C be targeted for degradation? As these cell lines are critical for the rest of the study, this information is important.

5) How does the deltaK32 mutation affect the ability to detect lamin A/C with the N18 antibody? Could this provide further insight into the impact of LAP2alpha by extension?

6) Greater explanation for the apparent paradox between the increase in immobile fraction by FRAP and the increased diffusion coefficient by FCS in the LAP2alpha-depleted condition is needed. The authors suggest that the latter is due to the loss of LAP2alpha binding (line 395), but some modeling would go a long way here. What form are the lamins thought to be in, and how does the bulk that LAP2 alpha would bring match the apparent changes in diffusivity?

7) One prediction that arises from the proposed model is that regulation of LAP2alpha levels will modulate the relative pool of A-type lamins at the nuclear interior versus the nucleoplasm. Beyond the knock-out cells, is there any other evidence of this relationship?

8) Much of the biochemical characterization seems confirmatory - e.g. the binding and gradients in Fig. 5A and B. Use of the assembly mutants of lamin here could be informative is essential to interpret the changes induced by addition of LAP2alpha.

9) With regards to the effects on chromatin mobility - over what time interval was the volume of movement observed? This is important because more fluctuations in nuclear position, for example, could influence this measure. In addition, telomeres are a confusing choice, given abundant evidence that there is crosstalk between the state of the nuclear lamina and telomere biology (e.g. lamin mutants affecting telomere homeostasis, etc.). At a minimum, acknowledging that telomeres may not reflect the effect on chromatin globally is important. Examples of the raw mean squared displacements would be more informative. Is the difference between lmna KO and lmna/Lap2alpha DKO (Fig. 6 right panel) significant?

10) How do the authors think the membrane integrated LAP2beta fits into the story?

Reviewer #1:

This is a rigorous and very interesting study on a timely topic: combining modeling traditions of (reinforcement) learning and decision-making. The central claim of the paper is that the often-used combination of reinforcement learning with the drift diffusion model does not provide an adequate model of instrumental learning, but that the recently proposed "advantage accumulation framework" does. This claim will likely be of interest for anyone studying learning and decision-making, ranging from mathematical psychologists to neuroscientists running animal labs. I have a number of concerns regarding this paper.

1) I think the basic behavior and model fit quality should be better described. The reinforcement-learning + evidence accumulation models (RL-EAM) are fitted to choices and reaction times (RTs). I find it therefore odd that we don't get to see any actual RT distributions, but only the 10th, 50th and 90th percentile thereof. What did the grand average RT distribution and model predictions look like (pooled across subjects and trials)? How much variability was there across subjects? I understand that that model was fit hierarchically, but it would be nice to (i) see a distribution of fit quality across subjects, to (ii) see RT distributions of a couple of good and bad fits, and to (iii) check whether the results hold after excluding the subjects with worst fits (if there are any outliers). Related, in the RT percentile plots (Figures 3 & 4), it would be nice to see some measure of variability across subjects.

2) The authors pit four competing RL-EAMs against one another. I have a number of issues with the way this is done:

-The qualitative model fits presented in Figure 3 are potentially misleading, as the competing models have different numbers of free parameters: DDM, 4; RL-RD, 5; RL-IARD, 5; RL-ARD: 6. RL-ARD has most free parameters, which might trivially lead to the best visual fit. For this reason, I find the BPIC results more compelling, and I think these should feature more prominently (perhaps even as bars in the main figure?).

-All three racing diffusion models implement an urgency signal. Why did the authors not consider a similar mechanism within the DDM framework? Here, urgency could be implemented either as (linearly or hyperbolically) collapsing bounds, or as self-excitation (inverse of leak); both require only one extra parameter.

3) I could imagine a scenario in which the decision-making process becomes progressively biased toward the more rewarding stimulus. In fact, this can be observed in Figure 7. Therefore, I wonder if the authors have considered RL-AEMs in which the choice boundaries do not correspond to correct vs. error, but instead to the actual choice alternatives (stimulus A vs. B). In such an implementation one can fit bias parameters like starting point and/or drift bias.

4) The authors write that RL-AEMs assume that "[...] a subject gradually accumulates evidence for each choice option by sampling from a distribution of memory representations of the subjective value (or expected reward) associated with each choice option (known as Q-values)." Sampling from a distribution of memory representations is a relatively new idea, and I think it would help if the authors would be more circumscribed in the interpretation of these results, and also provide more context and rationale both in the Introduction and Discussion. For example, an interesting Discussion paragraph would be on how such a memory-sampling process might actually be implemented in the brain.

Reviewer #1:

This article investigates how uncertainty about the value of alternatives affects the decision process through the lens of the drift diffusion model. The article proposes several models for how uncertainty might affect the drift rates or diffusion variance, and tests those models on four different food-choice datasets. The authors conclude that the best model is one in which the drift rate depends on the values of the options divided by their degree of uncertainty.

I think the article is pursuing an interesting question. The core set of results are perhaps not as surprising or as puzzling to a DDM audience as the introduction might have you believe, but from there the paper does a nice job of exploring different ways in which uncertainty might affect the choice process. This seems like a good set of models to consider, as they cover the obvious ways in which one might consider incorporating uncertainty into the DDM, and each one, except for the favored Model 4, has a clear inability to capture a facet of the data.

1) I could quibble about why the authors don't explore more variants of the favored Model 4, for example ones where the values are divided by non-linear functions of the uncertainty measure (e.g. squared or square root)? The results in Figure 4 are not a slam dunk for Model 4, as the effect of dC seems to outweigh C, while in the data it is the opposite. I don't think this is critical, but the authors might try an extra exponent parameter on uncertainty in Model 4. At minimum, the authors should discuss how they might modify Model 4 to better match the data.

2) As I alluded to above, I think the article somewhat mischaracterizes the DDM by saying that "the most straightforward way to include option-specific noise in the preferential DDM - by assuming that noise increases with value uncertainty - leads to the wrong qualitative predictions..." "Most straightforward" is subjective. The standard diffusion model sets the diffusion noise variance to a constant, and so no, adjusting the noise is not "straightforward"; in many DDM software packages it is not even an option. Instead the effect of uncertainty would show up in the drift rate (or boundaries), as it does here. So, I would urge the authors to temper their claims in the introduction and discussion about what the "straightforward" model would be. Many researchers who use the DDM think about the drift rate as a signal-to-noise ratio, and for them Model 4 would have been the straightforward model.

3) This isn't to say that what the article does isn't interesting or important. A standard DDM analysis would just fit different drift-rate and boundary parameters to high and low uncertainty conditions and then report the differences. This article takes a more elegant approach by explicitly modeling uncertainty in the DDM components. This is why I would urge the authors to do a bit more with that aspect of the paper, to try to better understand how uncertainty impacts the drift rates.

4) On Page 16 - the authors write "in line with the best fit parameters". What exactly do they mean here? Did they use the best-fitting parameters or not? Could the authors add a table to the supplements with the average best-fitting parameters for each model, for each dataset? That would greatly help in understanding the results.

5) Figure 4 - how were the experimental data and model simulations combined to generate these figures? For the data, was this one big mixed-effects regression including all datasets? How did the authors handle the random effects in this case, given the multiple datasets? The simulations are also vaguely described. How "similar" were the input values to the data; how exactly were these input values generated? Again, how were the simulations from different subjects/studies combined to generate a single plot per model? It would be useful, though not strictly necessary, to see the basic behavioral results broken down by study (in the supplements). It is unclear how consistent the patterns in Figure 2/4 are across the studies.

Reviewer #1:

This MEG study by Griffiths and colleagues used a sequence learning paradigm which separates information encoding and binding in time to investigate the role of two neural indexes - neocortical alpha/beta desynchronization and hippocampal theta/gamma oscillation - in human episodic memory formation. They employed a linear regression approach to examine the behavioral correlates of the two neural indexes in the two phases, respectively and demonstrated an interesting dissociation, i.e., decreased alpha/beta power only during the "sequence perception" epoch and increased hippocampal theta/gamma coupling only during the "mnemonic binding" phase. Based on the results, they propose that the two neural mechanisms separately mediate two processes - information representation and mnemonic binding. Overall, this is an interesting study using a state-of-art approach to address an important question. Meanwhile, I have several major concerns that need more analysis and clarifications.

Major comments:

1) The lack of theta-gamma coupling during the stimulus encoding period is possibly due to the presentation of figure stimulus, which would elicit strong sensory responses that mask the hippocampus activity. How could the author exclude the possibility? In other words, the dissociated results might derive from different sensory inputs during the two phases.

2) About the hippocampal theta/gamma phase-power coupling analysis. I understand that this hypothesis derives from previous research (e.g., Heusser et al., 2018) as well as the group itself (Griffiths et al., PNAS, 2019). Meanwhile, MEG recording, especially the gradiometer, is known to be relatively insensitive to deep sources. Therefore, the authors should provide more direct evidence to support this approach. For instance, the theta/gamma analysis relies on the presence of theta-band and gamma-band peak in each subject. Although the authors have provided two representative examples (Figure 3A), it remains unknown how stable the theta-band and gamma-band peak exist in individual subject.

3) Related to the above comment, the theta-gamma coupling is a brain-wide phenomenon including both cortical and subcortical areas and not limited to just hippocampus. Although the authors have performed a control analysis to assess the behavioral correlates of the coupling in other regions, the division of brain region is too coarse and I am not convinced that this is a fair comparison, since they differ from hippocampus at least in terms of area size in the source space. The authors could consider plotting the power-phase coupling distribution in the source space and then assessing their behavioral correlates, rather than just showing results from hippocampus. This result would be important to confirm the uniqueness of the hippocampus in this binding process.

4) About behavioral correlates. The current behavioral index confounds encoding and binding processes. Is there any way to seperate the encoding and binding performance from the overall behavioral measurements? It would be more convincing for me to find the two neural indexes at two phases predict the two behavioral indexes, respectively.

5) The author's previous works have elegantly shown the two neural indexes during fMRI and intracranial recording in episodic memory. The current work, although providing an interesting view about their possible dissociated functions, only focuses on the memory formation period (information encoding and binding). Given previous works showing an interesting relationship between encoding and retrieval (Griffith et al., PNAS, 2019), I would recommend the authors to also analyze the retrieval period and see whether the two indexes show consistent dissociated function as well.

Reviewer #1:

In this manuscript, the authors revisit DCC and NTN1 mutants in order to better define the basis for midline crossing defects. This group recently demonstrated that midline zipper glia (MZG) must migrate along the interhemispheric fissure (IHF) and intercalate across the midline while remodeling the meningeal basement membrane to provide a substrate for callosal axons to cross the midline. In this study, they show that DCC and its ligand NTN1 are required for proper midline zipper glia (MZG) distribution/morphology along the IHF, proper remodeling of the basement membrane, and subsequent corpus callosum (CC) formation. The data in figures 2 and 3 generally do a nice job of supporting the model that DCC and NTN1 are expressed in MZG and that the morphology and distribution of MZG are affected in DCC/NTN1 mutants. There appear to be some defects in MZG migration that may account for this (Figure 4). Due to technical limitations, the author's attempt to use a conditional knockout of DCC to genetically dissect whether CC formation defects are due to defects in MZG or callosal axons are a bit inconclusive (Figure 6). Finally, the paper ends with experiments showing that mutations in DCC identified in acallosal patients are loss-of-function using an in vitro cell morphology assay (Figure 7 and 8).

The authors are commended for the quality of their imaging data and for being as quantitative as possible when measuring their in vivo phenotypes, which is not often done with these types of studies. There are few issues that need to be addressed.

Major points:

1) In Figure 4, in addition to the migration defects of Sox9+ MZG, there seems to be a rather large increase in the total number of Sox9+ cells along the IHF by E16 (more than 2 fold, Figure 4G). The authors show there is no change in cell cycle or apoptosis of these cells in the supplemental data (Figure S4), so what accounts for this increase? Is this also seen with NFIA/B staining at E16?

2) Regarding the attempt to distinguish between DCC in MZG versus callosal axons (Figure 6), the incomplete deletion/loss of DCC protein (Figures 6C, I, J) is a bit concerning. It's not clear to me why this would happen, but it confounds the interpretation of the results. While the authors state "The severity of callosal agenesis was associated with the extent to which the IHF had been remodeled" (pg 15), they don't actually quantify this. It might be informative to generate scatterplots of IHF length vs. CC/HC length to determine if there is a significant correlation between the two. This might lend more evidence to a causal relationship between IHF remodeling and CC/HC formation.

3) At the end of the result section, the authors state: "mutations that affect the ability for DCC to regulate cell shape (Figure 8F), are likely to cause callosal agenesis through perturbed MZG migration and IHF remodelling." (pg. 19). While the authors nicely show that patient mutations in DCC affect the morphology of cells in cell lines (Figure 7-8), it is not clear why simply transfecting WT DCC into cell lines results in such a dramatic change in morphology, or why addition of NTN1 doesn't increase this. The authors mention that the cell lines could express NTN1 or that NTN1 is not required for the effect. This seems an important distinction. Did the authors check this? Could they use a function blocking antibody or a soluble fragment of the NTN1 binding domain of DCC to block NTN1:DCC interactions? DCC has been shown to function as a "dependence receptor" that can induce apoptosis in the absence of ligand; are the authors certain that the morphology changes they are seeing in DCC transfected cells aren't cytoskeletal changes resulting from caspase activation?

Minor points:

1) The authors should mention recent work showing Netrin localization to basement membranes during axon guidance (Varadarjan et al, Neuron 2017). The data in Figure 2 are very much in agreement with this previous work, and it should be mentioned in this context.

2) Figure S5A: Representative images from each genotype don't look comparable, even though there's no difference in quantification.

3) Did the authors check whether the cell lines they used in Figure 7-8 express DCC?

Reviewer #1:

This manuscript investigates TE diversity and variation across several clades of bdelloid rotifers, which are particularly interesting from an evolutionary perspective since they reproduce asexually. As stated by the authors, theory predicts that asexuality may lead to two opposite outcomes in terms of TEs content. In the absence of sex, TEs may not easily jump into new genomic backgrounds where they are not repressed, leading to a decline in TE content. On the other hand, there is no recombination without sex, which removes the selective pressure against TEs due to their involvement in ectopic recombination. The authors show that despite these extreme expectations, asexual rotifers do not seem to display any of these patterns, although recent insertions seem rare and possibly brought through horizontal transfers. They do not observe any clear effect of adaptation to desiccation on TEs content, which seems to exclude any effect of enhanced DNA repair mechanisms in controlling TEs. They observe less LINEs and more (recent) DNA transposons in bdelloid rotifers, which is consistent with the absence of sex (limiting LINEs spread) and horizontal transfers (more frequent for DNA transposons). The expansion of RNAi gene silencing pathways suggests that asexuality comes at a cost, such as the proliferation of TEs, the accumulation of genetic load, and the control of horizontal gene transfers that might be deleterious. I think this supports the hypothesis of strong TEs activity associated with the onset of asexuality, leading to a strong evolutionary response. This suggests that these clades survived the arms race with TEs. This work shows how intricate the coevolutionary dynamics between TEs and their hosts can be. The manuscript is well-written, analyses are sound and detailed. I have a few general comments/questions that I detail below: Horizontal gene transfer: given the abundance of recent DNA transposons in some clades (class I), it may be worth discussing a bit more this possibility (at this stage it is mostly discussed in the Conclusion).

If my understanding is correct, there is no assessment of TEs or SNPs heterozygosity for each individual. This might be interesting to explore. If TEs are deleterious recessive, one might observe more frequently at the heterozygous state. For intraspecific data, it may be interesting to look at how nucleotide diversity varies along the genome. Since variable recombination may be associated with diversity due to the effects of selection at linked sites, checking diversity along the genome may bring another layer of information about the frequency of sexual reproduction and its effects on TEs diversity. I acknowledge that this would be a rather exploratory analysis, and am not asking the authors to carry it, but I am curious to know how do methods designed to estimate effective recombination rates perform on these data (e.g. LDHat, or more recently iSMC for a single diploid genome).

Question related to demography and selection: would it be possible to obtain estimates of the effective population size for these clades? It would be interesting to have such an estimate to get an idea of the efficiency of purifying selection against TEs, and whether Muller's ratchet could explain the current abundance of TEs (in the case of moderate/small effective population sizes). I liked the idea of using the ABC to test for consistency with asexuality, but am wondering to what extent it is biased by non-constant transposition rates, which cannot be properly modeled by the coalescent simulation? I would also assume these simulations do not take into account past changes in demography (I believe this option has not been included in the software yet). This is not necessarily a major issue for me, as long as these limitations are mentioned. When presenting the ABC framework in the Methods section, you may want to give more details about the part carried with the abc package itself (e.g. which regression/rejection algorithms were used, etc.).

A few other comments linked to specific paragraphs/sentences:

• L419: why choosing LTR-Rs in particular (abundance and the fact they are not class I I guess).
• L450: Would it be possible to obtain a time in generations from, e.g., an approximate mutation rate?
• L455: Would it be possible to call heterozygote SNPs/elements?
• L550-656: do you examine the most recent elements only? It may be interesting to check these correlations for elements of different ages, since selection may have had the time to act on the most ancient TEs.
• L642: It might also be that longer elements display functional regulatory/promoter regions, and have a stronger impact on fitness.
• L725: I liked this part, but wondered if a slightly more detailed discussion was possible. As the authors state, the expansion of RNAi pathways is consistent with a control mechanism against TEs. It is important to detail alternative explanations since there is no functional evidence in this model that this expansion actually controls TEs proliferation (unless I missed something). Given the rather unique properties of these organisms, it may be worth discussing.

Reviewer #1:

This paper presents a very interesting set of techniques (monocular and binocular visuomotor tracking) to evaluate subtle differences in visual processing as a function of luminance.

Despite some technical caveats I'll explain below, the paper fairly convincing demonstrates that the monocular visuomotor tracking task can be used to identify millisecond-scale differences in visual processing lags, e.g. caused by different levels of luminance. The basic experimental analysis and comparison to traditional approaches were fairly thorough and convincing.

The binocular tracking component was less convincing, and the data were messy (which the authors acknowledge). Unfortunately, the very small sample size (N=5), lack of attention to trial order effects and learning of this new task, etc, reduce enthusiasm about this part of the paper.

While this seems like a solid paper in most respects, it seems it’s primary focus is to demonstrate that a 'new' technique visuomotor tracking (which is not new per se, but may be new in this field), gives results on delay estimation that are indistinguishable from traditional psychophysical techniques. This new approach requires fewer experiments and uses the richness of the full time series for analysis. The basic approach is near and dear to my heart in that it uses continuous-time system identification to really extract rich information.

However, while I think the technique (which I quite like) is promising, I do not know what the new finding is. The analysis also only scratches the surface. I think this is a solid, field specific paper that verifies a new method and, despite its technical contributions, may be suitable for a field-specific readership, with modest effort to address or at least acknowledge the technical limitations.

Technical Limitations:

1) The visuomotor behavior is not new; continuous tracking moving stimuli is an age-old process. What is potentially new here is the use of this behavior for identifying subtle differences in delay. For a fairly old review with several papers cited in this area, see:

Roth, S. Sponberg, and N. J. Cowan, "A Comparative Approach to Closed-Loop Computation," Curr Opin Neurobiol, vol. 25, pp. 54-62, 2014

But there are many (much older) papers dating back for example to McRuer on visuomotor tracking tasks for identifying control systems in human visumotor control, including careful analysis of visuomotor delay.

For a recent paper (in a non-human system) for detecting differences in delay, see:

Luminance-dependent visual processing enables moth flight in low light Sponberg et al, 2015, SCIENCE 12 JUN 2015 : 1245-1248

2) There are no error bars. With 40 trials per condition, a simple SEM may be sufficient.

3) The binocular data highlights a general problem which is that people need to learn this task, and if you are doing system identification during learning, you are doing system ID on a time varying system. This sounds like a confusing task and I agree with the authors that "higher level cognitive processes" are probably taking place but more importantly the learning system is not in steady state even after that many trials.

4) Very importantly, unlike the traditional psychophysics trials (which are based on perception not motor output), this data must be analyzed as a closed-loop system. There are now two pieces of visual information: exogenous reference and self-movement feedback. It is extremely likely that these are processed differently, via feedforward and feedback controllers. See these papers ... These are very new, so I wouldn't have expected the authors to know about them, but they will still be useful for understanding this concept and improving your analyses:

Yamagami, M., Howell, D., Roth, E., & Burden, S. A. (2019). Contributions of feedforward and feedback control in a manual trajectory-tracking task. IFAC-PapersOnLine, 51(34), 61-66.

Yamagami, Momona, et al. "Effect of Handedness on Learned Controllers and Sensorimotor Noise During Trajectory-Tracking." bioRxiv (2020). https://www.biorxiv.org/content/10.1101/2020.08.01.232454v1

That said, the highest-frequency responses - those picked up in the earliest moments of the impulse response function - are largely "open-loop", a fact that can be verified by noting that in the frequency domain, there is a very low gain (which is almost surely true with this data as it is in all other visuomotor tracking data across species that I am aware of, and that fundamentally must be true to ensure stable tracking!). So, the observations about short-time-scale (i.e, high frequency) differences being attributed to differences in the visual processing, are likely substantiated. But a more nuanced and accurate description of the theoretical basis for this is warranted.

5) One second is not steady state in human visuomotor tasks. Tracking bandwidth for visuomotor behavior is in the ballpark of around 0.5-2Hz, which means there is still significant phase lag at 1 Hz. So the 11 second trials, with the first second thrown away does not necessarily "erase" initial conditions. As one example, see a recent paper (again I wouldn't have expected you to know this, but it still shows 1 second is not long enough):

Zimmet, A. M., Cao, D., Bastian, A. J., & Cowan, N. J. (2020). Cerebellar patients have intact feedback control that can be leveraged to improve reaching. eLife, 9, e53246.

In Fig 4S2 in that paper you see that the phase lag at 1Hz is well over 90 degrees. Always wait 10 seconds to be certain, since at 0.1Hz, the phase lag is very low.

6) Perhaps most fundamentally, lag and delay are not the same thing. Delay induces a very specific time shift, but it should be noted that in a closed-loop system one can NOT just shift the closed-loop cross-correlation function (equivalent to the impulse response in this case due to the noise input). If the delay were only on the measured target signal, and not on the feedback of self-motion, then indeed a simple time shift would be adequate; but there is a complex and subtle "compounding" of the feedback delay in closed-loop that leads to a distortion, not a simple shift, of the impulse response function. These papers show different ways on how to estimate delay differences in closed loop correctly:

Luminance-dependent visual processing enables moth flight in low light Sponberg et al, 2015, SCIENCE 12 JUN 2015 : 1245-1248

Zimmet, A. M., Cao, D., Bastian, A. J., & Cowan, N. J. (2020). Cerebellar patients have intact feedback control that can be leveraged to improve reaching. eLife, 9, e53246.

I love the first paper's method, but it is not always applicable. I think it may be applicable in this case where one may be able to assume nothing changes but the delay.

Reviewer #1:

The manuscript describes analyses of genomic data to study the population structure and demographic history of Brachypodium distachyon - a selfing Mediterranean grass species. Major findings include the existence of large-scale population structure (3 lineages), discordance between geographical occurrence and genetic relatedness (clades within the lineages), and at shorter scales, signs of dispersal without interbreeding. These patterns are explained by a combination of near-complete selfing and seed dispersal. The methods are appropriate, results well reported, and writing is good. As such, the paper provides interesting insights into the evolutionary history of B. distachyon, but due to its descriptive nature, I somewhat question the paper's value for a wider audience (i.e. people not directly working with B. distachyon). At points, the authors also engage in speculation (not supported by data) where I feel that more simpler population genetic processes are ignored.

In my opinion, the biggest weakness is the descriptive nature of the paper: it describes the genetic structure and demographic history of B. distachyon, but potential processes giving rise to the structure are only speculated. In particular, the authors invoke pre- and post-zygotic reproductive isolation (lines 384 - 387) and pathogen-driven frequency-dependent selection (lines 431 - 435) as potential causes for the observed structure. However, as the paper provides no evidence for such processes, it's not clear to me why they need to be invoked in the first place? Evidence for seed dispersal over relatively short spatial scales is shown (within populations in Italy, Fig 4), but to my reading the results suggest little dispersal/gene flow over long distances (only few individuals with increased heterozygosity or signs of admixture). Therefore, I believe that the simplest explanation for the genetic structure is founder effects (perhaps human-induces, given the peculiar differences within the A and B lineages) combined with the near-complete selfing. This would explain the emergence of the genetic lineages and the lack of interbreeding. Furthermore, I would imagine that the genetic groups are locally adapted (e.g. there's extensive local adaptation among the selfing populations of A. thaliana), which would ensure that one lineage/accession doesn't take over when otherwise feasible (e.g. within the B lineage). If the authors argue otherwise, I would like to see more convincing evidence and/or discussion supporting the invoked processes.

Below I list a few more specific comments:

Lines 26 - 27: "[our study] identifies adaptive phenotypic plasticity and frequency-dependent selection as key themes to be addressed with this model system". While reading the abstract this sentence got me interested and I expected at least some analyses addressing these topics. However, the only place where they are mentioned again are two highly speculative sentences at the end of the discussion (lines 427 - 435). Although the authors write "themes to be addressed", I think that the complete lack of evidence for adaptive plasticity or pathogen-driven frequency-dependent selection in the current study makes this sentence too misleading to be left in the abstract.

Lines 51 - 53: "For plants, genome-wide coalescence approaches have therefore been largely restricted to domesticated species and Arabidopsis thaliana". This might have been true some years ago, but not anymore. Just to highlight a few wild plant species (and studies) where demographic history has been studied using whole-genome data: A. lyrata (Mattila et al. 2017 MBE), A. arenosa (Monnahan et al. 2019 Nat Ecol Evol), Capsella genus (Douglas et al. 2015 PNAS, Koenig et al. 2019 eLife), Boechera stricta (Wang et al. 2019 Genome Biol), Populus genus (Wang et al. 2016 MBE, Hou & Li 2020 Front Plant Sci), Coclearia genus (Bray et al. 2020 bioRxiv), and many more.

Lines 383 - 387: "Flowering time differences are at best part of an explanation for genetic structure. In the scenario of subsequent lineage expansions we propose here, reproductive isolation might have evolved when the lineages were geographically isolated; and it might include other pre- and post-zygotic barriers in addition to flowering time, namely niche differentiation or genomic incompatibilities". These sentences kind of come out of nowhere. First, I don't fully understand the distinction between genetic structure and lineage expansions. If the latter is a process beyond population structure (i.e. incipient speciation), the paper shows no evidence of that. In fact, as I outlined above, I would imagine that founder effects and near-complete selfing is enough to cause and maintain population differentiation without reproductive isolation?

Lines 389 - 390: "Furthermore, differences observed in the greenhouse are most likely exaggerated through artificially short vernalization times. As our outdoors experiment shows, all accessions produced flowers within two weeks when they went through prolonged vernalization during winter". How representative are these vernalization times of the natural growing conditions? Large differences were observed in the greenhouse experiment, but the authors argue that these are not meaningful because the outdoor experiment showed little differences. However, a single experiment conducted in Zurich certainly does not capture environmental variation existing across the Mediterranean, so I'm not convinced that the role of flowering time can be ruled out so strongly based on these results. That said, the near-complete selfing suggests to me that flowering time is likely not a major factor underlying the genetic structure, and founder effects are a better explanation for it.

Line 548: Only one species (B. stacei) was used to define ancestral alleles in the fastsimcoal2 analysis. There are multiple studies showing that the use of a single outgroup, especially based on parsimony, leads to unreliable inferences of ancestral and derived alleles (e.g. Keightley et al. 2016 Genetics, Keightley & Jackson 2018 Genetics). In particular, this leads to overestimation of high-frequency derived variants, distorting the shape of the unfolded SFS. As the observed SFS has more shared high-frequency variants than predicted by the demography model (Fig S5), I imagine that this is an issue. FSC2 also works with the folded SFS, so I wonder why the authors chose to use the unfolded SFS? Unless there is a compelling reason, I suggest to either add more outgroups or to simply fold the SFS.

Reviewer #1:

This is an excellent study of centrosome polarization in the process of establishing immunological synapse and the effect of kinesin-4 on this process. The authors use a variety of microscopy techniques and controlled perturbations of the cell to obtain beautiful images that clearly suggest that kinesin-4, by increasing frequency of pauses and subsequent MT catastrophes, limits MT length, which assists dynein pulling in polarizing the centrosome. They complement the experiments with modeling based on Cytosim; the model supports the conclusions from the data, and suggests some interesting ideas.

I am not an expert in experimental techniques, though I understand what's been done, and in my limited opinion, the results are first-rate. The paper is well written and accurate. Modeling, which I know intimately, is done very well.. I have just a few minor comments:

1) I was not quite clear what does the modeling say about the centrosome sometimes being in apical position, and sometimes half-way between apical and basal positions.

2) I understand that 2d modeling cannot address this issue explicitly, but can the authors speculate about the apparent ring of MTs along the periphery of the synapse in the non-polarized case?

3) My perhaps most significant comment: the model nicely integrates and explains the data, but is it predictive? A detailed model like that clearly can generate some nontrivial prediction that could be experimentally tested.

4) "Interestingly, in our simulations, a small number of KIF21B motors was sufficient to prevent the overgrowth of the MT network." - this is a bit counter-intuitive: if the motor number is less than MT number, how would this work? Or, by a "small number of KIF21B motors" you mean still greater than ~ 100?

Reviewer #1:

In this work the authors measure the activity of the octopaminergic VUM neurons that arborize throughout the somatic body wall muscles in the Drosophila larva. They use three different larval preparations: isolated CNS (no sensory afferents), semi-intact (CNS exposed while maintaining sensory input), and intact. They find that isolated CNS has rhythmic waves of activity in the VUM neurons, but that semi-intact preparations do not show rhythmic VUM activity. They also show that "harsh" or "gentle" touch elicits different responses in VUM neurons.

There are several interesting findings. The ability of VUM neurons to show rhythmic activity in the isolated CNS is a novel finding. It would be even more interesting to register these waves to that of the glutamatergic body wall motor neurons that drive locomotion. It is also interesting that touch applied to an anterior segment results in elevated VUM activity in a posterior segment, and conversely posterior touch leads to elevated VUM activity in an anterior segment, suggesting that sensory input dampens VUM activity.

There are also issues that need to be addressed, which are listed below.

1) The function of the VUM neurons in locomotion was not tested, e.g. by silencing or activating them. These experiments would greatly strengthen the paper.

2) The three larval preparations are poorly described. (a) The fictive preparation is clearest but still should have a citation to Pulver 2015 at first use, as that paper provides a detailed description of the isolated CNS prep. (b) The semi-intact prep is not well described: is the CNS pulled from the body? How can this be done without ripping the nerves? How can the intactness of the nerves be validated? (c) The intact prep sounds simple, but how is VUM GCaMP3 fluorescence measured in an intact larva as shown in Figure 4? Is the "intact" prep the same as the "in vivo" prep? One name should be used throughout for clarity.

3) The semi-intact prep showed Ca++ signals in only 5% of the preps. This makes me worried that the prep is unhealthy, and that the data from the 5% are not physiological.

4) Experiment 1 shows four individuals, but population data for all larvae were not shown. Selecting only a subset of the analyzed larvae is not appropriate; data from all should be shown.

5) Experiment 2 shows low resolution data (left) that is not interpretable. The data highlighted in the right panel is much better but again, only three examples are presented; no population data or statistics are shown.

6) It is also unclear how many larvae were analyzed in Experiment 2. Line 163 says "...~5% of the in vivo preparations (n=27)..." but is that 1/27 or 27/540? In addition, are the different stimulation patterns done sequentially on the same larva, or independently on different larvae?

7) The prep used for Experiment 3 is not mentioned. Not in the text, not in the figure legend.

8) The prep for Experiment 4 appears to be the intact larva, but if so, how were GCaMP signals measured? How were movement artifacts handled?

9) In Experiment 4, the term "crawling frequency" is not defined. Is it frequency that locomotion is initiated?

10) How do the authors standardize harsh and gentle touches?

11) It says "in very rare cases..." on line 246. Please give actual numbers.

12) The figures are cited out of order (1, 3, 2, 4).

13) Many references are missing in the first part of the Introduction, e.g. lines 64. 65, 73, 78, and 83.

Reviewer #1:

The authors have used hydrogen deuterium exchange mass spectrometry and molecular dynamics simulations to study the interaction between the sars-cov-2 spike protein and the ace2 protein. The results suggest that the protein-protein interaction induces extremely long-range allosteric effects on the spike protein, triggering the proteolysis of the spike protein. The results of this work have implications for the development of small molecule inhibitors.

In general, the manuscript is written extremely well. The work is timely, and the results will be of interest to many. The major conclusions of the work are generally supported by the results. However, there are several key - generally minor - details, enumerated below, the authors should provide in order to strengthen the manuscript and validity of the results.

1) The authors should provide more technical details of the molecular dynamics simulations in the supplementary materials. Could the authors provide more details on the equilibration protocol? Was there any analysis done or metric used to assess whether the system was properly equilibrated? How often were snapshots of the trajectory saved for analysis? How many Na+ and Cl- ions were added to achieve 0.15 M of salt concentration? Also, how many water molecules were added? These details are relevant to the non-casual readers.

2) The authors should probably include the techniques used to study the systems in the abstract section of the manuscript.

3) Also, the authors should probably also include the fact that they performed molecular dynamics simulations in the last paragraph of the introduction. This is not apparent until toward the end of the first paragraph of the results and discussion sections.

4) Page 7; line 147: Figure 4 is introduced before Figure 3. The authors should switch the order or modify accordingly.

5) Figure S1: Could the authors elaborate on Figure S1B in the figure legend? Is (i) measuring the binding of ace2 to the S protein? Is (ii) measuring the binding of RBD to the ace2 protein? The distinction between (i) and (ii) is not made in the figure legend.

In summary, the work is interesting and timely, and the manuscript will be of interest to many in the field. The authors should address the aforementioned points.

DOI: 10.1016/j.celrep.2020.108404

Resource: (ZFIN Cat# ZDB-ALT-071127-1,RRID:ZFIN_ZDB-ALT-071127-1)

Curator: @Naa003

SciCrunch record: RRID:ZFIN_ZDB-ALT-071127-1

Curator comments: allele name: li1Tg Danio rerio ZFIN Cat# ZDB-ALT-071127-1

What is this?

DOI: 10.1016/j.celrep.2020.108404

Resource: (ZFIN Cat# ZDB-ALT-070316-1,RRID:ZFIN_ZDB-ALT-070316-1)

Curator: @Naa003

SciCrunch record: RRID:ZFIN_ZDB-ALT-070316-1

Curator comments: allele name: c264Tg Danio rerio ZFIN Cat# ZDB-ALT-070316-1

What is this?

DOI: 10.1016/j.celrep.2020.108404

Resource: (ZFIN Cat# ZDB-ALT-071120-1,RRID:ZFIN_ZDB-ALT-071120-1)

Curator: @Naa003

SciCrunch record: RRID:ZFIN_ZDB-ALT-071120-1

Curator comments: allele name: zf52Tg Danio rerio ZFIN Cat# ZDB-ALT-071120-1

What is this?

DOI: 10.1016/j.celrep.2020.108404

Resource: (ZFIN Cat# ZDB-ALT-120320-1,RRID:ZFIN_ZDB-ALT-120320-1)

Curator: @Naa003

SciCrunch record: RRID:ZFIN_ZDB-ALT-120320-1

Curator comments: allele name: sd11Tg Danio rerio ZFIN Cat# ZDB-ALT-120320-1

What is this?

DOI: 10.1016/j.celrep.2020.108404

Resource: (ZFIN Cat# ZDB-ALT-110307-1,RRID:ZFIN_ZDB-ALT-110307-1)

Curator: @Naa003

SciCrunch record: RRID:ZFIN_ZDB-ALT-110307-1

Curator comments: allele name: pd12Tg Danio rerio ZFIN Cat# ZDB-ALT-110307-1

What is this?

Reviewer #1:

This study investigates asymmetry in functional gradients in human subcortical structures (thalamus, striatum and cerebellum). The authors found that the 1st principal gradient of thalamus and palladium are asymmetric, while that's not the case for caudate, putamen and the cerebellum. In the case of the caudate and cerebellum, their 2nd and 3rd gradients were asymmetric. Further analyses suggest that these differences arise based on connectivity between subcortical structures and the cerebral cortex. In the case of the thalamus and lenticular nuclei, asymmetry is stronger in regions with no direct or driver cerebral cortical afferent connections. In the case of the cerebellum and caudate, asymmetry is stronger in regions linked to cortical regions with higher inter-hemispheric asymmetry. The writing style of this paper is quite different from the usual papers. I actually quite enjoy this conversational/didactic style. Please see my major and minor concerns below.

1) The computation of the laterality index is not clear to me. In the methods section, it's defined as "(left_score - right_score) / (left_score + right_score), where left_score and right_score correspond to the sum of all functional connectivity values for each left and right structure (for example, in the case of thalamus, functional connectivity values in left and right thalamus)". This sounded like they were averaging across all voxels within for example across all thalamic voxels. But in Figure 2, I assume each dot represents a thalamic voxel. So what are the authors averaging over? Indeed, in the results section, the authors said "We then computed a laterality index that quantified the degree of asymmetry in each functional connectivity map from each seed (see methods), and plotted laterality index scores for each voxel in thalami and lenticular nuclei against their corresponding functional gradient value." So for each thalamic voxel, the authors computed the correlation of the voxel's time course to all brain voxels or something else? This was also not clear. After obtaining the correlation map for a thalamic voxel, how do the authors then compress the correlation map of the thalamic voxel into either "left_score" or "right_score". That was not really explained. Furthermore, in order to compute the laterality index, the authors need to define a homologous thalamic voxel on the other hemisphere. How was this done? Did the authors use a symmetric MNI template? Which one? This was also not explained.

2) "Projection of subcortical functional gradients to cerebral cortex" does not quite make sense to me. According to the authors, basically FC maps of voxels are weighted by the absolute gradient values of the voxels. Essentially this means that voxels with extreme gradient values are weighted more. In the case of the thalamus, lenticular nuclei and caudate, voxels with extreme gradient values are indeed voxels with high inter-hemispheric functional asymmetry (IHFaS), so this is ok. However, in the case of the cerebellum, motor regions in lobules I-IV have extreme gradient values as well. As such, these regions would also be weighted more. Thus the resulting projected subcortical gradients might not simply reflect gradient asymmetry. Perhaps it would make more sense to compute a laterality index based on the gradient scores (i.e., left score and right scores are gradient values), and then use the absolute value of the laterality index as the weight rather than the absolute gradient values.

3) The analysis level in Figure 5 is too coarse. By performing a weighted average of thalamic voxels' FC maps (or caudate or lenticular or cerebellum), the authors are ignoring variation in functional connectivity patterns across thalamic (or cerebellar or caudate or lenticular) voxels. A more direct test of the authors' hypothesis should be as follows. According to the authors' hypothesis, cerebellar/caudate voxels that exhibited greater gradient asymmetry should be more strongly correlated with cortical vertices with strong absolute laterality index. Then there should be strong positive correlations between the absolute laterality index of cerebellar/caudate voxels and the absolute laterality index of the cortical locations mostly strongly correlated with the corresponding cerebellar/caudate voxels. On the other hand, there should be weak correlations for thalamic and lenticular nuclei.

4) The authors suggest that no p value is necessary with a 1000-subject dataset. That might be true for certain things like functional connectivity maps, but a number of analyses, such as Figures 2, 4 and 5 do require supportive inferential statistics.

5) "IHFaS is more prominent in first order nuclei (compared to higher-order nuclei)" is not really quantified. The authors should specify in Figure S2, which nuclei are first order nuclei and which are non-first order nuclei. Perhaps the labels on the x-axis could be colored differently for first order and non-first order nuclei.

Reviewer #1:

The manuscript reports the results of a study examining the linear correlation between white matter tracts and AD- related pathology in the grey matter regions connected by the white matter tracts. The integrity of the tracts were measured using FA, MD, AD, RD (corrected for free water) and free water index (FW) and apparent fiber density (AFD). The white matter tracts examined were the cingulum (main and posterior branch), uncinate fasciculus, and fornix. The population studies were older healthy subjects at risk (based on family history) for developing AD. The AD related pathology were tau and amyloid measured using PET. The study was very well done and it addresses key questions in regards to the p-clinical phase of AD.

Questions:

a) It would be very helpful to the reader to understand the distribution of the global ABeta SUVR and temporal tau SUVR - given that studies dichotomise study participants based on high & low deposition, it would help readers better understand the context of the results. The mean and range given in table 1 is not enough.

b) Related to previous question, I would suggest that the same graphs be made for the ROIs at then end of the tracts - again it would help a reader understand the context of the study.

c) I am surprised that APOE e4 allele was not included as a covariate in the statistical model. Why not? Given that APOE increases risk of developing AD, it would seem to be a relevant parameter. Amyloid positivity has been shown to be associated with age, sex and APOE e4 status.

d) The negative results of the posterior cingulate and yet statistically significant results for the uncinate fasciculus are an interesting contrast. Both tracts connect regions with presumably high Beta and high tau deposition. Have there been studies that have compared the amyloid deposition in posterior cingulate cortex and anterior cingulate/anterior frontal regions? It might be supportive of the idea that posterior cingulate is further along the disease progression compared to the anterior frontal regions. Having the data plots as described in (a) and (b) could help in supporting the points made in the discussion.

Reviewer #1:

The manuscript by Carreño-Muñoz seeks to tackle an important problem in behavioral neuroscience, that is classifying behavior at fine resolution during free exploration in rodents. Though the goals of this study are lofty, this platform, in my opinion, isn't a substantive step forward in relation to other tools currently available.

Major concerns:

1) What is presented in this work is a piezoelectric based sensor to detect rodent movements. My main criticism with this work is that the behaviors were coded by hand. If the authors had developed a way to automatically measure spontaneous behaviors of interest, or even train a machine to detect behavioral signatures after some human input, this system would have broader appeal. As is, the experimenter uses standard whole animal tracking with ethovision, then observes what the animal is doing by hand, then quantitation is added to certain movements. This I believe, is not a major advance, as current weight bearing devices already have this capacity.

2) For the breathing and heartbeat studies in figure 2, I am not convinced that this approach is more beneficial than the standard EEG approaches.

3) Figure 3 is poorly developed and the biology is very questionable. "Shaking" after surgery as a read-out of pain is not a measurement currently used or seen in the pain field. Although the authors report that this measurement is reduced with BPN, there are other trivial or pure coincidental explanations for this unusual finding. This reviewer tends to believe that the anesthesia or some other surgical by-product, not with pain as a driver, is contributing to this phenotype. I don't believe the authors have discovered a new post-op pain behavior. If so, substantial data needs to be added to be convincing.

Reviewer #1:

The authors develop a Bayesian approach to modeling macroscopic signals arising from ensembles of individual units described by a Markov process, such as a collection of ion channels. Their approach utilizes a Kalman filter to account for temporal correlations in the bulk signal. For simulated data from a simple ion channel model where ligand binding drives pore opening, they show that their approach enhances parameter identifiability over an existing approach based on fitting average current responses. Furthermore, the approach can include simultaneous measurement of multiple signals (e.g. current and fluorescence) which further increases parameter identifiability. They also show how appropriate choice of priors can help model and parameter identification.

The application of Bayesian approaches to kinetic modeling has recently become popular in the ion channel community. The need for approaches that inform on parameter distributions and their identifiability, as well as allow model selection, is unquestioned. Also, it is ideal to use as much information in the experimental data as possible, including temporal correlations. As such, the authors’ addition is a valuable contribution.

Comments:

I note that my comments are restricted largely to the results rather than the mathematical derivation of the author's approach.

1) I understand that this is somewhat secondary to the paper's intellectual contribution. However, one thing that would be enormously useful is accompanying software usable by others. The supplied code is not well commented, and it is unclear whether it is applicable beyond the specific models examined in the paper. It was supplied as .txt files, but looks like C code. I did not spend the time to get it working, so an accompanying GitHub page or some such with detailed instructions for how to apply this approach for one's own model of interest would make this contribution infinitely better. Even better if there was a GUI, although easily adaptable code is of primary importance.

2) What are the temporal resolutions of the current and fluorescence simulations shown in Fig 1? I assume that they are the same. However, most current recordings are much higher temporal resolution than fluorescence recordings. If you were to reduce the sample rate of the binding fluorescence relative to current simulations to something experimentally reasonable, how would the resulting time averaging of the binding signal impact its enhancement of parameter identifiability?

3) For comparison, it would also be nice to see how addition of the binding signal in the data helps the RE approach. i.e. Is addition of the binding signal more important than choice of RE vs KF, or is optimization method still an important factor in terms of correctly identifying the model's rate constants or in selecting the true model?

4) Fig 7: For PC data, why is RE model BC appear to be better than KF model BC if the KF model does a better job at estimating the parameters and setting non true rates to zero? Doesn't this suggest that RE with cross validation is better than the proposed KF approach? In terms of parameter estimates (i.e. as shown in Fig. 3), how does RE + BC stack up?

Reviewer #1:

In this study Robert et al. describes the properties of long-range projections from the SuM to the CA2 area of the hippocampus. The authors identified direct excitatory and indirect inhibitory drive from SuM inputs on CA2 pyramidal neurons and showed that direct excitatory drive impinges on PV-positive basket cells. The overall effect of the input on CA2 activity was an increased precision of APs. The study also suggests that the input from the CA2 drives inhibition in the CA1 area. The study provides very interesting and new information about the cellular properties of SuM input in the CA2 area. This is an important question given the increasing importance of SuM inputs in social memory encoding. The study is timely, currently we have very limited data about the features and exact cellular profile of this input. The study is using elegant technical approaches to answer the central question of the study. While the study is addressing an important question and provides novel data, the author's central claim about the role of feed-forward inhibition would need to be strengthened by the addition of experiments addressing how E-I balance changes in trains in individual neurons and how this can be linked to changes in the temporal precision of synaptically evoked APs.

Action potentials are evoked with a current step. Since the study is focused on the network effects of feed-forward inhibition, it would be useful to see how the properties of synaptically evoked action potentials change. In the cortex and in the CA1 feed forward inhibition was shown to limit the temporal summation of excitatory inputs which lead to decrease in AP jitter (Gabernet et al., 2005, Pouille and Scanziani 2001). In order to map these dynamics APs should be evoked via synaptic stimulation and not through current injection.

The authors show recordings of monosynaptic EPSCs in pyramidal cells and interneurons. It would be important to know how inhibitory and excitatory PSCs change in a train. Recordings from single cells held at E-GLUT and E-GABA would allow the authors to monitor excitatory and inhibitory events in a train and map how their balance changes. Can the change in E-I balance explain the change in AP jitter?

What are the characteristics of the SuM-driven inhibitory currents? Does the latency and jitter of monosynaptic EPSCs and disynaptic IPSCs differ? If one is monosynaptic and the other is disynaptic one would expect significant differences in both of these parameters.

How do the authors exclude the contribution of feed-back inhibition? Feed-forward and feed-back inhibition both could have an impact on the temporal precision of APs.

Reviewer #1:

Expansins are mysterious cell wall proteins because they lack known hydrolytic activity but are somehow correlated with acid-induced cell wall loosening/extension and cell expansion. Here the authors catalog the tissue expression of several native promoter driven expansin-FP fusions (EXPA1, 10, 14, 15) and find partially overlapping expression patterns and evidence that some expansins are restricted to particular cell wall regions (e.g. tricellular junctions (Figs 1-4). Using Brillouin light scattering (BLS) microscopy they find that, contrary to several previous reports for EXPA1, EXPA1 overexpression induces tissue stiffening that is relatively independent of extracellular pH (Fig 5, 7). They corroborate these data using AFM of different cell walls in a similar tissue (Fig 8). Thus, EXPA1 overexpression results in shorter roots (Fig 9). While BLS seems like an interesting technique for studying cell walls, essential controls are missing making it difficult to interpret these results.

Major Comments:

1) Expansins have traditionally been identified with promoting cell wall extension by loosening the cell wall under acidic conditions. Recent reports have corroborated this: Ramakrishna et al., 2019 showed decreased lateral root initiation in mutants, implying EXPA1 plays a role in loosening, while Pacifici et al 2018 showed decreased cell elongation in expa1 mutants and increased cell elongation in EXPA overexpression lines, but only when grown on low pH (pH 4) media. All of these results are consistent with EXPAs playing a role in cell wall loosening. By contrast, the authors here find that EXPA1 overexpression causes cell wall stiffening and reduced root growth, that low pH (pH 4) media decreases this stiffening (Fig 5). Their discussion of these discrepancies is insufficient. For example, how do their levels of EXPA1 overexpression compare to Pacifici et al., 2018? How can they reconcile the results in these previous papers with their study?

2) Since the authors only really see changes in BLS of their EXPA1 line with over 10,000x overexpression (their inducible EXPA1-mCherry line with "only" >100x expression relative to wild type does not cause significant changes to cell wall "stiffness"), it is unclear how sensitive this technique is to cell wall changes. Controls are required to interpret these BLS experiments. For example, a known mutant or overexpression line with increased cell wall stiffness and another with decreased cell wall stiffness.

3) It will also be important to document whether the authors can replicate the lack of changes to cell wall stiffness in the expa1 mutant using AFM.

4) It would be helpful to see a detailed correlation analysis between the new technique (BLS) and an established cell wall analysis technique (AFM) across multiple data points (i.e. positive and negative controls for cell wall stiffness changes).

5) These AFM values are also presented on a scale that is almost 7x higher than previous data from the authors (e.g. Peaucelle 2014 JoVE). Please discuss.

6) The authors are comparing BLS data from the inner longitudinal cell wall versus AFM data from the outer longitudinal cell wall, which have very different properties. Please discuss.

7) EXPA1 gene overexpression is determined 7 days after Dex induction, but BLS experiments are conducted on plants that have been induced for a much shorter time (e.g. 3h). What is the expression of the EXPA1 gene over this timeframe of induction? Ideally, the authors would also use an EXPA1 antibody to monitor protein levels, since this is what is actually relevant.

8) It is difficult to see from the BLS shift maps provided (e.g. Fig 5A) where in the root the authors are imaging. Given that this is a relatively new technique to the cell wall field, it would be helpful to provide additional images to provide context to readers.

9) "Data not shown" (e.g. trans-zeatin treatments, line 149; EXPA1 protein levels, line 360) must be included as supplemental figures or the claims removed from the manuscript.

Reviewer #1:

In this manuscript, the authors report on two separate experiments designed to understand the relationship between lip-movement induced theta phase and auditory processing. In the first experiment, subjects detected tones embedded in noise while viewing silent videos. The results demonstrate that tone detection performance improved when tones are presented later relative to earlier in a trial. It was also demonstrated that correct detection, for tones that occurred later in the trial, was systematically linked with the phase of the theta oscillatory activity conveyed by the lip movements. In the second experiment EEG was recorded while participants viewed the silent videos and performed an emotion judgement task. Theta phase coupling was demonstrated between auditory and visual areas such that oscillations in the visual cortex preceded those in the auditory cortex.

The authors conclude that these results demonstrate that lip movements directly affect the excitability of the auditory cortex. However, due to the indirect nature of the reported effects, I do not believe this conclusion is justified. I elaborate on this concern below:

1) In experiment 1, the main finding that performance is better later in the trial could arise from many factors including non-specific attentional effects.

2) The analysis reported in the bottom of page 5 (comparing vector lengths for hits vs misses) is critical to the argument but the results are inconclusive (significant interaction, but subsequent comparisons not quite significant. Likely because the experiment is underpowered?).

3) In Experiment 2: the task performed by the listeners might have biased them towards speech imagery leading to the pattern of effects observed. Indeed, the observed involvement of the left hemisphere may be consistent with the involvement of speech imagery. This would render the observed link between visual and auditory cortices as somewhat trivial and not new (such links have been reported in many previous studies as acknowledged by the authors).

4) Most importantly, the authors do not provide any direct evidence that the auditory effects observed in Experiment 2 are related to those observed in experiment 1.

Other comments:

1) For the analyses in Figure 2A, were the number of trials over which the analysis is conducted adjusted for "first tone" vs "second tone"? Since the hit rate is higher for the second tone, there may be a concern that including more trials in the analysis would result in better SNR and hence a more robust effect.

2) In Experiment 2 the analysis is focused on phase effects. Can you report whether there are any power differences in the delta band in the "early" vs "later" time windows?

3) Line 176, the authors write "these results established that entrainment of theta lip activity increased in time". It is not clear to me which aspect of the results supports this statement.

4) Line 405: "any lag between visual and auditory stimuli onsets was later compensated...". I could not find mention of this elsewhere (i.e. how lags were compensated, how large they were). This is critical for interpreting the results and therefore should be described in detail.

5) Line 430-437 why did you choose to quantify the envelope in this way rather than just taking the wide band envelope?

6) Figure S3 is important and should be in the main text.

7) Line 473 "auditory pure tones"

8) The description in lines 478-481 doesn't make sense. It is unclear how loudness reported in line 480 (91dB SPL; incidentally this is very loud) relates to the later reported value of 72dB SPL.

9) Line 485 "embedded"

10) Please clarify whether in your loudness adjustment procedure you were adjusting the loudness of the tone, the noise or the SNR (and thus keeping the overall loudness of the stimulus fixed)

11) Line 537 "preceding"

Reviewer #1:

The manuscript 'Integron activity accelerates the evolution of antibiotic resistance' by Souque et al. investigates the genetic variations created by a class 1 integron during antibiotic exposure. In the study, the authors examine the evolution of an integron encoded on a R388 plasmid; they introduce three antibiotic gene cassettes into the integron and follow its evolution in the presence of one corresponding antibiotic - here gentamicin. They find that antibiotic exposure leads to a rapid re-shuffling of the integron cassette. The re-shuffling favors the aadB gene in the first position downstream of the integron promoter while mainly keeping the (original) last position in the integron. The study represents an interesting example of rapid adaptation to increasing concentrations of an antibiotic that is facilitated by mobile elements. While the experiments are overall interesting and very well designed, the study lacks a certain depth. In the sense that their results might be as well explained by random mutations (genetic diversity). In addition, the two parts of the experiments (integron analysis & chromosomal evolution) need to be connected as it is so far unclear what role the chromosomal mutations have in the integron-facilitated evolution.

Major Comments:

1) The authors don't mention whether they detected re-arrangements in the negative control that was evolved without antibiotics. Furthermore, re-arrangements might appear but at a very low frequency. What is the sequence coverage used in the study? How can the authors ensure they don't miss a low frequency of re-arrangements? It might be possible that random re-arrangements appear at a very low frequency that are only fixed under changing conditions (similar to mutations). The authors should clarify this point.

2) Did the authors measure the Integrase expression levels? This could ensure that there is no expression without stress to the cell.

3) Regarding the mutational analysis: Is there any sign of a cost to the integrase activity? The authors conduct an intensive analysis on chromosomal and plasmid mutations. Nonetheless, it is unclear how these mutations are generally connected to the integrase activity (and not only to the AB treatment).

4) The authors call the integrase activity 'adaptation on demand'. It would be interesting to know how fast a potential reversal would appear in the integron in the populations. Is there any evidence for a deletion of the duplication of the aadB gene after removal of the antibiotic? In the same line of thought, do the authors expect the other AB resistance genes to follow the same path when incubated in the corresponding antibiotic? It would be interesting to know how antibiotic 'type' dependent the experimental result might be.

Reviewer #1:

The importance of host associated microbiomes for health and disease of their hosts cannot be overstated. Fungi tend to feature more prominently in microbiome studies of soil or plants, but microbiome work in animals has mostly focused on bacteria, with fungi having received comparatively less attention. The current study addresses the question whether there is evidence for co-evolution or consistent ecological filtering of fungal communities in the animal gut, similar to what has been reported for bacteria. Such patterns have been termed "phylosymbiosis", even though the ecological interactions that underlie such patterns are largely unknown.

The strength of the study is the wide range of animals investigated, 49 species from eight different classes of vertebrates and invertebrates. However, this wide sampling also is a weakness, as few groups are well sampled. Members of the same species are found to have relatively similar bacterial and fungal microbiota, and fungal microbiota are found to be somewhat correlated with phylogenetic distance. There is also correlation between bacterial and fungal communities, but whether this is driven by independent effects of the host on both groups, or primarily by interactions between the two microbial groups remains unknown. Some of the other observations, such as the tendency of bacterial diversity to be higher than fungal diversity, are more difficult to parse, since it is not clear what the proper yardstick for diversity comparisons is (i.e., whether functional differences between fungal ASVs are comparable to functional differences between bacterial ASVs). This study provides interesting insight regarding the general characteristics of the fungal microbiome and its relationship to the bacterial communities and the host. It does not directly reveal how these communities might affect the host. As the authors themselves state, "The drivers of phylosymbiosis remain unclear".

Reviewer #1:

Major Comments:

The experimental design is inconsistent in at least three ways:

1) The genomes of 14 resistant clones were analyzed by whole exome sequencing (WES), whereas the genomes of the remaining 21 clones were analyzed using whole genome sequencing (WGS).

2) And the sequencing approach even differed among the six lines evolved in three separate drugs: doxorubicin, paclitaxel, and gemcitabine.

3) We feel the authors did not adequately explain how the different sequencing methodologies could affect their results and the inferences drawn from them. For example, one is likely to miss information with respect to copy number variants by only sequencing exomes. The authors highlight this fact in their discussion, but they do not explain by how much they could be off in their assessment.

In some cases the same parental clone was used to find replicate lines subjected to the same selective pressure, and in other cases, the same parental clone was used to find replicate lines subjected to different selective pressures.

Lines were evolved anywhere from seven to thirty weeks, and the length of the evolution experiments does not correlate with the selecting drug (e.g., three replicate lines were evolved in doxorubicin for 9 weeks and three other lines were evolved to this same drug for 12 weeks). Did the authors normalize by generations? Again, the authors do not address this issue in their manuscript.

Reviewer #1:

The manuscript by Kilroy and colleagues centers on demonstrating that inactivity is deleterious for DMD zebrafish and that electrical stimulation is highly beneficial in the model. The authors identify a subpopulation of inactive DMD (sapje) zebrafish that progress faster in dystrophic disease muscle breakdown. They use tricaine to restrict movement and show a faster myofiber breakdown in the severe DMD fish cohorts. The authors then use neuromuscular electrical stimulation (NMES) to improve muscle pathologies and overall DMD zebrafish outcomes. The authors go into extensive details in characterizing the consequences of NMES on normal and DMD zebrafish muscle growth, health, and overall function. Transcriptomic analysis reveals fibrotic and regenerative genes are modulated by NMES.

Overall, this is a strong manuscript on the effects of NMES/electrical stimulation on DMD muscle growth. It does lay several parameters for evaluation of NMES in the zebrafish model. The manuscript is fairly well-written and most of the experiments are presented in a straight-forward manner with clear interpretations. I do have some issues with one or two points that the authors try to extrapolate from their studies. I have significant issues with the description and use of tricaine as an inactivity paradigm in these studies as there are multiple interpretations of these findings. I have a few points about the NMES stimulation protocol and NMJ contribution that should be addressed. This is a good manuscript and can be an important addition to the field if these points are addressed.

1) The inactivity paradigm (e.g. figure 2) using tricaine as a means of inducing inactivity has pluses and minuses. There are issues with comparing it to rodent and human inactivity experiments (which usually involve hindlimb/limb immobilization), as the authors here are using chemical inhibition. Tricaine has systemic effects on multiple tissue types and organ systems including neurological and respiratory systems. I would be careful to call this model an inactivity model as a more appropriate model would be to physically restrain the zebrafish larvae to prevent movement. While technically challenging this experiment can be done and would likely be more reflective of the consequences of physical inactivity in the DMD fish than tricaine anesthesia. Mdx mice have respiratory consequences due to pulmonary muscle weakness, independent of an inactivity (Burns et al., J.Physiol., 2017).

The authors need to rule out if the consequences of tricaine administration is due to inactivity or pulmonary/secondary dystrophic pathology issues (e.g. swim bladder or respiration).

2) The NMES protocol is more extensively established by the authors and has a clearer interpretation. That being said, the main benefit of NMES is to stimulate muscle force/function in the absence of proper innervation by the NMJ, which is also disrupted in DMD. The authors do an excellent job in demonstrating that the NMJ does not change in morphology via immunofluorescence and anatomical observations. Can/have the authors evaluated the functional output of the NMJ in the NMES-treated DMD zebrafish? Were any electrophysiological measurements performed on the NMES treated DMD fish, independent of any therapeutic experimental protocol?

3) Hmox1 overexpression has been pursued as a strategy for DMD in mice by the Zoltan Arany and Joseph Dulak's groups, so the findings in figure 10 are supported. Have the authors evaluated whether or not the entire Hmox1 pathway was affected in the NMES-treated DMD fish?

Reviewer #1:

Obstructive sleep apnea is an important medical problem, with elevated cardiovascular risk as a common association. Intermittent hypoxic episodes are a good predictor of such risk so a connection is indeed plausible. Thus the manuscript starts with a good premise, but what limits my enthusiasm is the large number of loose ends in the story that make it likely that what we are seeing is a small amount of signal, with a large amount of noise, limiting potential mechanistic insights that are translatable.

Major comments:

1) OSA and intermittent hypoxia are clearly different things. Further the hypoxia of OSA is much less in the lung compared to the systemic organs. To illustrate this point, an upper estimate for alveolar CO2 is the venous CO2, or more commonly 10-15 mm Hg elevation over normal i.e. 55 mm Hg. At even 60 mm Hg CO2, local oxygen tension in lungs would be above 80 mm Hg. Systemic desaturation is because of widening A-a gaps and physiological/pathophysiological shunts. While severe OSA with prolonged apnea could indeed be worse, the clinical associations are seen even with milder disease. Thus a-priori it is very unlikely that the model reflects the disease accurately.

2) Given the limitations of the model, it is imperative that at least the pathways elicited by intermittent hypoxia be clearly defines so that even if we do not gain fully understanding of OSA, we may understand the consequence of intermittent hypoxia that may be relevant in another context. Here too the manuscript is lacking. The genomic analysis is interesting and indeed data rich. However, more attention could have been paid by exploring a hypothesis, ensuring multiple markers for target cell populations, and building a mechanistic model. In current form, the work is hypothesis generating, based on limited markers and analysis, and is extrapolated widely to other pulmonary disease without a solid rationale.

Reviewer #1:

In the manuscript entitled “ASIC1a is required for neuronal activation via low-intensity ultrasound stimulation in mouse brain", Lim et al. investigate the mechanism underlying the activation of brain neurons by transcranial low-intensity ultrasound stimulation. The authors propose that ultrasound stimuli-induced movements of the extracellular matrix and the cytoskeleton cause mechanical activation of ASIC1a in cortical neurons, which leads to Ca2+ influx and subsequent expression of pERK, which the authors used as a surrogate marker for neuronal activation.

While I agree that the finding that ultrasound activates neurons via activation of a mechanosensitive ion channel is per se very interesting, I have to say that in my opinion most of the conclusions and claims are not supported by the actual data.

1) The entire study is purely correlative. Thus, the authors made two independent experiments; on the one hand they show that in-vivo transcranial ultrasound stimulation induces pERK in various brain regions and on the other hand they shown that ultrasound-evoked Ca2+ influx in cultures of cortical neurons is probably mediated by ASIC1a. From this data they conclude that pERK activation is also mediated by ASIC1a activation. This is, however, pure speculation. The authors must provide additional evidence to support their claim. In my opinion the sole use of PcTx1 is not sufficient to prove that the Ca2+ signals are mediated by ASIC1a. Hence, firstly the authors should demonstrate that ASIC1a is indeed activated by ultrasound. This is a very simple experiment. All they would have to do is express ASIC1a in a cell line (e.g. HEK293, CHO, etc) and show that this expression renders the cells sensitive to ultrasound. Second, I would appreciate it if the authors would show that cortical neurons, especially those that show pERK activation, express ASIC1a in the first place. This would also be quite simple - just co-stain the brain sections with an anti-ASIC1a antibody. Third, if the authors want to keep up their claim (see title) that ASIC1a is required for ultrasound activation of brain neurons they should examine ultrasound-induced pERK activation in ASIC1a-knockout mice.

2) It is difficult to evaluate the Ca2+ imaging experiments, because the method - especially the ultrasound stimulation - is not very well described. Hence it is unclear to me how close to the cell the ultrasound stimulator was placed. Moreover, the N-numbers of the Ca2+ imaging experiments are rather small (by the way, it would make reading much easier if the N-numbers were indicated in the figure). Most importantly, it is unclear if the inhibitors (Gadolinium, GsMTx4 etc - Figure 2B-H) were applied to the control cells from the same panel or to different cells. In this context it would be important to know how many control cells actually responded to the ultrasound stimulation. Considering the low N-number, I was wondering if the authors may have had a hard time finding cells that responded and that this is the reason why the N-numbers are so small? I suggest examining many more control neurons and provide information about the proportion of cells that respond. If only for the controls as well as for the cells treated the various channel inhibitors.

Reviewer #1:

The study by Lenz et al. explores the acute action of retinoic acid (RA) in adult human cortical neurons. The main findings are:

1) Consistent with previous findings in mouse neurons, the authors reported enhanced excitatory synaptic transmission in RA-treated cortical layer 2/3 neurons.

2) Also consistent with previous findings, this enhancement is independent of gene transcription, but requires protein synthesis.

3) RA's effect on EPSC requires expression of an actin-modulating protein called synaptopodin. In the Synaptopodin deficient mouse mPFC neurons, RA's effect on EPSC is eliminated. Moreover, in synaptopodin deficient hippocampal dentate gyrus neurons, enhancement of LTP by RA is also reversed.

Overall, this study demonstrates RA-induced synaptic plasticity in acute human cortical neurons, thus expanding the previous findings from mouse neurons and immature human neurons induced from iPS cells to adult human cortical neurons.

Specific Comments:

1) Figure 3 shows that in synaptopodin deficient mouse neurons, RA no longer increases sEPSC amplitudes. The rescue experiments are very nice. However, in both WT neurons (stated in main text, not in figure) and rescue neurons (Fig. 3B), the baseline sEPSC amplitudes are significantly smaller than those of the KO neurons. Can the authors speculate why deletion of synaptopodin may lead to enhanced basal excitatory synaptic transmission?

2) The LTP experiments are a bit problematic. First of all, it was done in mouse hippocampal DG neurons, not cortical neurons. The effect of RA may be different in different neuronal types, as has been shown in previous mouse studies. It will be nice to examine whether RA changes basal synaptic transmission in these neurons in acute slices. Without knowing the effect on basal transmission, it is hard to interpret the LTP results. Second, why did WT DG show no LTP? Third, previous work by Arendt et al. (2015) showed that RA enhances hippocampal CA1 neuron basal EPSCs, and occludes further LTP. The observation here in the DG with RA treatment points the opposite direction. Can the authors offer some explanation (i.e. RA alters LTP threshold through some kind of priming)? Again, knowing the effect of RA on basal transmission specifically in the DG neurons would be informative toward understanding the effect on LTP.

3) The pharmacological treatments (ActD, anisomycin etc.) in this study are in general very long (6 hr) compared to conventional methods (less than 2 hr). To control for potential toxicity associated with prolonged treatment, vehicle control should be added in both Fig 5 and Fig 6.

Reviewer #1:

The manuscript by Sachella examines the role of the lateral habenula (LHb) in learning to associate a context and a cue with an aversive event. The methods use pharmacological and optogenetic modulation of LHb function. The data show that inactivation of the LHb impairs contextual fear conditioning (CFC) as well as cued fear conditioning (when testing occurs in a novel context). The disruption in context but not cued FC is also obtained when testing occurs in the context of conditioning (A) 7 days after training but the deficit in both is evident when testing occurs 21 days after training. Overall, similar results are obtained with cue-specific optogenetic inhibition using ArchT and more sustained optogenetic excitation across the entire training session with oChiEF. Finally, exposure to the context and tone 24hrs prior to the test rescued cued but not contextual fear.

The present paper provides an interesting set of studies looking at the role of the LHb in fear conditioning. There are many strengths to the paper. The variation in testing and training conditions is great. It allows to examine memory to the conditioning context when it is the only stimulus the animals learn about, as well as to examine the memory for the cue when tested in a novel context in the absence of influence from the conditioning context (i.e., cue test in context B), as well as in the context of conditioning (i.e., context A). This allows the authors to rule out overshadowing as an interpretation. For example, the LHb-inactivated animals do not present an augmented case of overshadowing in the cued and contextual fear training conditions. If that was the case in the CFC alone experiment, LHb inactivation would not have disrupted learning, but it did. Further, if the LHb had a specific role in summation of context and cued fear (this could account for the data in Fig 3 as ceiling levels could mask performance differences in 3B), then it would not modulate contextual and cued FC when examined independently (Fig 1 and 2). The authors allude to this briefly in line 226. Other strengths of the manuscript include excellent anatomical controls.

Despite the strengths, there are a number of weaknesses that need to be addressed. The major one, I believe, lies in the necessity for additional data to support the conclusions. Although there are a lot of data presented in the manuscript, together they are not a convincing set that speaks to one interpretation. Specifically, the idea that LHb inactivation/stimulation leads to weakening of the memory strength is interesting, but it also requires additional investigation to show that under conditions when the CFC is strengthened, LHb inactivation has a less devastating effect. Further, the authors concede on line 252-253 that more experiments are needed to determine whether LHb inactivation disrupts the associative or representation components of CFC. I agree but feel this should have been done in the present paper instead of the reconsolidation studies which are also incomplete. The authors argue 'under inactivation of the LHb, a cued FC memory is formed whose retrieval depends on the context in which the cue is presented'. However, the disruption of contextual fear makes this interpretation difficult to accept. If the correct context is needed for cued fear to be expressed then this suggests either a possible generalization decrement effect that is ameliorated by being placed in the same context or a context-gating effect. Both require some knowledge of the context where the cued fear learning occurred. Yet, this is difficult to reconcile with the consistent disruption in context fear.

The reconsolidation experiments, although interesting, lack clarity and the vehicle controls. A systematic investigation of exposure to the conditioned context or the conditioned cue (in context B) on fear to the conditioned context, the cue and both would help dissociate how retrieval-based reconsolidation acts in the current preparation. This may warrant an independent investigation/publication.

Some other arguments that I didn't find convincing: The equivalent reduction in exploration in the OF for the vehicle and muscimol animals is argued to suggest that similar contextual representation are formed between the groups and therefore the CFC differences are unlikely to be due to deficits in context encoding. The OF data are insufficient to argue this. Many aspects can modulate activity in the OF from the traditional anxiety argument (here similar reduction in anxiety) to a sense of familiarity. There is no evidence for similar contextual encoding.

Some additional comments:

The way the 24hr and 7d data are presented is a little odd. While the authors justify this, it seems strange from the reader's perspective to see the 7d test data before the 24hr test data. In addition, the 24hr tests data are referred to as long term memory, which can be perceived as odd relative to the longer 7d test. This section just needs to be revised for clarity in the presentation.

Does the difference in cued fear at the 24hr interval persist if conditioning differences are used as a covariate in the analysis and if a difference score is calculated from the baseline difference?

Reviewer #1:

The paper tackles an important aspect of neuroanatomical and language research concerning the lateralization differences related to functional lateralization of language. No clear cut results are currently available nowadays and methodological limitations of previous approaches are here addressed with a new type of analysis. Despite this new angle in the tractography analysis is of interest, the differences in the tasks that are used to address language lateralization are also as important. This may also explain possible differences in previous studies and also with the current one. This aspect seems to be missed in this work.

Although the Letter fluency task implies the use of language, this task is commonly considered in neuropsychological assessments as an executive function task. A more appropriate task would have been a Semantic Fluency task or as in previous work (Vernooij et al 2007) a verb generation task. There is a close relationship between executive function and many aspects of language production, there is not doubt about this. But this does not mean they are the same. Actually the Forceps minor has been found to be associated with individual differences in executive functions in language function (Mamiya et al 2018; Farah et al 2020). This is a limitation of the study and should be acknowledged since the results may differ with a more purely linguistic task, limiting the scope of the study and its conclusions in terms of language lateralization. I do believe the data are worth publishing and the methodological approach is novel but the reader should be clearly aware of the limits in terms of the conclusions the authors can draw from the selection of the sample that may correspond to lateralization of executive function for language more than language lateralization per se.

Reviewer #1:

The work by Pipitone et al. is a very carefully performed and technically sophisticated elucidation of the establishment of the thylakoid membrane system in Arabidopsis chloroplasts upon first illumination of cotyledons. Its charm is the three-dimensional resolution during a time course that allows it to follow the rapid changes occuring during the short time window in which the greening occurs. In addition, the authors included proteomics and lipidomics approaches complementing the morphological observations by sound molecular data. All together the study provides a very detailed catalogue of the processes that trigger chloroplast biogenesis that is highly useful for the community as it provides important numbers of size and development.

Improvements:

Actually the work has been performed very carefully and there is not much to improve.

The introduction could contain more references (e.g. lines 77, 83, 90, 93, 98,, 131, 132)

SBF-SEM should be spelled out at first mentioning (line 146) and maybe a bit more background about the technology would be helpful for the reader to understand it.

Line 244: The occurrence of starch granules is of course caused by the continuous illumination. It however may also have an impact on the final size of the plastid. It would be interesting to know whether chloroplasts at the end of a night phase are smaller than at the end of a light phase. This is not mandatory for the current manuscript but an interesting question to follow in future and maybe to be discussed.

Line 251: The surface area.... please define what is meant since membranes have two sides.

Lines 256-261: There is another study done in cell culture that has a similar design (Dubreuil et al ), are the two studies compatible with each other in their conclusion and if not, what are the differences?

Lines 549-551: This sentence is not perfectly clear to me. Maybe the authors can explain this a bit more in detail using examples.

Lines 564-573: I think it is worth noting that the interactions between PSII complexes located in neighbouring thylakoid membranes trigger the stacking of the grana. It is therefore tempting to speculate that stroma lamellae are established first and that these membranes are then stacked after PSII complexes are inserted into the membrane because they provide the adhesion points between them.

Reviewer #1:

The study by Lyengar et al describes age- and temperature-dependent changes in the neurophysiology of the giant fiber (GF) system in adult wild type and superoxide dismutase 1 mutant flies (SOD[1]). While the main GF circuit and downstream circuits exhibit little change when flies are reared at 25C, GF inputs and other circuits driving motoneuron activities show age-dependent alterations consistent with earlier studies. Rearing flies at 29C temperatures had no additional effects except that age-dependent progression of defects were accelerated, as it was expected from previous studies. In SOD[1] mutants, which are short lived, changes in the neurophysiology of the GF system were different from those induced by high temperature.

Overall this technically challenging, and well executed study provides a nice description of the effects of aging, high activity (induced by higher temperature), and loss of SOD function on the neurophysiology of the GF system. However, most of the described effects have been observed in other systems and are thus not entirely novel. Moreover, the study does not provide any insight into the mechanisms underlying the age-dependent alterations of the examined neurons. Thus, the overall significance of the described findings is limited.

Reviewer #1:

This manuscript compares the effects of a novel versus a classical augmented acoustic environment protocole on partial improvement of congenital hearing loss. The new protocol is based on the idea that temporal structure, and in particular auditory gaps in the augmented environment should improve perception of temporal features in sounds, in particular of auditory gaps.

Technically sound, the study describes how the encoding of gap in the auditory midbrain (inferior colliculus, IC) of a mouse hearing loss model is affected by the novel temporally enriched paradigm with respect to control mice and to the classical paradigm. The study clearly confirms that augmented acoustic environments improve spectral tuning, and detection of sound features with respect to control animals in IC. IC neurons also appear to show a more robust increase of sensitivity to amplitude changes (onsets and offsets) when the animals have gone through the temporal augmented sound environment, both in the presence and in the absence of background noise, as compared to the classical paradigm, at least if one considers the magnitude of the effects with respect to control. However, only few measures show a significant difference when directly testing between the classical and the temporally enriched paradigm. Thus, there is an overall impact of the temporal paradigm which is worth emphasizing as a small but likely useful increment of the auditory enrichment approach for improving hearing loss. This is a definitely interesting, even if somewhat expected result which could drive further studies on clinical practice. It seems however too specialized for broader readership. A few things in the presentation of the results could be improved, and behavioral data could eventually reinforce the message although it is not mandatory to make these results interesting :

1) A figure of the auditory enrichment setup would be nice, to better understand how this works. Are mice constantly submitted to the sounds? Are control mice in a more silent environment than normally housed mice?

2) The lack of behavioral data opens the question whether IC changes have actually an impact on perception. Although it is likely, it would be interesting to measure the magnitude of this impact.

3) What makes the study interesting is the tendential bias in favor of the temporal paradigm with respect to the classical one. This is however rarely significant in one to one comparisons for each sensitivity measure. To reinforce their point the authors could consider a multivariate statistical analysis (e.g. two way ANOVA) to show that over all their measures there is a significant improvement with temporal against classical.

Reviewer #1:

This report makes a logical connection between depressive-like behaviors induced in mice following LPS-injection to mimic bacterial infection and the down regulation of phospholipid transporting enzyme, ATP8A2, in the prefrontal cortex. The intermediary is IFN-gamma. The work is quite convincing that LPS down regulates ATP8A2 by upregulating IFN-gamma and that this has some limited effects on behavior. However, the impact of the findings is limited by several factors.

1) The use of FST and TST as measures of depression is increasingly falling out of favor as there is no face validity to humans. It is understood that these tests have been long in use and were in the past considered the best measures of "depressive-like" behaviors in mice but the field has moved on to much more relevant constructs such as social defeat, anhedonia etc. As it stands the behavioral analysis here is limited and the effects are modest at best.

2) The use of LPS as a model to induce depression also has limitations. The injection paradigm used is likely to have caused massive inflammation, as evidenced by the increase in cytokines, but what this is modeling is unclear and how the impact would be specific to depression later in life is equally unclear. Indeed, the references the authors cite for the LPS regime they use offer completely different mechanisms and impacts of the inflammation. This is not to say the current findings aren't important, they are, but rather this pathway may be one among many that is invoked following massive inflammation during early development which then has many non-specific effects.

3) There is no functional connection between down regulation of ATP8A2 developmentally and adult neural activity. Clearly a membrane phospholipid transporting enzyme is important, but exactly how it is important here, meaning what enduring impacts there are on neuronal function, is unknown.

4) The experiments were designed to test the relationship between IFN-gamma and ATP8A2 but then conclude that the behavioral effects are mediated by this connection. There could be many other effects of IFN-gamma that are not considered here but would be nonetheless blocked by the neutralizing antibody approach used. Thus the main conclusions of the manuscript are not supported in terms of the role of ATP8A2 in LPS-induced depression.

Reviewer #1:

Mackay et al. present a study on the phenotype of neurons from YAC128 mice, an HD model expressing mHTT with 128 CAG repeats. They show (i) that cultured cortical YAC128 neurons exhibit increased mEPSC rates transiently during development in vitro (i.e. between DIV14-18 but not at DIV7 or DIV21), (ii) that calcium release from ER by low-dose ryanodine increases mEPSC rates only in WT but not in YAC128 cells, and (iii) that blocking SERCA to deplete ER calcium stores reduces mEPSC rates in YAC128 neurons as compared to WT controls. These data are interpreted to indicate that a presynaptic ER calcium leak increases mEPSC rates in YAC128 neurons. Using rSyph-GCaMP imaging, the authors then show (i) an increase in longer-lasting AP-independent calcium signals in synaptic boutons of YAC128 neurons as compared to WT, (ii) less profound increases in calcium signals upon ionomycin-mediated equilibration to 2 mM extracellular calcium, (iii) less profound increases in calcium signals upon caffeine treatment in YAC128 boutons, and (iv) less AP-related calcium events in YAC128 boutons. A final dataset shows that evoked synaptic transmission in YAC128 striatum as assessed by iGluSnFR imaging is inhibited by ryanodine in WT but not in YAC128 mice. The authors conclude that the overexpression of mHTT with 128 CAG repeats in the YAC128 mutant causes aberrant calcium handling (i.e. calcium leak/release from the ER), which leads to increased cytosolic calcium concentrations, increased AP-independent release events, but reduced AP-evoked glutamate release.

Comments:

1) I think the authors show convincingly that (presynaptic) calcium handling is perturbed in YAC128 cortical presynaptic boutons. What is conceptually unclear to me at the outset is whether this specific phenomenon is related to HD pathology. The phenomenon is transient during the development of cortical neurons in culture and gone at DIV21. In contrast, the first subtle behavioural defects of YAC128 mice arise at about 3 months of age, overt behavioural defects at 6 months of age, and striatal and cortical degeneration still later.

2) The issue discussed above (1) could have been addressed in part with the slice experiments, which were conducted with tissue from 2-3 months old mice, but the corresponding data are too cursory at this point. They indicate a small defect in evoked glutamate release in the YAC128 model, but it is unclear whether mEPSC rates are altered. It seems important to test this as the increased mEPSC rates are proposed to be at the basis of the phenotype described in the present study. Indeed, the authors ultimately conclude that the YAC128 mutation causes increased mEPSC rates at the expense of evoked glutamate release. This is generally unlikely to be true as the mEPSC rates in question are very likely overcompensated by the vesicle priming rate.

3) The phenomenon of altered calcium handling in YAC128 neurons is shown convincingly. However, this finding is not unexpected given that previous studies indicated such increased calcium release from endoplasmic reticulum in HD models in other subcellular compartments, and it remains unclear how this defect is caused by the mutant HTT.

4) As already outlined above (2) it remains unexplained how the calcium handling defects increase mEPSC rates but decrease evoked transmission. The corresponding part of the discussion reflects this uncertainty. This is aggravated by the fact that several of the drugs used have complex dose-dependent effects that cannot easily be reduced to specific effects on calcium handling by the ER. For instance, it is unclear whether caffeine effects on adenosine receptors or PDEs have to be taken into consideration. In general, the sole reliance on partly 'multispecific' pharmacological tools is a bit worrisome.

5) There are several other aspects of the paper that are not immediately plausible. For instance, I have difficulties to understand why a calcium transient minutes before ionomycin treatment would affect the calcium signal triggered by ionomycin in the presence of 2 mM extracellular calcium (Figure 4); after all, the example trace shows that the calcium levels return to baseline within seconds. And more generally, in this context: Can differences in calcium buffers and the like be excluded? A direct assessment of absolute cytosolic calcium concentrations would be the ultimate solution.

Overall, the present paper describes a phenomenon in presynaptic boutons of an HD model, key aspects of which (e.g. increased ER calcium handling defects) have been described in other subcellular compartments of HD models. The connection of this phenomenon to HD is unclear as the developmental timelines of the appearance and disappearance of the cellular phenotype and the disease progression do not match. The opposite phenotypes caused at the level of presynaptic boutons on AP-independent and AP-dependent release remain disconnected. The mechanism by which mutant HTT causes these defects remains unexplored. The pharmacological tools used do not always allow unequivocal conclusions regarding the targets affected. I think some more work is needed to generate a clear picture of what exactly happens presynaptically in YAC128 neurons, and to show how this might relate to HD.

Reviewer #1:

Deng et al. studied the mechanisms underlying the wide propofol effect-site concentration range associated with loss of responsiveness. Data was acquired from two centers (MRI, Canada; Auditory, Ireland). This is a well conducted study. The results could also explain why older patients (with presumably smaller gray matter volume) are more sensitive to propofol. My major concerns relate to precision in language.

1) The authors studied mechanisms underlying why patients lose consciousness at a wide range of propofol effect-site concentration. This behavioral phenomenon is known and well described (Iwakiri H, Nishihara N, Nagata O, Matsukawa T, Ozaki M, Sessler DI. Individual effect-site concentrations of propofol are similar at loss of consciousness and at awakening. Anesth Analg. 2005;100:107-10). I would suggest that the. authors position their paper as such. They did not study general anesthesia per se, and the allusions to awareness under anesthesia may not be relevant.

2) Per comment 1 above. Please reword the intro and discussion section i.e., " Anaesthesia has been used for over 150 years to reversibly abolish consciousness in clinical medicine, but its effect can vary substantially between individuals." What type of anesthesia are you referring to? Anesthetic vapors? Please provide a reference for this statement or make it propofol specific. Awareness under general anesthesia is related to numerous factors, many of which are iatrogenic as detailed in the NAP 5 study "The incidence of awareness rose from 1 out of 135,000 general anaesthetics to 1 out of 8,200 general anaesthetics when neuromuscular blockers were used" (https://pubmed.ncbi.nlm.nih.gov/25204697/). Further, it is unclear when dreaming occurs (during induction which is reasonable to expect/during emergence which is also reasonable to expect versus during the anesthesia). My suggestion is to qualify your statements by stating that this should be further studied in the context of possible genetic predisposition to awareness (Increased risk of intraoperative awareness in patients with a history of awareness. Anesthesiology 2013;119:1275-83).

3) The term "moderate anaesthesia" is confusing to me, and would be to most clinicians. Please cite the description of what comprises moderate anesthesia. My interpretation is that the study was about sedation. Did you mean moderate sedation? (https://www.asahq.org/standards-and-guidelines/continuum-of-depth-of-sedation-definition-of-general-anesthesia-and-levels-of-sedationanalgesia).

4) "the antagonistic relationship between the DMN and the DAN/ECN #and# was reduced during moderate anaesthesia, with a stronger and significant result in the narrative condition relative to the resting state." Anticorrelation?

5) The suggestion that fMRI can be used to improve the accuracy of awareness monitoring is, in my opinion, not necessary and a stretch.

Reviewer #1:

This article proposes that the assembly of the Sars-CoV-2 capsid is mediated by liquid-liquid phase separation of the N protein and RNA. The strength of the manuscript is a series of in vitro experiments showing that N protein can undergo liquid-liquid phase separation (LLPS) in a manner enhanced by RNA. The authors also identify nilotinib as a compound that alters the morphology of assemblies consisting of RNA and the N protein. The primary weakness of the manuscript is that there is little data connecting the in vitro observations to intracellular events, or viral assembly. Taken together, I find the experiments interesting but, as detailed below, premature.

Major comments:

1) A key issue with any in vitro assembly process such as LLPS is a demonstration that same process occurs in the cell. This is an issue since many molecules can undergo LLPS in vitro in a manner unrelated to their biological function. In this work, the authors show that the N protein can undergo LLPS in vitro in a manner a) stimulated by RNA, b) enhanced by the R2 domain, and c) changed in morphology by nilotinib.

Their argument that this LLPS is relevant to the viral life cycle rests on: a) the observation that over-expressed N protein forms foci in the cytosol, and b) the number of these foci (but not necessarily their morphology as seen in vitro) is somewhat reduced by nilotinib. In my opinion, this is not a very convincing argument for two main reasons.

First, it is unclear why the N protein is forming foci in cells. Specifically:

a) Is it being recruited to P-bodies, or some other existing subcellular assembly? (Which could be examined by staining with other markers).

b) Is it forming a new assembly with RNA as they have proposed? (Which could be addressed by staining for either specific or generic RNAs, or purifying these assemblies and determining if they contain RNA)

Second, it is unclear that the foci seen in cells are related to the LLPS they observe in vitro or relevant to the viral life cycle. Specifically:

c) Is the assembly related to the LLPS they have observed in vitro beyond a poorly understood alteration with nilotinib ? (Which could be addressed by examining if the deletions they observe affect LLPS in vitro also affect the formation of N protein foci in cells).

d) Is the nature of this assembly relevant to the viral life cycle? (Given the difficulty of working with COVID, this is hard. My suggestion here is at a minimum to discuss the issue, and ideally do an experiment with a related coronavirus to test their hypothesis). Frankly, the idea that coronavirus would trigger a LLPS of multiple viral RNAs would seem to be inhibitory to efficient packaging of individual virions. A discussion of how the virus would benefit from such a mechanism, as opposed to a cooperative coating of a viral genome initiated at a high affinity N protein binding site would be important to put the work in context.

2) The manuscript would be improved by examining the presence of RNA in each LLPS, and the ability of RNA to undergo self-assembly under the conditions examined in the absence of the N protein. As it stands, in some cases, the authors could be studying RNA based self-assembly, that then recruits the N protein to the RNA LLPS by RNA binding (see Van Treeck et al., 2018, PNAS for specific example of this phenomenon). This may be particularly likely for some of the longer viral RNAs that can form more stable base-pairs and thereby promote more "tangled" assemblies (e.g. Tauber et al., 2020, Cell).

3) I found the CLMS to not fit well in this manuscript for two reasons:

a) As I understood the methods, the CLMS experiment is looking at cross linking in high and low salt, with some LLPS occurring under low salt. However, since the cross linking was not limited to the dense phase of the low salt condition, a significant fraction (perhaps majority?) of the N proteins will not be in the dense phase. Because of this, the cross linking is essentially mapping interactions that change between high and low salt. If the authors really want to do this experiment, they should separate the phases and examine the crosslinks forming in the dense and dilute phases under the same salt conditions.

b) A second issue with this cross-linking experiment is that the regions that dominate the changes in cross linking are not ones that appear to be important in driving LLPS in vitro based on their deletion analysis. If the authors want to include this data, it should be related to the deletion experiments and connected to the work in a manner to make it meaningful.

4) The work would be improved by comparing how alterations that impact LLPS affect specific biochemical interactions of the relevant molecules. In these experiments, the authors are examining assemblies that form through N-N, N-RNA, RNA-RNA interactions. In each case, biochemical assays could be used to examine which of these interactions are altered by deletions or compounds. By understanding the underlying alterations in molecular interactions, a greater understanding of the mechanism of the observed LLPS, and its relevance to the viral life cycle could be revealed.

Reviewer #1:

This study is based on previous work that exposure to valproic acid (VPA), which is used to model autism spectrum disorders, produces excess local synaptic connectivity, increased seizure susceptibility, abnormal social behavior, and increased MMP-9 mRNA expression in Xenopus tadpoles. VPA is an interesting compound that is also used as an antimanic and mood stabilizing agent in the treatment of bipolar disorder, although the therapeutic targets of VPA for its treatment of mania or as a model of neurodevelopmental disorders have remained elusive. The authors validate that VPA exposed tadpoles have increased MMP9 mRNA expression and then test whether the increased levels of MMP9 mediate the effects of VPA in the tadpole model. The authors report that overexpression of MMP-9 increases spontaneous synaptic activity and network connectivity, whereas pharmacological and genetic inhibition with antisense oligos rescues the VPA induced effects, and then tie the findings to experience dependent synaptic reorganization.

1) What is the exact nature of "increased connectivity"? Is there an increase in synapse numbers or solely an increase in dendritic complexity coupled with a functional plasticity? The authors should document properties of mEPSCs and mIPSCs recording in TTX to isolate synaptic properties. Coupling this "mini" analysis to quantification of synapse numbers will address whether the changes are solely due to structural plasticity or also due to a functional potentiation of transmission. These experiments should at least be conducted in MMP-9 overexpression, VPA treatment and VPA treatment+MMP-9 loss-of-function cases to validate the basic premise that there is an increased connectivity.

2) It is unclear why the authors focused on MMP-9 compared to other genes dysregulated by VPA. This point should be further discussed.

3) How does VPA alter MMP-9 levels? Is this through an HDAC dependent mechanism? Granted VPA has been proposed to work through a variety of mechanisms including HDAC inhibition.

4) Does SB-3CT rescue the expression levels of MMP-9?

5) How is increased MMP-9 produces the synaptic and behavioral effects? What is the downstream target (specific receptor?) that would produce the broad changes in synaptic and behavioral phenotypes? Or is this a rather non-specific effect of extracellular matrix? Based on years of data on MMP-9 function its impact on "structural plasticity" in general terms is not surprising but further mechanistic details and specific targets would help move this field forward.

Reviewer #1:

This manuscript has novelty in it’s approach. The authors use an animal model to abolish the circadian rhythm in mice to study the impact on susceptibility to challenge with LPS. The experimental approach they use involves both wild-type mice subject to sudden stop of the light-dark (LD) cycle and mice knocked-out for the Clock system (KO). I have some points of concern:

• The investigators show that mice shift from LD to DD become more lethal to LPS. If this is due to abolishment of the circadian rhythm, similar lethality should appear with the challenge of the KO mice. The opposite was found. Please explain.

• LPS is acting through TLR4 binding. Can the author provide evidence that TLR4 expression is down-regulated in transition from LD to DD? Does the same apply for the expression of SOCS3?

• TLR4 is a receptor for alarmins with IL-1alpha being one of them. Can the authors comment, based on their IL-1alpha findings, if this may be part of the mechanism?

Reviewer #1:

This manuscript uses simultaneous fMRI-EEG to understand the haemodynamic correlates of electrophysiological markers of brain network dynamics. The approach is both interesting and innovative. Many different analyses are conducted, but the manuscript is in general quite hard to follow. There are grammatical errors throughout, sentences/paragraphs are long and dense, and they often use vague/imprecise language or rely on (often) undefined jargon. For example, sentences such as the following example are very difficult to decipher and are found throughout the manuscript: "if replicated, an association between high positive BOLD responsiveness and a DAN electrophysiological state, characterized by low amplitude (i.e., desynchronized) activity deviating from energetically optimal spontaneous patterns, would be consistent with prior evidence that the DMN and DAN represent alternate regimes of intrinsic brain function". As a result, the reader has to work very hard to follow what has been done and to understand the key messages of the paper.

Much is made of a potential power-law scaling of lifetime/interval times as being indicative of critical dynamics. A power-law distribution does not guarantee criticality, and could arise through other properties. Moreover, to accurately determine whether the proposed power-law is indicative of a scale-free system, the empirical property must be assessed over several orders of magnitude. It appears that only the 25-250 ms range was considered here.

The KS statistic is used to quantify the distance between the empirical and power-law distributions, which is then used as a marker of the degree of criticality. It is unclear that this metric is appropriate, given that transitions in and out of criticality can be highly non-linear. Moreover, the physiological significance of having some networks in a critical state while others are not is unclear. Each network is part of a broader system (i.e., the brain). How should one interpret apparent gradations of criticality in different parts of the system?

The sample size is small. I appreciate the complexity of the experimental paradigm, but the correlations do not appear to be robust. The scatterplots mask this to some extent by overlaying results from different brain regions, but close inspection suggests that the correlations in Fig 6 are driven by 2-3 observations with negative BOLD responses, the correlations in Fig 7A-B are driven by two subjects with positive WMSA volume, and Fig 7B is driven by 3 or so subjects with negative power-law fit values (indeed, x~0 in this plot is associated with a wide range of recall scores). Some correction for multiple comparisons is also required given the number of tests performed.

Figure 1 - panel labels would make it much easier to understand what is shown in this figure relative to the caption.

Figure 2- the aDMN does not look like the DMN at all. It is just the frontal lobe. Similarly, the putative DAN is not the DAN, but the lateral and medial parietal cortex, and cuneus.

P6, Line 11 - please define "simulation testing"

Reviewer #1:

Using two behavioral experiments, the authors partially replicate known effects that rotated faces decrease the benefit of visual speech on auditory speech processing.

As reported by the authors, Experiment 1 suffers from a design flaw considering that a temporal drift occurred in the course of the experiment. This clearly invalidates the reliability of the results and this experiment should be properly calibrated and redone. There is otherwise well-known literature on the topic.

Experiment 2 should be discussed in the context of divided attention tasks previously reported by researchers so as to better emphasize how and whether this is a novel observation.

Additionally:

-The question being addressed is narrowly and ill-construed: numerous authoritative statements in the introduction should reference existing work. For instance, seminal models of Bayesian perception (audiovisual speech processing especially) should be attributed to Dominic Massaro. Such statements as "studies fail to distinguish between binding and late integration" are surprising considering that the fields of multisensory integration and audiovisual speech processing have essentially and traditionally consisted in discussing these specific issues. To name a few researchers in the audiovisual speech domain: the work of Ruth Campbell, Ken Grant, and Jean-Luc Schwartz have largely contributed to refine debates on the implication of attentional resources to audiovisual speech processing using behavioral, neuropsychology, and neuroimaging methods. In light of the additional statements of the kind "The importance of temporal coherence for binding has not previously been established for speech", I would highly recommend the authors to do a thorough literature search of their topic (below some possible references as a start).

-What the authors understand to be "linguistic cues" should be better defined. For instance, the inverted face experiment aimed at dissociating whether visemic processing depends on face recognition (i.e. on holistic processing) or whether it depends on featural processing (and it does constitute a test, as suggested by the authors, of whether viseme recognition is a linguistic process per se).

Some references:

-Alsius, A., Möttönen, R., Sams, M. E., Soto-Faraco, S., & Tiippana, K. (2014). Effect of attentional load on audiovisual speech perception: evidence from ERPs. Frontiers in psychology, 5, 727.

-Chandrasekaran, C., Trubanova, A., Stillittano, S., Caplier, A., & Ghazanfar, A. A. (2009). The natural statistics of audiovisual speech. PLoS Comput Biol, 5(7), e1000436.

-Jordan, T. R., & Bevan, K. (1997). Seeing and hearing rotated faces: Influences of facial orientation on visual and audiovisual speech recognition. Journal of Experimental Psychology: Human Perception and Performance, 23(2), 388.

-Grant, K. W., & Seitz, P. F. (2000). The use of visible speech cues for improving auditory detection of spoken sentences. The Journal of the Acoustical Society of America, 108(3), 1197-1208.

-Grant, K. W., Van Wassenhove, V., & Poeppel, D. (2004). Detection of auditory (cross-spectral) and auditory-visual (cross-modal) synchrony. Speech Communication, 44(1-4), 43-53.

-Schwartz, J. L., Berthommier, F., & Savariaux, C. (2002). Audio-visual scene analysis: evidence for a" very-early" integration process in audio-visual speech perception. In Seventh International Conference on Spoken Language Processing.

-Schwartz, J. L., Berthommier, F., & Savariaux, C. (2004). Seeing to hear better: evidence for early audio-visual interactions in speech identification. Cognition, 93(2), B69-B78.

-Tiippana, Kaisa, T. S. Andersen, and Mikko Sams. (2004) "Visual attention modulates audiovisual speech perception." European Journal of Cognitive Psychology 16.3: 457-472.

-van Wassenhove, V. (2013). Speech through ears and eyes: interfacing the senses with the supramodal brain. Frontiers in psychology, 4, 388.

-Van Wassenhove, V., Grant, K. W., & Poeppel, D. (2007). Temporal window of integration in auditory-visual speech perception. Neuropsychologia, 45(3), 598-607.

Reviewer #1:

This work claims to show that learning of word associations during sleep can impair learning of similar material during wakefulness. The effect of sleep on learning depended on whether slow-wave sleep peaks were present during the presentation of that material during sleep. This is an interesting finding, but I have a lot of questions about the methods that temper my enthusiasm.

1) The proposed mechanism doesn't make sense to me: "synaptic down-scaling of hippocampal and neocortical language-related neurons, which were then too saturated for further potentiation required for the wake-relearning of the same vocabulary". Also lines 105-122. What is 'synaptic down-scaling'? what are 'language related neurons'? ' How were they 'saturated'? What is 'deficient synaptic renormalization'? How can the authors be sure that there are 'neurons that generated the sleep- and ensuing wake-learning of ... semantic associations'? How can inferences about neuronal mechanisms (ie mechanisms within neurons) be drawn from what is a behavioural study?

2) On line 54 the authors say "Here, we present additional data from a subset of participants of our previous study in whom we investigated how sleep-formed memories interact with wake-learning." It isn't clear what criteria were used to choose this 'subset of participants'. Were they chosen randomly? Why were only a subset chosen, anyway?

3) The authors do not appear to have checked whether their nappers had explicit memory of the word pairs that had been presented. Why was this not checked, and couldn't explicit memory explain the implicit memory traces described in lines 66-70 (guessing would be above chance if the participants actually remembered the associations).

Reviewer #1:

In the present manuscript, Evans and Burgess present a computational model of the entorhinal-hippocampal network that enables self-localization by learning the correspondence between stimulus position in the environment and internal metric system generated by path integration. Their model is composed of two separate modules, observation and transition, which inform about the relationship between environmental features and the internal metric system, and update the internal metric system between two consecutive positions, respectively. The observation module would correspond to projection from hippocampal place cells (PCs) to entorhinal grid cells (GCs), while the transition module would just update the GCs based on animal's movement. The authors suggest that the system can achieve fast and reliable learning by combining online learning (during exploration) and offline learning (when the animal stops or rests). While online learning only updates the observation model, offline learning could update both modules. The authors then test their model on several environmental manipulations. Finally, they discuss how offline learning could correspond to spontaneous replay in the entorhinal-hippocampal network. While the work will certainly be of great interest to the community, the authors should improve the presentation of their manuscript, and make sure they clearly define the key concepts of their study.

Online learning is clearly explained in the manuscript (e.g. l.101). Both environment structure (PC-PC connections) and the observation models (PC->GC synapses) are learned online, and this leads to stable grid cells. Then, the authors suggest that prediction error between the observation and transition models triggers offline inference that can update both models simultaneously. However, it is hard to figure out what offline learning is exactly. The section "Offline inference: The hippocampus as a probabilistic graph" is quite impossible to follow. Before explicitly defining offline learning the authors introduce a spring model of mutual connection between feature locations, but it is not clearly explained if this network is optimized online or offline.

The end of this section is particularly difficult to follow (line 180): "In this context, learning the PC-GC weights (modifying the observation model) during online localization corresponds to forming spatial priors over feature locations which anchor the structure, which would otherwise be translation or rotation invariant (since measurements are relative), learned during offline inference to constant locations on the grid-map.".

What really triggers offline inference is only explained much further in the manuscript, l. 366. Interestingly, this section refers to Fig. 1G for the first time, and should naturally be moved at the beginning of the manuscript (where Fig.1 is described)

Along the same lines, the role of offline learning should be made much more explicit in Fig. 2.

The frequent references to the method section too often break the flow of paper and make it difficult to follow. The authors should start their manuscript with a clear and simple definition of the core idea and concepts, almost in lay terms and only introducing a few annotations, using Fig. 1 (perhaps with some modification and focusing especially on panels A and F) as a visual support, and to move mathematical equations such as Eq. 3 to the supplementary information.

The authors have tested their model on various manipulations that have been previously carried out in freely moving animals, such as change in visual gain and in environmental geometry. These sections are interesting but, again, would be much clearer if presented after a clear explanation of online and offline learning procedures, not in between.

Finally, the authors discuss the relationship between offline inference and neuronal replay, as observed experimentally in vivo (Figs 6&7). This is interesting but would perhaps benefit from some graphical explanation. It is not immediately obvious to understand the fundamental difference between message passing (Fig. 6A) and simple synaptic propagation of activity among connected PC in CA3. Fig. 7 is actually a nice illustration of the phenomenon and should perhaps be presented before Fig. 6.

Reviewer #1:

The authors present a workflow based on targeted Nanopore DNA sequencing, in which they amplify and sequence nearly full-length 16S rRNA genes, to analyze surface water samples from the Cam river in Cambridge. They first identify a taxonomic classification tool, out of twelve studied, that performs best with their data. They detect a core microbiome and temporal gradients in their samples and analyze the presence of potential pathogens, obtaining species level resolution and sewage signals. The manuscript is well written and contains sufficient information for others to carry out a similar analysis with a strategy that the authors claim will be more accessible to users around the world, and particularly useful for freshwater surveillance and tracing of potential pathogens.

The work is sufficiently well-documented and timely in its use of nanopore sequencing to profile environmental microbial communities. However, given that the authors claim to provide a simple, fast and optimized workflow it would be good to mention how this workflow differs or provides faster and better analysis than previous work using amplicon sequencing with a MinION sequencer.

Many of the June samples failed to provide sufficient sequence information. Could the authors comment on why these samples failed? While some samples did indeed have low yields, this was not the case for all (supp table 2 and supp figure 5) and it could be interesting to know if they think additional water parameters or extraction conditions could have affected yields and subsequent sequencing depth.

One of the advantages of nanopore sequencing is that you can obtain species-level information. It would therefore be helpful if the authors could include information on how many of their sequenced 16S amplicons provided species-level identification.

While the overall analysis of microbial communities is well done, it is not entirely clear how the authors define their core microbiome. Are they reporting mainly the most abundant taxa (dominant core microbiome), and would this change if you look at a taxonomic rank below the family level? How does the core compare, for example, with other studies of this same river?

This is a page note. I can write overall comments about the pre-print here.

Tags can also be added below.

Reviewer #1:

This study takes two existing models of hippocampal theta rhythm generation, a reduced one with two populations of Izhikevich neurons, and a detailed one with numerous biophysically detailed neuronal models. The authors do some parameter variation on 3 parameters in the reduced model and ask which are sensitive control parameters. They then examine control of theta frequency through a phase response curve and propose an inhibition-based tuning mechanism. They then map between the reduced and detailed model, and find that connectivity but not synaptic weights are consistent. They take a subset of the detailed model and do a 2 parameter exploration of rhythm generation. They compare phenomenological outcomes of the model with results from an optogenetic experiment to support their interpretation of an inhibition-based tuning mechanism for intrinsic generation of theta rhythm in the hippocampus.

General comments:

1) The paper shows the existence of potential rhythm mechanisms, but the approach is illustrative rather than definitive. For example, in a very lengthy section on parameter exploration in the reduced model, the authors find some domains which do and don't exhibit rhythms. Lacking further exploration or analytic results, it is hard to see if their interpretations are conclusive.

2) The authors present too much detail on too few dimensions of parameters. An exhaustive parameter search would normally go systematically through all parameters, and be digested in an automated manner. For reporting this, a condensed summary would be presented. Here the authors look at 3 parameters for the reduced model and 2 parameters in the detailed one - far fewer than the available parameter set. They discuss the properties of these parameter choices at length, but then pick out a couple of illustrative points in the parameter domain for further pursuit. This leaves the reader rather overwhelmed on the one hand, and is not a convincing thorough exploration of all parameters of the system on the other.

3) I wonder if the 'minimal' model is minimal enough. Clearly it is well- supplied with free parameters. Is there a simpler mapping to rate models or even dynamical systems that might provide more complete insights, albeit at the risk of further abstraction?

4) Around line 560 and Fig 12 the authors conclude that only case a) is consistent with experiment. While it is important to match data to experiment, here the match is phenomenological. It misses the opportunity to do a quantitative match which could be done by taking advantage of the biological detail in the model.

5) The paper is far too long and is a difficult read. Many items of discussion are interspersed in the results, for example around line 335 among many others.

Reviewer #1:

Studies in mouse models and humans show synapse loss and dysfunction that precede neurodegeneration, raising questions about timing and mechanisms. Using longitudinal in vivo 2-photon imaging, Jackson et al., investigate pre- and post-synaptic changes in rTg4510 mice, a widely used mouse model of tauopathy. Consistent with cross sectional studies, the authors observed a reduction in density of presynaptic axons and dendritic spines in layer 1 cortex that relate to degeneration of neurites and dendrites over time. Taking advantage of an inducible model to overexpress tau p301L, they show that reducing expression of tau by DOX early in disease progression, resulted in amelioration of synapse loss, also consistent with other studies. Interestingly, the authors observed a significant reduction of dendritic spines less than a week before dendrite degeneration. In contrast, they observed plasticity and turnover of presynaptic structures weeks before axonal degeneration, suggesting different mechanisms.

Overall the results are interesting and largely consistent with previous findings. The new findings shown in Figures 5 and 6 address the timing of pre and postsynaptic loss and structural plasticity and reveal interesting differences; however, the data are highly variable and there are several issues that diminish enthusiasm as outlined below. Moreover, this study does not include new biological or mechanistic insight into the differences in pre- and post-synaptic changes from previous work in the field.

The main weakness relates to the significance and relevance beyond this specific mouse model and brain region. I appreciate the strengths but also technical challenges of in vivo longitudinal imaging, including a small field of view. Thus, the rationale and choice of model and brain region, and validation of key findings is critical to support conclusions. In this case, the tau model, although used by others, has several caveats relevant to the investigation of synapse loss (see point 2 below) that weaken this study and its impact.

1) Most of the work in the model related to synapse loss and dysfunction have been carried out in hippocampus and other regions of cortex in this model and tau and amyloid models. Here the authors focused on layer 1 of (somatosensory) cortex and followed neurites of pyramidal cells labeled with AAV:GFP, an approach that does not enable one image and track axons and dendrites from large numbers of neurons. They observed divergent dynamics in spine and presynaptic TBS of individual dendrites and axons. Given the small number of neurons sampled, significant noise in their imaging data, these findings need more validation using other approaches. This is particularly important for the data and conclusion drawn from Figures 5 and 6 (see point 3).

To estimate the overall effect of genotype the authors fitted Generalized Additive Mixed Models (GAMMS) to their data given the variability in the data within animals and genotype. It would be helpful to those less familiar to provide more comparisons of data using additional statistical tests and analyses along with power analyses calculations.

2) Major caveat with inducible Tau mode Tg4510. While this inducible model has the advantage of controlling timing of tau overexpression in neurons, a recent study by Gamache et al (PMID: 31685653) demonstrated that there are issues with the transgene insertion site and factors other than tau expression are actually what is driving the phenotype. Thus, differences in synaptic and behavioral phenotypes are based on the mouse line used and this needs to be carefully controlled. This was not addressed or discussed. See https://pubmed.ncbi.nlm.nih.gov/31171783/ and https://pubmed.ncbi.nlm.nih.gov/30659012/

3) The interesting new findings presented in Figures 5 and 6 that address timing and differences in axonal and dendritic/spine plasticity and loss need to be validated with more neurons and animals. The sample size is small ( i.e. n= 18 axons from 7 animals and not clear how many neurons. Given the significant variability of the data even within animals, these experiments and data are considered preliminary.

4) How does anesthesia influence these changes in structural plasticity observed? This was not addressed or discussed.

Reviewer #1:

Xu and colleagues compared the intersubject correlation (ISC) and intersubject functional connectivity (ISFC) of participants listening to narrative and argumentative texts while undergoing fMRI. Replicating earlier findings, they show that ISC in the DMN was greater when participants listened to an intact narrative than when they listened to a sentence-scrambled version of the same narrative. Listening to a sentence-scrambled argument elicited ISC in language and control regions of the brain, though interestingly, there was no region in the brain where ISC was greater when participants listened to an intact version of the argument. Instead, there was greater ISFC between the IPS and language areas of the brain when participants listened to the intact argument than when they listened to the scrambled argument. The authors interpret their results as suggesting that listening to the intact argument did not recruit additional brain systems, but instead promoted the cooperation between regions that were already involved in processing the argument.

Most prior work using "naturalistic stimuli" has examined the neural responses to narratives. This manuscript extends this work in an important way by examining how the brain responds to arguments, which comprise a non-trivial proportion of the linguistic content people are exposed to on a daily basis. The ISFC results (Fig. 7) are particularly noteworthy and novel. My main concerns have to do with the possibility that ISC for the scrambled argument seems to be stronger and more extensive than that for the intact argument, and how this might affect the authors' interpretation of their results. Below are some suggestions and comments which I think the paper could benefit from considering further:

1) I think it would be helpful to run the Scrambled Argument > Intact Argument ISC contrast. Visual inspection of Figure 2 suggests that ISC for the scrambled argument might be stronger than that for the intact argument, especially in control regions. If this is truly the case, I think the authors should discuss what this might imply about what is happening during the scrambled condition and if this affects thinking of the scrambled condition as a control for low-level linguistic features. In particular, the 2.97 out of 5 comprehensibility rating of the scrambled arguments suggests that participants might have understood the scrambled arguments. If participants are actively trying to make sense of the scrambled argument text, it seems like this could then drive observed differences in ISFC between the intact and scrambled arguments as well (e.g., decreased connectivity between control and language regions when trying to make sense of scrambled text, rather than increased connectivity between control and language regions when processing an intact argument).

2) More broadly, I think the authors need to make sure their effects aren't driven by the scrambled conditions. For example, for Figure 2 - figure supplement 2, the (Intact Narrative - Scrambled Narrative) > (Intact Argument - Scrambled Argument) contrast can be driven by high ISC in the Scrambled Argument condition, which would suggest a different interpretation of the results. My suggestion would be to run the contrast as (Intact Narrative - Scrambled Narrative) > max((Intact Argument - Scrambled Argument),0) to make sure that the contrast isn't driven by a negative value on the right hand side of the inequality.

3) Point 2 also applies to Figures 6 and 7. Relatedly, the rightmost panel of Figure 6C suggests that the analysis is indeed capturing some edges where the SES of the Scrambled Argument is greater than that of the Intact Argument.

4) How well do the vertexes identified in Figure 7D overlap with the Intact Argument > Resting map? Given the authors interpretation that the ISFC results suggest cooperation between areas involved in processing the intact stimulus, I think this should be properly assessed.

5) Both ISC and ISFC capture only signal that is shared across participants. Most narratives are crafted such that all listeners have a similar interpretation. This is unlike arguments, where different listeners might agree with an argument to a different extent. If listeners had differing interpretations of the argument, ISC/ISFC would miss brain activity/connectivity involved in processing an argument. I think this possibility should be considered and discussed, especially given the null DMN finding for the argumentative texts.

6) For the t-tests on the behavioral ratings , it looks like the authors collapsed over the two texts within a category. This doesn't seem right, given that the ratings for each text are dependent. A mixed model approach would be more appropriate. I doubt this will change the results, but I think it would be good to follow best practices when possible.

Reviewer #1:

Major issues:

I have two major comments on the work.

1) The authors motivate the work from the use of naturalistic speech, and the application of the developed method to investigate, for instance, speech-in-noise deficits. But they do not discuss how comprehensible the peaky speech in fact is. I would therefore like to see behavioural experiments that quantitatively compare speech-in-noise comprehension, for example SRTs, for the unaltered speech and the peaky speech. Without such a quantification, it is impossible to fully judge the usefulness of the reported method for further research and clinical applications.

2) The neural responses to unaltered speech and to peaky speech are analysed by two different methods. For unaltered speech, the authors use the half-wave rectified waveform as the regressor. For peaky speech, however, the regressor is a series of spikes that are located at the timings of the glottal pulses. Due to this rather different analysis, it is impossible to know to which degree the differences in the neural responses to the two types of speech that the authors report are due to the different speech types, or due to the different analysis techniques. The authors should therefore use the same analysis technique for both types of speech. It might be most sensible to analyse the unaltered speech through a regressor with spikes at the glottal pulses a well. In addition, it would be good to see a comparison, say of a SNR, when the peaky speech is analysed through the half-wave rectified waveform and through the series of spikes. This would also further motivate the usage of the regressor with the series of spikes.

Reviewer #1:

The authors studied the over-representation of imprinted genes in the mouse brain by using fifteen single-cell RNA sequencing datasets. The analysis was performed at three levels 1) whole-tissue level, 2) brain-region level, and 3) region-specific cell subpopulation level. Based on the over-representation and gene-enrichment analyses, they interpreted hypothalamic neuroendocrine populations and monoaminergic hindbrain neurons as specific hotspots of imprinted gene expression in the brain.

Objective:

Though the study is potentially interesting, the expression of imprinted genes in the brain and hypothalamus is already known (Davies W et al., 20005, Shing O et al. 2019, Gregg et al, 2010 including many other studies cited in the paper). However, the authors put forth two objectives, the first being whether imprinted gene expression is actually enriched in the brain compared to other adult tissues, where they did find brain as one of the tissues with over-represented imprinted genes. Secondly, whether the imprinted genes are enriched in specific brain regions. The study objectives cannot qualify as completely novel as it is the validation of most of what is already known using scRNA-seq datasets.

Methods and Results

Pros:

-15 scRNA-seq datasets were analysed independently and they were processed as in the original publication.

-Two enrichment methods used to find tissue-specific enrichment of imprinted genes and appropriate statistics applied wherever necessary.

Concerns:

-It is not clear how the over-representation using fisher's exact test was calculated? It would be appropriate to include the name of the software or R package, if used, in the basic workflow section of Materials and methods.

-Why did authors particularly use Liger in R for GSEA analysis?

-GSEA plots generated using Liger and represented for each analysis in the paper by itself does not look informative. For eg. in figure 4 and other GSEA plots in the paper- i) Which 'score' does the Y-axis represent? Include x-axis label and mention corrected GSEA q value either in the legend or the figure. ii) Was the normalized enrichment score (NES) calculated? What genes in the cluster represent maximum enrichment? A heat map of the imprinted genes contributing to the cell cluster will add more clarity to the GSEA plots.

-Apart from the tissue-specific enrichment of gene sets, a functional GO/pathways enrichment of the group of imprinted genes will strengthen the connection of these genes with feeding, parental behavior and sleep.

-Are these imprinted genes coexpressed across the analyzed brain structures, as the authors repeatedly stress on the functioning of imprinted genes as a group?

-A basic workflow schematic might be necessary for an easy and quick understanding of the methods.

Overall, the study gives some insight into the brain regions, particularly cell clusters in the brain where imprinted genes could be enriched. However, the nature of the study is preliminary and validates most of previous studies. The authors have already highlighted some of the limitations of the study in the discussion.

Reviewer #1:

The manuscript “A computationally designed fluorescent biosensor for D-serine" by Vongsouthi et al. reports the engineering of a fluorescent biosensor for D-serine using the D-alanine-specific solute-binding protein from Salmonella enterica (DalS) as a template. The authors engineer a DalS construct that has the enhanced cyan fluorescent protein (ECFP) and the Venus fluorescent protein (Venus) as terminal fusions, which serve as donor and acceptor fluorophores in resonance energy transfer (FRET) experiments. The reporters should monitor a conformational change induced by solute binding through a change of the FRET signal. The authors combine homology-guided rational protein engineering, in-silico ligand docking and computationally guided, stabilizing mutagenesis to transform DalS into a D-serine-specific biosensor applying iterative mutagenesis experiments. Functionality and solute affinity of modified DalS is probed using FRET assays. Vongsouthi et al. assess the applicability of the finally generated D-serine selective biosensor (D-SerFS) in-situ and in-vivo using fluorescence microscopy.

Ionotropic glutamate receptors are ligand-gated ion channels that are importantly involved in brain development, learning, memory and disease. D-serine is a co-agonist of ionotropic glutamate receptors of the NMDA subtype. The modulation of NMDA signalling in the central nervous system through D-serine is hardly understood. Optical biosensors that can detect D-serine are lacking and the development of such sensors, as proposed in the present study, is an important target in biomedical research.

The manuscript is well written and the data are clearly presented and discussed. The authors appear to have succeeded in the development of D-serine-selective fluorescent biosensor. But some questions arose concerning experimental design. Moreover, not all conclusions are fully supported by the data presented. I have the following comments.

1) In the homology-guided design two residues in the binding site were mutated to the ones of the D-serine specific homologue NR1 (i.e. F117L and A147S), which lead to a significant increase of affinity to D-serine, as desired. The third residue, however, was mutated to glutamine (Y148Q) instead of the homologous valine (V), which resulted in a substantial loss of affinity to D-serine (Table 1). This "bad" mutation was carried through in consecutive optimization steps. Did the authors also try the homologous Y148V mutation? On page 5 the authors argue that Q instead of V would increase the size of the side chain pocket. But the opposite is true: the side chain of Q is more bulky than the one of V, which may explain the dramatic loss of affinity to D-serine. Mutation Y148V may be beneficial.

2) Stabilities of constructs were estimated from melting temperatures (Tm) measured using thermal denaturation probed using the FRET signal of ECFP/Venus fusions. I am not sure if this methodology is appropriate to determine thermal stabilities of DalS and mutants thereof. Thermal unfolding of the fluorescence labels ECFP and Venus and their intrinsic, supposedly strongly temperature-dependent fluorescence emission intensities will interfere. A deconvolution of signals will be difficult. It would be helpful to see raw data from these measurements. All stabilities are reported in terms of deltaTm. What is the absolute Tm of the reference protein DalS? How does the thermal stability of DalS compare to thermal stabilities of ECFP and Venus? A more reliable probe for thermal stability would be the far-UV circular dichroism (CD) spectroscopic signal of DalS without fusions. DalS is a largely helical domain and will show a strong CD signal.

3) The final construct D-SerFS has a dynamic range of only 7%, which is a low value. It seems that the FRET signal change caused by ligand binding to the construct is weak. Is it sufficient to reliably measure D-serine levels in-situ and in-vivo? In Figure 5H in-vivo signal changes show large errors and the signal of the positive sample is hardly above error compared to the signal of the control. Figure 5G is unclear. What does the fluorescence image show? Work presented in this manuscript that assesses functionality and applicability of the developed sensor in-situ and in-vivo is limited compared to the work showing its design. For example, control experiments showing FRET signal changes of the wild-type ECFP-DalS-Venus construct in comparison to the designed D-SerFS would be helpful to assess the outcome.

4) The FRET spectra shown in Supplementary Figure 2, which exemplify the measurement of fluorescence ratios of ECFP/Venus, are confusing. I cannot see a significant change of FRET upon application of ligand. The ratios of the peak fluorescence intensities of ECFP and Venus (scanned from the data shown in Supplementary Figure 2) are the same for apo states and the ligand-saturated states. Instead what happens is that fluorescence emission intensities of both the donor and the acceptor bands are reduced upon application of ligand.