Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: MULTI-GENE INCONGRUENCE CONSISTENT WITH HYBRIDISATION IN CLADOCOPIUM (SYMBIODINIACEAE), AN ECOLOGICALLY IMPORTANT GENUS OF CORAL REEF SYMBIONTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Brian et al. use Symbiodiniaceae sequencing data to look for incongruence in different gene regions, which would be consistent with (but not conclusive evidence of) hybridization among distinct species of coral symbionts. They apply several phylogenetic analyses to a set of 158 samples of symbiont communities residing in coral tissues, identifying 3 with clear patterns of incongruence between nuclear and organellar genomes in the most abundant symbiont sequences per gene. They discuss at length how the most parsimonious explanation is symbiont hybridization.

This is an extremely well written manuscript. The topic of Symbiodiniaceae hybridization is both understudied and controversial, and the authors deftly guide the reader through the nuances and difficulties of testing the hybridization hypothesis. They are quite forward about how their results are not definitive, but represent an exciting first step. Though I still have some “big picture” reservations about their methods, I find their execution sound and I appreciate their responsible approach to reporting their findings. Most of my suggestions are minor, though I do ask that the authors consider a potential problem that they don’t address in the manuscript (how the combination of sampling a symbiont community and using multicopy genes may lead to artificial incongruence signal when only the most abundant variants are selected for analysis).

My biggest concern crops up in L162-164. To arrive at one variant per gene in order to perform the incongruence analyses, the authors selected only the most abundant ITS2 variant within a given sample after amplicon sequencing. I have a general concern about combining this selective approach with Sanger sequencing of cob and psba. Here’s my line of thinking:

First, every sample of a given coral contains millions of individual symbiont cells. Second, the symbionts are a community of potentially several different species. Third, each symbiont species may encompass several genetically unique strains. Finally, the ITS2 region is part of a multicopy array, so within each unique symbiont genome, there is the potential for several sequence variants to exist for this gene. Although concerted evolution generally keeps sequence variants more similar within species than between species, the distribution of variants within a sample of a community can still be problematic. Certain variants may be maintained at different frequencies among different genomes within the same species or even across species. Sometimes a given variant is dominant in many different species, and other times, a single species contains different dominant variants depending on which individual cell is sampled.

So amplicon sequencing of ITS2 is going to capture a lot of variants from many different sources (interspecies, intraspecies, and intragenomic). However, direct Sanger sequencing of cob and psba is presumably only going to return the single most abundant variant (or whichever variant is most amenable to PCR amplification). While cob is fairly well conserved within a species and across individuals, psba, like ITS2, is multicopy. As far as I know, at this point it has not been established whether there is any association within a given genome between ITS2 variant abundance and psba variant abundance, and if so, to what extent these associations may vary in different populations.

Consider a hypothetical genome where ITS2 variant A represents 90% of the intragenomic variation, while ITS2 variant B represents 10%. In the same genome, psba variant 1 represents 90% of the intragenomic variation, while psba variant 2 represents 10%. We’ll call this the 9:1/9:1 genome to represent the ratios of variants for ITS2 and psba, respectively. It’s entirely possible that in another individual, the ratio is not the same; for example, you could get a 9:1/1:9 genome. Or a 9:1/4:6 genome. When millions of individuals with potentially different variant ratios across different genes are sampled from a symbiont community and the DNA is extracted, all of these variants are mixed into one giant pot.

Choosing the most abundant variant for a given multicopy gene (as was done for ITS2 after NGS, or through Sanger sequencing for psba) captures only the most abundant ratio after homogenizing all variants, but does not necessarily reflect the true gene sequence associations for the most abundant individuals within the population. I imagine in most cases it would, but I could also imagine rarer cases where a given population in a subset of samples happens to have a skewed intragenomic variant ratio distribution such that even though the most abundant sequence variants are represented WITHIN each gene region, the most abundant combination of variants ACROSS the three regions is not represented. I believe that this could manifest itself in the data as incongruence in a rare subset of samples, even though sequence combinations lacking incongruence could be found in isolation as distinct species entities in other community samples.

I think the only way to address this issue would be to sequence multiple markers from the same DNA strand through long-read sequencing, thus preserving the ratio of intragenomic variants within a given genome. Of course, that wouldn’t work for markers distributed across nuclear, mitochondrial, and chloroplast genomes. I don’t have a solution, but I do feel this issue needs to be acknowledged. The problem is unique to the way that the authors have sampled symbiont communities and then reconstructed gene region associations from only the most abundant sequences for multicopy genes. It’s a limitation of the technologies and genes we have available for Symbiodiniaceae phylogenetic analyses, and I feel it should be mentioned explicitly in addition to the other issues like independent lineage sorting.

My other major concern relates to the findings reported from L506-514 related to background symbiont populations. These results should be included in the Results section. They deserve a figure of their own as it’s hard to grasp the key concept without a visual. I’d recommend a background symbiont proportion diagram from the representative samples mentioned in the text.

L56: Should cite the genus revision here: LaJeunesse et al. 2018 Current Biology
L59: Change to “exclusively asexual in hospite”
L95: Change to “in several instances”
L127: Change to “warrants further study”
L131: Change to “genes are typically inherited biparentally”
L243-244: Why was the default changed?
L258-268: I didn’t quite follow how the reciprocal tests were evaluated to recognize whether a tree that was statistically significant was truly incongruent or not
L266: Please define “RELL bootstrap”
L444-446: You’re describing concerted evolution; I'd use the term here
L483: Change to “incongruence between nuclear”
L538: Delete “reasonably”
L541: Change to “lower-resolution than actin”


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DO HUMAN SCREAMS PERMIT INDIVIDUAL RECOGNITION?
Review round: 1
Reviewer: 1

Output:
Basic reporting: Engelberg et al. report an experiment exploring whether human listeners can accurately perceive identity from (human) screams through a speaker discrimination task. The authors report that screams can indeed convey information about speaker identity (d’ > 1 and mean accuracy > .5), with some effects of exposure, confidence and vocaliser gender are also apparent. An acoustic analysis did not yield any significant effects.

The study is written and structured in a clear way. The literature on the topic is reviewed, referenced and synthesised into an informative introduction section. Figures and tables are mostly adequately labelled and the raw data has been shared. Hypotheses and predictions are started clearly at the start of the introduction. Some minor comments about the basic reporting are listed below:

1. The authors state that little research into identity perception from non-verbal vocalisations, such as laughter and screams has been conducted for humans (l. 66). I would point out that there we have run a couple studies looking at identity perception from laughter, which may be relevant to the current study, especially given that there are only a small number of studies available.

-Lavan N., Scott S.K. & McGettigan C. (2016). Impaired generalization of speaker identity in familiar and unfamiliar voices. Journal of Experimental Psychology: General, 145(12), 1604-1614.
- Lavan N., Short B., Wilding A., & McGettigan C. (2018). Impoverished encoding of speaker identity in spontaneous laughter. Evolution and Human Behavior, 39(1), 139-145.

2. The x axis in Figure 1 is labelled as showing percent but the number only range from 0 to 1 - please amend this.

3. For all figures, it would be nice to explain in the figure legends what the error bars are showing.
Experimental design: The study falls within the aims and scope of articles published within PeerJ. As the authors accurately point out, little is known about the perception of identity from nonverbal/nonlinguistic vocal signals in humans and this study thus provides a novel contribution, addressing a gap in the literature.

The experimental design appears to be well thought out and appears to have been well-conducted. Methods are described adequately and in sufficient detail - I have some comments listed below regarding the some of the details of the design and the statistical analysis.

1. The current study includes a wide range of screams that do not only differ in their broad acoustic properties but seemingly also in the contexts in which they were produced. Since there is previous evidence showing differences in the perception of a type vocalisation (e.g. laughter) produced in different contexts, do the authors think that similar effects could be present for screams? It is of course difficult to post-hoc reconstruct why a scream was produced and the number of screams was limited in this study which precludes any formal analysis. It might however benefit the paper to include some notes on the heterogeneity of the types of screams - not only in terms of their acoustics but also the context they were produced (pain, anger, fear, etc.) in the discussion of the paper.

2. I was wondering whether the items within the stimulus pairs were randomised across participants or whether all participants were presented with the same pairs? From what I glean from the methods, it sounds like all participants were presented with the same pairs.

3. While I will not insist on this being changed for this manuscript, I would strongly encourage the authors to consider running their statistical analyses using (generalised) linear mixed models. This would allow them to account for participant as well as item-specific effects. Accounting for the item-specific (or here pair-specific) effects seems to be particularly important in the current study if the pairs were not shuffled (see point 2 above), thus resulting in a relatively low number of different pairs.

4. I was also finding myself getting a little confused when the for sections of the results, analyses were reported with the SAME-A trials included and then excluded, alongside analyses including and excluding the accidentally duplicated pairs as well as with and without premature responses. While I appreciate that some of these analyses are reported to provide full transparency, it might be desirable to streamline the reporting of the results a little bit. This could be achieved by perhaps always excluding the SAME-A trials after showing that they differ from the remaining trials (analyses could be moved into supplementary materials) and consistently omitting duplicated items and pre-mature trials.

5. While it is commendable to assess participants everyday exposure to screams via a questionnaire, this questionnaire is only tackles exposure through media while neglecting real-life exposure to screams. I can appreciate why this was done - perhaps to avoid asking questions that may be ethically a bit challenging - a broader measure of experience would have been interesting. A brief acknowledgement that screams are also encountered outside of video games might be useful in the discussion or methods section.

6. I was curious about why this particular type of acoustic analysis was chosen. While I am aware that it can be challenging to extract reliable acoustic measures for, for example, mean/median F0, spectral measures or measures of periodicity from some non-verbal vocalisations, I am from my reading to the literature on this topic (in psychology) a bit more used to seeing this type of analysis for human vocalisations. Maybe an analyses using these types of measures might shed some more light into the acoustic properties that may underpin listeners’ judgements?
Validity of the findings: The sample size (>100 participants) is impressive although some effects of listener and speaker characteristics are small and seem bounce between being statistically significant and not significant depending on which trials are excluded or included (see point 4 of the previous section). The effects relating to the main research question appear to be however robust and sizeable.

Much like the introduction, the discussion is well structured and clearly written. Results are linked back to and evaluated within the existing literature.
Additional comments: All in all, I believe that this study is well-conducted and of interest to the community and should be published after some revisions to mainly tidy up the reporting of the results.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DO HUMAN SCREAMS PERMIT INDIVIDUAL RECOGNITION?
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors examine the ability of human listeners to gauge individual identity from screams. This paper represents an important, and timely, contribution to the very small (but growing) body of research on human nonverbal vocalisations.

The paper is well written – clear, succinct, and with a logical flow. However the Introduction/Discussion sections would benefit from the addition of several omitted yet highly relevant references, as noted below.

Perhaps the most important references omitted are a series of recent papers examining identity perception from laughs (and other vocal stimuli) from Lavan et al. ( Scott/ McGettigan labs).

For instance, Lavan et al., 2018c (see refs below) have shown a limited capacity, in humans, to identify individuals from *spontaneous* laughter. These papers are obviously highly relevant and should be discussed (currently only one is cited)  – particularly the potential distinction between cues to identity in volitional vs spontaneous nonverbal vocalisations. Based on the sources for stimulus extraction outlined by the authors (L 160), it seems most scream stimuli used in this paper were probably ‘acted’, e.g., from films and adverts, and therefore would not classify as *spontaneous*. However, some of the screams could have been genuine (e.g., those taken from You Tube videos or sound banks). The high degree of accuracy in listeners’ ability to gauge identity from screams (current paper) compared to laughter (Lavan et al.) might be due in part to the use of acted versus genuine vocal stimuli. Acted screams could for instance follow a more stereotyped pattern within individuals and thus be easier for listeners to match. Another (non-mutually exclusive) explanation for the different results of these papers could be the type of vocalisation – e.g., laughs are lower-pitched and likely to vary more, acoustically, across bouts within-individuals compared to screams.

Other recent and highly relevant papers on human nonverbal vocalisations (incl. distress [fear and pain] screams) that have been omitted include:
- Raine et al., 2017, 2018a, b (recognition of sex, strength, body size etc. from nonverbal vocalisations);
- Anikin & Lima, 2017 (Perceptual and acoustic differences between authentic and acted nonverbal vocalizations)
- Anikin & Persson, 2017 (Corpus of naturalistic nonverbal vocalisations from amateur videos)

The authors could also include a short discussion of the relevance of nonverbal vocalisations, from an evolutionary and social (functional) perspective, and highlight the important ways in which nonverbal vocalisations differ from speech in this regard (acoustically/functionally). Nonverbal vocalisations are a common part of the human vocal repertoire yet hugely understudied. This fact underscores the importance of this paper, and calls for more research in this area.

Can the authors include the 10-item questionnaire, developed in their lab to measure exposure to screams in media, as supplementary material?

Including some, if not all, the scream pairs as supplementary material (especially those corresponding to the spectrograms in Fig 5) would also increase the transparency and replicability of this work.

The green and blue colours used for bar graphs are of a similar intensity and will not reproduce well in black and white. I suggest using more contrasting hues.
Experimental design: In general, the methods are clear and fairly well justified, particularly stimulus selection, stimulus preparation and playback procedures.

Where the methods are lacking is in acoustic analysis.

The acoustic analysis section (L277 – 301) is vague and poorly justified. For example, “Spectrograms of screams were generated in Adobe Audition CC and qualitatively inspected in comparison to Same Scores. Based on these initial observations, we identified two acoustic variables that seemed to correlate with participant responses: harmonic regime and bifurcations.”
-	What exactly do the authors mean by “we identified two acoustic variables that seemed to correlate with participant responses”?
-	Which acoustic features did the authors consider in their analyses, initially?
o	I am surprised that fundamental frequency/pitch (F0) is ignored, as this is a key predictor of vocal distress and probably the most salient nonverbal feature of human vocalisations. It is also a highly sexually dimorphic feature of the voice that could partly explain the sex-effects observed, e.g., 336. Lower-pitched (male) vocalisations will have a denser harmonic spectrum that could assist in formant discrimination and identity cues as noted on L 425 (see also Charlton et al., 2013; Pisanski et al., 2014).  In examining F0 the authors could test the prediction noted on L445, as well as how F0 predicted listeners’ judgments/accuracy scores.
o	Formants, as a key identity cue, could also be examined – though formants may be too difficult to measure from very high F0 vocalisations (as in Raine et al. 2017 with tennis grunts).
-	Were observers (L 285) blind? What criteria did they rely on to make these classifications?
-	Why was duration used for the Same-A condition, rather than e.g., F0?

On what basis were sample sizes (of voices/listeners) selected?

The uneven ratio of males to females (more females), both in vocal stimuli (Table 1) and among raters, should be discussed as a limitation. While an overrepresentation of women is common in student samples from psychology/behavioural sciences departments, the overrepresentation of female voices in the scream stimuli is more difficult to justify. How was this biased ratio controlled in the analyses of gender effects (L 336)?

Please also note whether the vocalisations were fully randomised, or blocked by sex, and how this might have affected accuracy in identification rates (considering also the biased sex ratio for screams).

Using a PCA on questionnaire items is not very common. Can the authors explain the rationale for this approach in more detail and provide justification (e.g., references?) for its validity?
Validity of the findings: Screams were extracted from online sources such as films and sound banks, from which three types of stimulus pairs were composed: Same-A (same scream from same vocaliser, with two different durations); Same-B (different screams from same vocaliser); Different (different screams from different vocalisers). Listeners were then tasked with indicating whether the two screams in each pair were produced by the same person, or two different people. The results indicate an impressive level of accuracy in listeners’ ability to gauge identity from screams, with higher than 70% accuracy scores in all three conditions.

As described in Section 1 (Basic reporting), a key issue that is largely ignored in this paper is the distinction between spontaneous/genuine vs. volitional/acted vocalisations, as identity cues may be more salient in the latter. The authors should explicitly comment on the proportion of scream stimuli that were likely acted vs genuine (to the extent that this can be discerned) and, most importantly, how this could affect their results. If possible, I would suggest controlling for this factor in their analyses. I’ve listed many references relevant to this topic below.

In terms of acoustic analysis, the authors conducted a post-hoc investgiation, and only examined harmonic regime and bifurcations. As described in Section 2 (Experimental design) I strongly suggest including additional justification for, and description of, their acoustic analyses, and to expand on the number of acoustic features analysed.
It is unclear why the authors have omitted several key acoustic factors (particularly F0, formants, and duration) from their analyses, given evidence that these features are key predictors in listeners’ voice-based judgments of a variety of speaker traits (and F0/formants are highly sexually dimorphic). Formants are also a key identity cue in humans, as in other mammals – see e.g., references listed below. Duration and F0 are also important predictors of genuine vs. authentic vocalisations (see e.g., Bryant & Aktipis 2014; Anikin & Lima, 2017).

References :

Anikin, A., & Persson, T. (2017). Nonlinguistic vocalizations from online amateur videos for emotion research: A validated corpus. Behavior research methods, 49(2), 758-771.

Anikin, A., & Lima, C. F. (2017). Perceptual and acoustic differences between authentic and acted nonverbal emotional vocalizations. The Quarterly Journal of Experimental Psychology, 1-21.

Bryant, G. A., & Aktipis, C. A. (2014). The animal nature of spontaneous human laughter. Evolution and Human Behavior, 35(4), 327-335.

Charlton, B. D., Taylor, A. M., & Reby, D. (2013). Are men better than women at acoustic size judgements?. Biology letters, 9(4), 20130270.

Lavan, N., Burton, A. M., Scott, S. K., & McGettigan, C. (2018a). Flexible voices: identity perception from variable vocal signals. Psychonomic Bulletin & Review, https://doi.org/10.3758/s13423-018-1497-7
Lavan, N., Domone, A., Fisher, B., Kenigzstein, N., Scott, S. K., & McGettigan, C. (2018b). Speaker Sex Perception from Spontaneous and Volitional Nonverbal Vocalizations. Journal of Nonverbal Behavior, 1-22.

Lavan, N., Short, B., Wilding, A., & McGettigan, C. (2018c). Impoverished encoding of speaker identity in spontaneous laughter. Evolution and Human Behavior, 39(1), 139-145.

Lavan, N., & McGettigan, C. (2017). Increased discriminability of authenticity from multimodal laughter is driven by auditory information. The Quarterly Journal of Experimental Psychology, 70(10), 2159-2168.

Pisanski, K., Fraccaro, P. J., Tigue, C. C., O'connor, J. J., & Feinberg, D. R. (2014). Return to Oz: Voice pitch facilitates assessments of men’s body size. Journal of Experimental Psychology: Human Perception and Performance, 40(4), 1316.

Raine, J., Pisanski, K., & Reby, D. (2017). Tennis grunts communicate acoustic cues to sex and contest outcome. Animal Behaviour, 130, 47-55.

Raine, J., Pisanski, K., Oleszkiewicz, A., Simner, J., & Reby, D. (2018). Human listeners can accurately judge strength and height relative to self from aggressive roars and speech. iScience, 4, 273-280.

Raine, J., Pisanski, K., Simner, J., & Reby, D. (2018). Vocal communication of simulated pain. Bioacoustics, 1-23.
Additional comments: Please refer to comments from Sections 1-3 above.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DO HUMAN SCREAMS PERMIT INDIVIDUAL RECOGNITION?
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is largely well-written, appropriately structured and unambiguous. All of the relevant raw data and analysis outputs were made available. Overall, the study will be a worthwhile addition to the literature, but in my assessment there are several issues with the analysis and Discussion that should be addressed before publication.

Please see below for specific comments on these matters.
Experimental design: I found the paradigm used by the authors to be appropriate for examining the extent to which humans are able to identify whether sequentially heard screams were produced by the same vocaliser. The ecological validity of this paradigm to the 'real world' problem  of being able to identify which of 30 odd group-members produced an unseen scream (as demonstrated in primate literature) is debatable, but this is acknowledged by the authors in their Discussion. However, it would greatly improve the Introduction if these limitations were also outlined there, as well as how the specific aims of this study will inform the broader question. Currently, this link is not as clear as it could be.

The methods were very clearly and thoroughly described such that replication would be straightforward. However, the statistical software used for analysis is not specified, which I would encourage. If R was used, then the relevant scripts would be a welcome addition to the supplemental materials.

My biggest methodological concern is that the authors approach to acoustic analysis was somewhat unconventional. They have taken a qualitative (two researchers deciding which screams are similar), rather than quantitative (directly measuring acoustic parameters to determine which are similar), approach towards determining similarity between screams. I think the manuscript would greatly benefit from a justification and cited precedent for the methods used here, or else a more formal acoustic analysis.
Validity of the findings: The primary findings regarding discrimination of screams are convincing and appropriately analysed. The authors' conclusions regarding this are grounded and well-justified.

Regarding the more tertiary analyses (response latency, the questionnaire and gender effects) the manuscript is considerably weaker, largely owing to the fact that the Discussion is currently quite lightweight. It could be strengthened by elaboration on the broader implications of individual findings, placing them within the context of the broader literature. The authors performed quite a thorough analysis of many factors, but many of the findings are glossed over, particularly with regards to the questionnaire data. For example, analysis of the Empathy Quotient is not mentioned in the Discussion at all, despite the lack of association with accurately discriminating screams contrasting somewhat with prior research mentioned in the Introduction. In general, if a variable was worthy of analysis then it should also be worthy of discussion even if it did not yield statistical significance.

In general, the questionnaire portion of the study feels somewhat extraneous, largely owing to the fact that discussion of the implications of both positive and negative findings relating to it are scarce. For example, the authors report that increased exposure to video-games was associated with accuracy, but then quickly write it off as likely being a consequence of the fact that gamers have experience of responding rapidly to computerised stimuli. If even positive results on items like this are of no significance to the underlying research question, then it is unclear why they were included in the first place.

Furthermore, the rational for examining gender effects is raised in the Introduction, but the findings on this (male voices are classified with greater accuracy, but female voices more quickly) are not discussed within the context of this literature. On this note, the argument regarding speed/accuracy trade-off with regards to male and female vocalisers is not very clearly expressed. I am not sure what the authors mean by males being easier to accurately identify due to but females being more ‘perceptually salient’, or why this would result in the trade-off mentioned.

I have recommendations for several aspects of the Results section:

Response latencies were calculated, but only from correct trials. If the authors have a good rational for this then it is not apparent in the text. Comparing latencies between correct and incorrect answers may shed further light on the ‘speed/accuracy trade-off’ discussed later in the paper.

In lines 343-344 the authors report whether the outcome of their analysis on gender effects is different if premature responses (given before the onset of the second stimulus) were included in the dataset. It is unclear why was done, since these responses cannot possibly provide any information on scream recognition. My preference would be to simply report what proportion of responses were given prematurely and throw this data out.

Finally, I recommend the use of boxplots (or similar) rather than bar-charts for all figures as they are much more effective at presenting the distribution of responses in a dataset.
Additional comments: Below are a number of minor comments and suggestions which I would also recommend the authors address but are not critical.

Line 78: remove the words ’serve to’ so that it simply reads ‘elicit’. I am also not sure this matches definitions of altruism within literature on the topic – helping behaviour/assistance could be more appropriate?

Line 131: What is an ‘inherently stable vocalisation’?

Line 188: I do not understand why the gap is ‘roughly’ 2000ms. Surely this would be under precise control when constructing the stimuli? If there is a range of values for some reason, the authors should clarify the reason and provide the range and average gap.

Throughout the Methods and Results, where a t-test or similar is used, the text should specify whether it was one- or two-tailed.

Lines 293-294: I’m not sure that this is best practice. The purpose of inter-observer reliability is surely to check for independent agreement between two observers; if they then set about with the aim of reaching absolute agreement on each item then this undermines that goal. This could be made more transparent by reporting how many screams were categorised in this fashion.

Line 420: ‘consistent main effect’ is not very clear phrasing. I assume the authors mean that there was no significant effect.

Line 322: This should specify again that only correct trials were examined

Line 324: This should specify the alpha-level after bonferonni correction

347-348: Statistical outputs should be included for the final claim in this paragraph.

Line 351: Throughout the manuscript, the authors should replace instances where ‘better’ performance is referred to with something more specific (‘more accurate’, etc). It is currently not clear until halfway through this paragraph whether the opening sentences refers to accuracy or latency.

Line 357-358: here a ‘small effect’ is referred to but no effect size is given. A marginally significant p value is not the same thing as a small effect.

387-388: The phrase ‘approaching statistical significance’ should always be avoided as it is statistically nonsensical, particularly when the value is as distant from the alpha-level as 0.097

Line 399: ‘permit’ is an unusual word choice here, as though screams themselves rather than listeners are the agents in this sentence. This also applies to the title of the manuscript.

Line 401: As discussed in a prior comment, replace phrases like ‘performed well’ throughout the manuscript with a specific outcome.

Line 435: Did measures of confidence also correlate with response latency?

Line 439-440: The fact that F2 was no longer significant when Same-A was included suggests a ceiling effect in this condition (which we can see in figure 1).


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DO HUMAN SCREAMS PERMIT INDIVIDUAL RECOGNITION?
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have addressed most of my concerns to my satisfaction - thank you!

I would only add that given that all 3 reviewers seemed to agree that the acoustic analysis is somewhat unconventional, doing at least a basic analysis of F0 and - if possible - formant frequencies would benefit the paper as other readers will probably have similar questions/concerns to the current set of reviewers. This type analysis seems to be no more fleshed-out than the original one and it would just be an alternative (that could be put into supplementary materials) to the originally proposed analysis.

However, the authors have also argued in their rebuttal letter that the inclusion of acoustic analysis was always a post-hoc decision and they note that any analysis is likely to be underpowered. This then speaks against conducting any acoustic analyses as underpowered analyses are unlikely to be informative.

Overall, I would encourage the authors to more clearly note their reservations about a lack of power to explain the null findings for the existing acoustic analyses. I'll leave the decision whether to request the inclusion of a more traditional acoustic analysis to strengthen their paper to the editor.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DO HUMAN SCREAMS PERMIT INDIVIDUAL RECOGNITION?
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have done an excellent job revising the paper and addressing the comments and concerns of the Editor and all three reviewers, I applaud their effort and believe that the end product is a much more transparent and replicable piece of research. Below I enumerate my remaining concerns regarding stimulus pair creation and acoustic analysis.
Experimental design: I thank the authors for now uploading the questionnaire and all vocal stimuli as supplementary materials. However listening to these stimuli has raised a few additional concerns.

First, it was not evident from the Methods section or Table 1 that some of the screams are ‘re-used’ in more than one stimulus pair. For example, Stimulus pairs ‘Different Vocalizer 2’ and ‘Different Vocalizer 3’ contain the exact same first scream, followed by a different second scream. Listeners could have used this information (I’ve heard this scream before) when judging whether two screams in a pair are likely to have been produced by the same Vocalizer.

In the Methods and in Table 1, where currently the authors provide only ‘stimulus pair gender breakdown’, it should be made clear how many different ‘Vocalizers’ were included in the stimulus pairs and how many of the screams were re-used across pairs. This should be notes as a potential confound.

Second, listeners could have used vocal cues to age, and to a lesser extent scream context, to judge whether screams were produced by the same vocalizer. Vocalisers in ‘Different Vocalizer’ pairs were matched for “gender, relative age (child or adult), and apparent emotional context” (L 210). However the authors do not provide any additional information about the age ranges of vocalizers. In theory, “adult” could include ages 18 to 100. Even if the age difference between two vocalizer’s in a ‘Different Vocalizer’ pair was relatively smaller than this (e.g., 20 years), it is possible that listeners could still pick up on this age difference to inform their judgment. To my knowledge there is no evidence (yet) that listeners can judge rough age from screams, but it’s probable that they can, and this too should be flagged as a possible confound in the judgment task.

Similarly I worry that context (pain, fear, excitement) could have aided listeners in their judgment.  While the authors note that screams in ‘Same Vocalizer’ stimulus pairs were either taken from “the same scream bout, or different screams from entirely separate bouts and eliciting contexts” (L 208), it seems likely that screams from the same individual would be taken from the same context more often than would screams from two different individuals.

Minor edits:

The authors indicated that, due to a coding error, two stimulus pairs were identical, i.e., contained the exact same first and second screams (L215). These pairs should be identified (and labelled) in the supplementary audio files.

Please indicate the degree of stretching (% from original) in the Duration Modified stimulus pairs (L 200).

In Table 1, the “Stimulus Type” category names still need to be revised (Same-A = Same Vocalizer, etc).
Validity of the findings: All three reviewers suggested that the authors provide additional descriptions and justifications for their acoustic analysis. As I noted in my original review, my biggest concern was the omission of key acoustic variables, namely F0, formants, and nonlinear phenomena (e.g., deterministic chaos) that are known to vary between individuals and to influence listeners’ voice-based judgments of a variety of speaker traits including identity, sex, age, body size, emotional and motivation states, etc. Formant frequencies are a key cue to identity in humans, as in other mammals, and F0 too appears to vary systematically between individuals, even in their nonverbal vocalisations (e.g., babies’ cries).

Omitting F0 and formants can be misleading. Based on a large amount of previous literature and strong theory-driven predictions, it is highly likely that these omitted acoustic parameters influenced (and thus would have predicted) listeners’ judgments, whereas the lesser-justified acoustic features that the authors chose to examine (bifurcations and harmonic regime) did not.

My recommendation is to either perform a comprehensive theory-driven acoustic analysis, or to remove acoustic analysis from the paper altogether. I appreciate that the authors’ main (and as they note, only) initial goal of the study was to test whether listeners can discriminate identity from screams. Their exploratory acoustic analysis was post-hoc. Perhaps this is all the more reason to remove the acoustic analysis from the paper altogether?

Identifying acoustic cues to identity in nonverbal vocalisations is clearly an important avenue for future work. Once the acoustic correlates of listeners’ judgments are identified, resynthesis techniques can be used to manipulate these acoustic parameters to test their direct, independent or interactive effects on listeners’ judgments and accuracy scores.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DO HUMAN SCREAMS PERMIT INDIVIDUAL RECOGNITION?
Review round: 2
Reviewer: 3

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors have substantially revised this manuscript in line with the suggestions from the reviewers and editor, resulting in a superior manuscript. In particular, I find that the additions and changes to the Introduction and Discussion have resulted in greatly improved narrative clarity, appropriately situating this work within the broader literature and providing a more thorough consideration of the outcomes of this analysis. The Analysis + Results sections are also considerably more transparent than in the previous version.

I am satisfied with the response to each of the comments provided in my original review and have no further suggestions.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ISOLATION AND IDENTIFICATION OF A HALOPHILIC AND ALKALIPHILIC MICROALGAL STRAIN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors in the submitted manuscript titled “Isolation and identification of a halophilic and alkaliphilic microalgal strain” presents information about identification of a microalgal strain JB19 isolated from the saline–alkaline soil of Songnen Plain of Northeast China. Isolation and identification of this train I believe will be of considerable interest to researchers in the field of microbiology. I have highlighted some of the issues with the article below. Addressing these issues would significantly improve the quality of the article.
1.	Line 158-163: It is customary to mention the figures in the text sequentially as it appears. As such, I suggest that this section is modified so that the figures are mentioned in correct sequence. Observations to Fig 4A should be mentioned first, followed by 4B and then 4C.
2.	Line 144-153: Figure 3B is not mentioned in the text. It should be mentioned next to the results discussed in this section. Also, the figures should be mentioned in the correct sequence, figure 3A followed by 3B then 3C and so on.
3.	Line 168-169: the two sentences should be rewritten to convey the message clearly to readers.
Experimental design: 1.	Lines 101-102: it is not clear what the authors meant by “DNA recovery to BGI to sequence were performed”. Please explain clearly in the text.
2.	Line 75: Please mention the total magnification used for the observation instead of the objective lens magnifications only.
3.	Line 89: Please mention the method used to ground the algal cells for e.g. by mortar pestle etc.
Validity of the findings: 1.	Line 176-177: “Thus, a large amount of glycerol is produced…”. I do not think that data presented can definitely conclude this statement. If it is a speculation, then it should be clearly mentioned. On other hand, if it is known from previously published work then it should be clearly referenced and cited.
2.	Figure 3: Please mention the concentration units in the x-axis of the bar graphs
3.	Figure 4: in the figure legend “NaHCO 3” should be “NaHCO3”
4.	The raw data for figures 3C-3D and S2 should be provided in an easily accessible excel or pdf file (or other appropriate format) which could be accessed by readers more easily.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ISOLATION AND IDENTIFICATION OF A HALOPHILIC AND ALKALIPHILIC MICROALGAL STRAIN
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript entitled "Isolation and identification of a halophilic and
alkaliphilic microalgal strain" by Chenxi Liu et al. identified a new halophilic and alkaliphilic microalgal strain JB19 strain from the saline–alkaline soil of Northeast China.

I have found many issues with this manuscript thus I do not recommend it for publication in its present form.

The English of the manuscript is poor. Sentences and informal and spoken language has been used. Authors are required to rewrite the manuscript in formal scientific language. There are dozens of spaces are missing especially in figure legend and references, also many times it is not easy to find out the meaning of the sentences. I would suggest seeking help of an academic expert with good language skills.

Introduction, results, and discussion sections are poorly written. Due to this, the major impact of this manuscript is hidden.

Major concern: In the earlier publication, Qiao et al. (2015) identified the algal strain JB19. They performed the 18S rRNA gene sequence of this strain, did evaluate the phylogeny, but didn’t characterize further without any explanation. However, in the current manuscript Chenxi Liu et al. performed the same line of experiment, as done by Qiao et al. (2015) for other strain, and checked the salt and alkali tolerance of this strain. So, the isolation of this strain was not performed by Chenxi Liu et al. and hence should be removed from the title of this manuscript.

In the earlier report of Qiao et al. (2015), this strain JB19 group together with Chlorococcum sp and not with Nannochloris sp. But in current manuscript JB19 aligns along Nannochloris sp. can author explain this discrepancy??
Experimental design: Experimental design is repetitive but as per the field and satisfactory, however the manuscript is poorly written, due to this the major impact of this manuscript is hidden. There are certain experiments needed that I had mentioned in general comments for the authors.
Validity of the findings: The manuscript entitled "Isolation and identification of a halophilic and
alkaliphilic microalgal strain" by Chenxi Liu et al. claim to identify a new halophilic and alkaliphilic microalgal strain JB19 from the saline–alkaline soil of Northeast China.
The strain was isolated and phyletic history was determined earlier, which is different in current report.
Additional comments: Line 21-23: Rewrite the sentence. “Morphological observation revealed that JB19 has a simple cellular structure; it is unicellular and spheric with a diameter of 4–6 μm and a cell wall thickness of 0.22 μm and contains two chloroplasts and one nucleus.”

Line 24: “constructed by 18S sequence homologous comparison” should be “constructed by 18S sequence homology”.

Line 41: References are not up to date. Need more recent references.
Irregular spacing in the references throughout the manuscript.

Line 45-46: “salt lakes, and north and south poles” to “salt lakes, and polar region”

Line 53-54: ‘we isolated and” to “we had isolated”

Line 55-56: “The microalga was subjected to morphological observation, molecular level identification, and halophilic (NaCl, NaHCO3) characteristic analysis.” Verb repletion in this sentence.
Can be rewritten as- “The isolated microalga was subjected to morphological, molecular and halophilic (NaCl, NaHCO3) characterization.”

Line 59: subheading “1.1 Materials” is not appropriate for this section. Here you have described a full methodology.

Line 62: “A loop of algae was taken with an inoculating loop and then streaked” to “A loop of algae was streaked”

Line 62-64: “When the algal colonies grew, the algae were again streaked until single colonies appeared on the plate upon microscopic examination.”
Authors are required to use the formal scientific language throughout the manuscript.

Line 74: “detected” to visualized

Line 76: “cells was” to “cells were”

Line 77: “Transmission electron microscopy slice-making and observation”
Change the subheading. “Slice –making” is not an appropriate word instead use “thin sectioning”.

Line 78: “and 3% glutaraldehyde fixed liquid” what does this mean?? Liquid was fixed by GA??
Line 86: “1.2.3 Systematic evolution of microalga JB19”. What is the meaning of systematic evolution here in method section???

Line 89: “ground” to “grounded”

Line 90: “bathed” to “incubated in bathtub”

Line 91: “the cells were” it is no longer an intact cells, it has turned into lysate.

Line 92: “supernatant fluid was” to “supernatant was”

Line 98: The sentence is unclear and like that many sentences further in Material and Metods section are ambigious, unclear and grammatically incorrect like: “The primers were universal to eukaryotic algae: 18SF: 5′ AACCTGGTTGATCCTGCCAGT-3′ and 18SR:5′-TTGATCCTTCTGCAGGTTCACC-3′ (Katana et al.,2001).

Line 101-102: “to BGI to sequence.” To to BGI was performed. Also explain BGI.

Line 102-106: “Homology comparison was carried out on NCBI (http://blast.ncbi.nlm.nih.gov/Blast.cgi). With the software ClustalX(1.8), 18S rRNA of the microalgae was sequenced, and its relative genetic distance was calculated with MEGA5.0 software. A phylogenetic tree was constructed with the maximum likelihood method (UPGMA), and bootstrap analyses (1000 replications) were performed to test the molecular phylogenetic tree.”
Very poor sentence structure, please rewrite the whole paragraph.

Line 109: “NaCl and NaHCO3 solution was added” to “NaCl and NaHCO3 solutions were added.”

Line 109-111: “The final concentrations of NaCl were successively 0, 100, 200, 400, 600, 800, and 1000 mmol/L, whereas those of NaHCO3 were 0, 50, 100, 200, 300, 400, and 500 mmol/L.” for what??

Line 111-113: After mixing, the solution was cultured at 25 ℃ in light/dark (16h/8h) condition, shook several times every day, and observed after 14 h. The value of ODλ=700 was measured by a spectrophotometer.
Authors are advised to use formal scientific writing pattern

Line 114: 1.2.5 Influence of saline environment on microalgal cellular ultrastructure.
Subheading is inappropriate for method section. It can be used for result subheading.

Line 132: 2.2 Construction of microalgal JB19 phylogenetic tree
Subheading is inappropriate for result section. The result section subheading should be focused on outcome. It should not be “construction of phylogenetic tree”, rather than “what you got know from that tree!”

Line 133: The 18S rDNA of JB19 was obtained by sequencing the PCR products purified by electrophoresis by using universal primers.
What does that mean? PCR product was purified by electrophoresis?? It is PCR product was separated by electrophoresis and desired band was gel eluted. Again; primer was used to amplify target sequence by PCR and not to purify PCR product by gel electrophoresis.

Line 136: “similarity to Nannochloris sp. BLD-15, with only four base substitutions,” Did author checked the sequencing chromatogram for these four base substitution? A comparison of BLD15 and JB19 chromatogram for the mismatch region is required in main figure.

Line 139-140: Thus, microalga JB19 was initially identified to be the physiological race of the genus Nannochloris.
Is author mean to say that prior to their work, it was already known that this new strain JB19 was of genus Nannochloris. It is important point and author should make it clear at the very beginning of introduction.

Line 142: 2.3 Growth characteristics of the salt and alkaline tolerance of microalga JB19.
The subheading is repeatitive as also in 2.3.1. It may be changed to “salt and alkaline tolerance of microalga JB19”.
Then for follow up subheading: 2.3.1 would be Growth pattern of microalga JB19 in NaCl and NaHCO3 treatments, and
2.3.2. Morphological changes of microalga JB19 under NaCl and NaHCO3 treatments

Line 144: Microalgal JB19 cells in the same growth state were phenotypically observed under resistance to NaHCO3 (Figure 3-A).
What do you mean by this sentence???

Line 145-146: The green color of the algal cells darkened as the NaHCO3 concentration in the medium increased, indicating that cell growth significantly accelerated??
To validate this statement, authors are required to monitor the chlorophyll absorbance as they measured the cell density increase and with respect to NaHCO3 concentration and present the data in bar or line graph.

Line 151: “Phenotype” to “phenotypic”

Line 152-153: The growth rate of the microalga reached the maximum (Figure 3-D) and the cells of JB19 still survived under the treatment of 1 M NaCl.
What is the meaning of this sentence? After growth reached maximum, then cells were put on salt treatment??

Line 156:  2.3.2 Characteristics of the cellular structure of microalga JB19 under NaCl and NaHCO3 treatments.

Line 159: “We detected microalgal cells under 400 mmol/L NaHCO3” to “We analyzed microalgal cells at the concentration of 400 mmol/L NaHCO3”.

Line 160: “Results showed a great number of starch grains” to “Images shows the high accumulation of starch granules”

Discussion needs to be rewritten. Discussion should include the outcome and importance of figures and finding??
In figure um and not uM. Figure legends need to be re-written, with more details. Also author can use of arrow or other symbol to highlight the things they want to explain in figure.

Figure 3 C and D: mention what is on the x and y axis with unit. Also why C and D written in bold red??
In figure 4: please explain in legend about the figure and observation, provide statistical data of how many of these cells showed the morphological changes and granule accumulation?


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ISOLATION AND IDENTIFICATION OF A HALOPHILIC AND ALKALIPHILIC MICROALGAL STRAIN
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors have addressed all the criticisms
Experimental design: Authors have addressed all the issues which were raised with respect to experimental design
Validity of the findings: Authors have addressed all the criticisms about study
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ISOLATION AND IDENTIFICATION OF A HALOPHILIC AND ALKALIPHILIC MICROALGAL STRAIN
Review round: 2
Reviewer: 2

Output:
Basic reporting: Manuscript has significantly improved after revision but still need minor corrections before acceptance. Rebuttal letter is poorly written and hard to follow. Author should also mention the changes made in manuscript in their "response to reviewer".
Experimental design: Satisfactory.
Validity of the findings: Satisfactory
Additional comments: "The microalgae JB19 in this paper is now changed to microalgae SAE1. The SAE1 strain was re-isolated from the saline-alkali soil in Northeast China and identified a new halophilic alkalophilic microalgae belonging to Nannochloris sp."

Author's explanation is not satisfactory in the above sentence! Still, it is not clear that the JB19 strain from earlier work "Qiao et al. (2015)" is the same strain here? What is the rationale behind changing the name of strain if it is same as mentioned earlier? Please clearly mention in text about what and how SAE1 is different from previous JB19 isolates/ or if it is same?


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ISOLATION AND IDENTIFICATION OF A HALOPHILIC AND ALKALIPHILIC MICROALGAL STRAIN
Review round: 3
Reviewer: 1

Output:
Basic reporting: The manuscript entitled "Isolation and identification of a halophilic and
alkaliphilic microalgal strain" by Chenxi Liu et al. has improved after revision. There are minor corrections suggested below after which it is acceptable for publication.

Line 46: polar region.(Brock,1975;Carson and Brown,1978;Rayburn,Mack & Metting,1982;Hu et
Check punctuation and space.

Line 101: BGI(Beijing Genomics Institute, China)

Space missing before bracket, check this type of typos in the manuscript.

Did not need to attach English language certificate in manuscript.
Experimental design: Explained earlier.
Validity of the findings: Explained earlier.
Additional comments: Accepted after minor revision.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DECOUPLED RECOVERY OF ECOLOGICAL COMMUNITIES AFTER RECLAMATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript reports on plant, soil, and nematode responses to reclaimed rangelands. The manuscript is well written and follows appropriate formatting guidelines. The manuscript has sufficient background and represents a self-contained unit of publication. This manuscript should be of interest to the broad readership of PeerJ.
Experimental design: The design seems appropriate. However, there are a few points that need clarification.

Lines 205-206: Please also state if type III sum of squares was used (this is the default). This seems most appropriate for your design.

Line 207: By “sampling location” do you mean reclaimed/remnant prairie? Using the terms location and site in the same model description could be confusing.

Lines 207: After you performed the mixed-models analysis, was the model homoscedastic? Or were there changes in the spread of residuals? You should confirm the Pearson residuals are not changing in their spread using plot(model). This is a more important assumption than normality.

Line 212: This is confusing. I think you meant to say post-hoc multiple comparisons using the Holm method were performed. The Tukey test is another multiple comparison method.
Validity of the findings: The findings in this manuscript seem valid.
Additional comments: Line 25: Should there be keywords after the abstract?

Line 54-55: Might the slow recovery be due to dispersal limitations? How might the soil microstructure and plant community influence dispersal?

Line 167: I think Table S1 should be part of the main manuscript, not a supplemental table. It could be combined with Table 2. Also a measure of soil moisture (such as gravimetric water content) should be reported with soil compaction test.

Line 215: Why not put the continuous predictors in the same model as the categorical predictor?

Line 229: Make the NMDS and PERMANOVA a new paragraph. Consider performing a PERMDISP as well. It seems the two groups in Fig. 3 are overlapping (perhaps a spurious PERMANOVA result because of differences in dispersion of the two groups).

Fig. 3: Add a legend for the two groups.

Line 356: Remove the comma between adjacent and intact

Line 435: Reorder the sentence so that the author is not the subject of the sentence.

Lines 443-446: This is interesting that the plant presence rather than plant identity could be important for nematodes in your study areas. Perhaps you could expand a bit more. This could be because there is little variation in plant species present. If there is considerable variation in plant species, then perhaps many nematode groups can respond to a wide variety compounds deposited in the rhizosphere.

Lines 482-483: Below is a reference that might be useful here that supports repeated seeding can increase plant richness

Wilsey B, Stirling G (2007) Species richness and evenness respond in a different manner to propagule density in developing prairie microcosm communities. Plant Ecol 190:259–273


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DECOUPLED RECOVERY OF ECOLOGICAL COMMUNITIES AFTER RECLAMATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: Writing is clear and English correct. Literature citations are appropriate and sufficient. Article structure is good, figures and tables professionally done.

There are some changes that could clarify the captions and interpretation of the Figures and Tables:
Tables 1-3: The caption could include a reminder that sampling location is the main fixed effect and clarify what a significant response means in this analysis.

Fig. 3: I might suggest a legend rather than just explaining in the caption, but totally up to the authors.

Fig. 5: I would suggest pointing out the difference in scale between the panels here. I see why it is the way it is, but it’s also worth pointing out that the omnicarnivores are an order of magnitude lower than total abundance (gives a sense of their contribution to the overall community).

The Raw data are currently included as supplemental material. I would encourage the authors to consider a public database like Dryad to share the data. I also could find no link to the R code for the statistical analysis, although the is mentioned in the supplemental material.

Results all addressed specified hypotheses and were synthesized into an informative SEM model. The synthesized SEM also provides a compelling case for including 5 hypotheses in the manuscript, which could be overwhelming without a concrete synthesis.
Experimental design: This is an original data manuscript and fits well within the Aims & Scope of the journal.

The research questions are well-defined and addressed appropriately. This work does address a gap in scientific knowledge, as very little work in restoration ecology has synthesized above- and belowground communities across multiple trophic levels. The work on reclaimed well heads in the Brakken oil field is also an important contribution to address the future of well-heads as they are retired in this region. The importance of considering soil invertebrates like Nematodes, which uniquely span multiple trophic levels could be articulated even more in the manuscript.

The investigation was rigorous, using respected approaches to sampling and analysis. I found no ethical concerns.

Some additional information could be included to clarify the experimental design in the Methods.
i.	I strongly recommend a table, even if supplemental the showed site, age class, and more clearly represented what was considered “undisturbed prairie” (e.g. the transect 100m from the reclaim, both the 50 and 100?) Not all readers will realize the reclaimed well heads are surrounded by undisturbed prairie, and that the transects moving away from the reclaimed area are representing undisturbed prairie. This would help tremendously with clarifying the fixed effects categories and degrees of freedom reported with the ANOVA statistics. For example, I was unsure where the degree of freedom of 26, reported in Tables 1-3 is coming from. I understand the 2 (reclaim/50m/150m distinction), but total N=42. Were only 2 of the 3 transects included in the ANOVA (28-2=26)? Please clarify if I’m missing something.
ii.     Building from (i), it is challenging to understand how the sites are distributed across the 33 year consequence. This adds confusion when the location*time interaction is discussed (lines 98-100, 2017-220, 264-269, 387-389, 440-441). Consider how including a table of the sites or changes to the text might clarify these sections.
iii.	Site was used as a random factor, and that is fine. Was there any consideration of using time as a random factor, to account for potential changes over time in the ANOVA model?
Validity of the findings: As mentioned above, this work addresses a clear knowledge gap and the findings provide important context for not only understanding how soil and plant communities recovery in reclaimed oil and gas drill sites. The paper builds the ecological knowledge gap first, and it might be helpful to identify what is meant by "well" earlier in the text, even in the abstract, as not all readers will jump to the understanding that this means natural gas or oil well.

The data are robust and controlled. The data are statistically sounds, although some clarification in description and reporting of the statistics would improve the manuscript.

The conclusion evaluates the hypotheses and stays well within the frame of inference from the data.

I have no concerns about speculation arising from the data.
Additional comments: Overall, very nice paper. As mentioned above, there are some changes that could be made to clarify the experimental design, particularly the time aspect. In addition, clarifying that wells and reclaims refer to gas and oil wells might be helpful in the abstract and early in the Introduction, just to help out readers, particularly international readers, unfamiliar with what is meant by energy development in the Great Plains.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DECOUPLED RECOVERY OF ECOLOGICAL COMMUNITIES AFTER RECLAMATION
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This study examines plant and soil community response to disturbance associated with oil extraction in the Bakken oil fields of western North Dakota. Adding the soil community analysis is the novel element in this project. Therefore I focused on Hypothesis 4 and 5. Hypothesis 4 predicts that the nematode community recovery on reclaimed sites would be linked to soil factors and plant community. This is a reasonable prediction since there is an increasing amount of information that microbial feeding nematodes respond positively to plant biomass. Plant feeders have been shown to respond positively to plant diversity and presumably resource quality reflected by C/N ratios. (Cortois et al, 2017; Cesarz et al, 2017). Hypothesis 5 predicts that the nematode community would lag behind that of plant communities due to slower dispersal. This prediction, I believe is probably contingent on geographic scale. Certainly, plant feeding specialists are dependent on the presence of their hosts. But some species of plant-feeding grassland nematodes have broader host-ranges, feeding on a number of native and possibly introduced grass species. A number of the plant-feeding genera, e.g. Paratylenchus, Helicotylenchus, ,and Quinisulcius all members of the mixed-grass prairie community, appear to go in and out of an anhydrobiotic state rapidly, and probably are dispersed by wind-blown soil in dry conditions or in surface water during heavy rains. Many microbivores have phoretic associations with insects. Nonetheless, both hypotheses are testable. Basically the results did not support a specific linkage nor a time lag in the relationship between nematode communities and soil conditions or plant communities. While the authors can speculate about possible fewer qualitative requirements in northern prairie nematode communities, I think they are closer to the answer in the paragraph starting on line 450. The trophic group analysis is a very coarse measure of nematode community structure. Since the analyses were probably made at the family or superfamily taxonomic level, the reclaimed  and rangeland soil nematode communities could differ considerably in taxonomic composition. The limitations of the trophic group analysis, which has been a standard form of ecological analysis for years, is a compromise due to the time-consuming taxonomic analysis necessary to get a more refined understanding of nematode community structure. The authors point out this trade-off. However, one concern I have that is not addressed by the authors, is the method of nematode extraction. Many ecologists persist in conducting Baermann funnel nematode extractions when it is well known that funnel extraction bias nematode recovery in favor of fast moving, active nematodes. Several prominent groups of plant feeding nematodes known to be abundant in grasslands will be underrepresented in funnel extractions. Obviously it will bias reference and disturbed sites equally, but the resulting trophic group comparisons with other studies is skewed. Overall I think the study with regards to the plant community and soil conditions is probably solid, the verdict on the nematode communities is still an open question. Greater taxonomic resolution, either by higher resolution microscopic analysis or molecular approaches are probably necessary to resolve the issue.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DECOUPLED RECOVERY OF ECOLOGICAL COMMUNITIES AFTER RECLAMATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors have addressed all my concerns about the manuscript.

I have one minor editorial note: on line 142 the sites can be referred to as reclaims because the abbreviation was indicated earlier in the methods.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DECOUPLED RECOVERY OF ECOLOGICAL COMMUNITIES AFTER RECLAMATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: Lingering revisions:
•	Table captions: The authors state that they made changes to the text to specify the fixed effect in Tables 1-3 and clarify what the response meant, but it seems the caption text is identical to the original manuscript.
•	Figure 5: Authors state that a change was made to the legend to highlight the scale difference in panel A and B; however, I do not see a legend at all on this figure.
Experimental design: No further clarifying explanation required.
Validity of the findings: No further revisions necessary.
Additional comments: Dear Sylvan et al.,
I have reviewed the revision of “Decoupled recovery of ecological communities after reclamation” submitted to PeerJ (peerj-30920-v1). Overall, I find that you have made careful and thoughtful revisions. I noted two places where your response indicated changes had been made, but I failed to find them in the revised manuscript:
•	Table captions: The authors state that they made changes to the text to specify the fixed effect in Tables 1-3 and clarify what the response meant, but it seems the caption text is identical to the original manuscript.
•	Figure 5: Authors state that a change was made to the legend to highlight the scale difference in panel A and B; however, I do not see a legend at all on this figure.

Perhaps the wrong files were incorrectly uploaded during the revision submission process? It seems the concerns were addressed, I just could not find the changes. Thank you for your time and effort on this manuscript.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DESCRIPTION AND CLASSIFICATION OF BIVALVE MOLLUSKS HEMOCYTES: A COMPUTATIONAL APPROACH
Review round: 1
Reviewer: 1

Output:
Basic reporting: Subject is important. Taking into account geometrical complexity of objects, methods of fractal geometry are appropriate.
Experimental design: Experimental methods are adequate.
Validity of the findings: Three morphological cell types, obtained by cluster analysis methods, from a biological point of view look very reasonable.
Additional comments: However the statistical analysis is quite weak.

The results of the factor analysis are not presented either in the tables or in the graphs; a verbal description is not enough.

An attempt to statistically justify the results of cluster analysis contains a vicious circle – it is based on the same data as cluster analysis. It’s mistakenly to compute significance by such a way. If we take a random data set and apply the cluster analysis, it will always break the set of objects into some groups. If we apply discriminant analysis namely to these groups using the same traits, DA will always show significant differences.

A possible way out of this situation would be bootstrap analysis, but in general for cluster analysis these methods have not yet been developed. Therefore, it is necessary to confirm the results obtained by means of biological and geometrical arguments.

Concrete remarks:

Annotation, 18, 106. “dimensional characteristics (area, perimeter)”.
In physics and mathematics, the dimension of a mathematical space (or object) is informally defined as the minimum number of coordinates needed to specify any point within it (Wikipedia). It isn’t size. Fractal dimension is a fractional number.

66 – 68. All ratios are not linear, but dimensionless parameters.

71. “were normalized …” specify, please. There are several variants of normalization with equal contributions to clustering.
80  «… Euclidean distance as a measure of proximity». Euclidean distance isn’t a measure of proximity, but  is a measure of dissimilarity.

116 “… dropped below 3”. What is the measure of explained variation? Eigenvalues or percents?

135 – 137 “When more than two populations are compared, the F-test is calculated as the external variance to internal variance ratio, determining the difference between variances of the selected clusters.”
This is not true. No variances of clusters are compared. But the inter-sample variance of the all cluster centroids is compared with the combined in all clusters intra-sampling variance.

P-values aren't provided in tables 3, 4. The tables are symmetric, p-values can be placed below or above the diagonal.

The cell types shown in Fig. 2 aren't reflected in Fig. 1.

Conclusion. Article should be remade.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DESCRIPTION AND CLASSIFICATION OF BIVALVE MOLLUSKS HEMOCYTES: A COMPUTATIONAL APPROACH
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript entitled “Description and classification of bivalve mollusks hemocytes:a computational approach” submitted by the authors Y. A. Karetin, A. A. Kalitnik,  A. E. Safonova and E. Cicinskas aims to describe the hemocyte populations from bivalves, Spisula sachalinensis and Callista brevisiphonata by a new method for identification.
The manuscript is generally well-written and organized; however there are several general concerns, which, in my opinion, do not allow publishing it.
Experimental design: 1.	In Introduction the authors did not provide available information about types of hemocytes of the species studied. If there are no such data for these bivalves it should be stated.
2.	The analysis is carried out on 458 hemocytes of Spisula sachalinensis and 628 hemocytes of Callista brevisiphonata. Is this number of cells sufficient for statistics and further morphometric measurements? According to the Table 1 the SE for some cells characteristics is more than ½ of the mean value (see the values of Area, Per, 1/2half, in50/out50, LCFD PreLac for Spisula sachalinensis and 1/2half for Callista brevisiphonata). Moreover, some of these parameters were used for the further characterization of hemocytes. This means, that determination of cell types, which are hardly distinguished due to their similarity and occurrence of transitional forms, is based on the parameters with great variability. May be authors should provide data confirming the significance of the differences in the characteristics chosen between types of hemocytes for each species.
Validity of the findings: In Discussion the authors do not provide any comparative analysis of the results obtained by the new approach and other methods used for hemocyte identification. Thus, it remains unclear, whether the new technique gives the adequate precise distinguishing of hemocytes. There are no citations of literature within the section, therefore, the reader does not have an opportunity to independently come to conclusion about the efficacy of the method. The authors should provide information, which agrees with the data, obtained by the new method and confirms its convenience of application.
References. The authors should substantially work with the literature. Among 12 citations only a half can be classified as “new” or “latest” works. The rest of references were published before 2008, more than 10 years ago. Most of the “new” citations belong to the author of the manuscript. Thus, for my opinion, the results of the research are insufficiently justified.
Additional comments: These are the reasons why to reject this publication as it stands. I recommend to resubmit a new MS with extra data linked to the evidence of the efficacy of the new approach.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WNT SIGNALING IN LIVER DISEASE: EMERGING TRENDS FROM A BIBLIOMETRIC PERSPECTIVE
Review round: 1
Reviewer: 1

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: I thank the editor for providing an opportunity to review the article “Wnt signaling in liver disease: emerging trends from a bibliometric perspective”.
Since this is not an original research article, it can be considered for “resource” or “prospective” group of publication.
The article is written well and can be considered for publication after addressing these comments:

1.	Why Wnt signaling was specifically chosen for bibliometric analysis? What was the motivation behind?
2.	Authors should include flow diagram for the Wnt signaling pathway, to give better prospective for readers.
3.	Figures should be merged, and the number should be reduced (there are figures for each point). Fig 1 should be about summary of past research and Fig 2 should be future prospective research topics.
4.	Take home message for this article is to give current trends and future prospects to Investigators about Wnt signaling. This point should be highlighted and included in the figure, rather than summarized in the table.
5.	For example, Fig 6 should be about what could be potential future research topics rather than what keyword used most frequently. Authors should include a figure to speculate future research topics and importance based on the bibliographic analysis. And also discuss why authors think that these suggested topics would be important to address in the future for Wnt signaling research.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WNT SIGNALING IN LIVER DISEASE: EMERGING TRENDS FROM A BIBLIOMETRIC PERSPECTIVE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript entitled Wnt signaling in liver disease: emerging trends from a bibliometrics perspective by Guangyi Jiang et al. summarized the advancements and emerging trends in Wnt signaling in liver diseases using bibliometrics methods. Although this is theoretical paper and this type of analysis had already been performed earlier and many in social science research yet it is new for biological science field and comprehensive overview for field development.
Experimental design: NOT APPLICABLE
Validity of the findings: Limited impact.
Additional comments: There are few major concern that I mentioned below:

In result section:
Line 108: The subheading is “Authors, institutions, and nations”. But the authors started the paragraph with manuscript numbers. There is no analysis on “author” been presented under this subheading. I would suggest that author need to work on result. Author should structure their result section in a systematic way. For example, author may consider the following subheadings to structure their result:

1 Publication outputs/Numbers
2 Country/Geographical distribution
3 Institution analysis
4 Research hotspots
5 Journal analysis/Landmark manuscript
6 Research areas/ subtopics
7 Author analysis
8 Research trends/Evolution of scientific ideas

Line 128: “3. Important subtopics” Important: is an adjective which may be refrained from using in subheading.

Figures:
Figure figure number are not matching. Figure 3 is Fig 2b. Author need to rewrite the all the figure legends.

Figure 1: The numbers on x and y axis are hardly visible. Author could write number on top of each year’s bar as well or may present by line diagram instead of bar.

Figure 2a/2b: The figure doesn’t represent the text in result section. In text, Line 114-116 author has mentioned the individual countries publication which is not apparent in figure. I would suggest all the countries with their publication in table form. In figure 2b “Peoples R China” can be written as “China” similar to USA for United State of America.

Figure 3a/4: Map can show the distribution of institute on globe, it’s hard to predict the institution., again table will work better than globe.

Figure 3b/5: It is hard to read institute name and correlate with map in figure. This data can be presented in simpler form like horizontal bar graph.

Figure 4a/6: I would suggest removing or change this figure with as nothing is clear in picture. Please elaborate the every detail of figure in its legend e.g. what does lines in figure signify, what are nodes and color of nodes signify?

Figure 4b and figure 5 is not clear at all. Texts in figures are unreadable, neither it is clear that which node or which part of the figure is highlighted by text.

Figure 6/9: In Foam tree, all the keyword has same area, which obscure the purpose of figure.

Remove language certificate from supplementary file.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WNT SIGNALING IN LIVER DISEASE: EMERGING TRENDS FROM A BIBLIOMETRIC PERSPECTIVE
Review round: 2
Reviewer: 1

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: Authors have included all suggestions and addressed all comments on the manuscript. This article can be accepted for publication.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WNT SIGNALING IN LIVER DISEASE: EMERGING TRENDS FROM A BIBLIOMETRIC PERSPECTIVE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript entitled Wnt signaling in liver disease: emerging trends from a bibliometric perspective by Guangyi Jiang et al. summarized the advancements and emerging trends in Wnt signaling in liver diseases using bibliometric methods.
Experimental design: Not Applicable
Validity of the findings: Not Applicable
Additional comments: Manuscript has improved significantly after revision.
Few minor concerns listed below:
Author should check the journal’s guideline to adjust the ‘Font size’ of the manuscript, especially in ‘Tables’. It is hard to visualize the text of tables.

Surprisingly ‘Acknowledgement’ is ‘Not Applicable’??!!


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: METABOLOMIC AND BIOCHEMICAL CHARACTERIZATION OF A NEW MODEL OF THE TRANSITION OF ACUTE KIDNEY INJURY TO CHRONIC KIDNEY DISEASE INDUCED BY FOLIC ACID
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In the present study, Marlene Marisol Perales-Quintana et al have tried to characterize and establish folic acid induced rat model of acute kidney injury (AKI) to chronic kidney disease (CKD) transition . The experimental design is good as they have looked into various inflammatory, kidney injury markers and metabolites related to CKD in serum and urine after inducing CKD with folic acid . However, some of the minor concerns are as below.

1) The group have just performed H and E staining for histology and mentioned about inflammatory infiltrate, it would be good if they could stain for specific macrophage infiltration (CD68) in the kidney tissues for assessing inflammation.
2) The group have looked into inflammatory and kidney injury markers in systemic circulation by measuring it in serum, but it would be good to look into some of the inflammatory, oxidative stress and kidney injury gene expression levels in the kidney tissue to relate it to kidney damage.
3) The authors should proofread the paper for minor grammatical errors and sentence formations.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: METABOLOMIC AND BIOCHEMICAL CHARACTERIZATION OF A NEW MODEL OF THE TRANSITION OF ACUTE KIDNEY INJURY TO CHRONIC KIDNEY DISEASE INDUCED BY FOLIC ACID
Review round: 1
Reviewer: 2

Output:
Basic reporting: See the general comments for the author.
Experimental design: See the general comments for the author.
Validity of the findings: See the general comments for the author.
Additional comments: In this work, the authors developed metabolomics approach to investigate the transition of acute kidney injury to chronic kidney disease induced by folic acid-induced renal injury model. Several suggestions are made as follows to improve the quality of the manuscript.
1.	Metabolomics approaches, such as UPLC-MS and HNMR, applied to AKI or CKD have been reported in the several excellent reviews such as Nat Rev Nephrol 2017,13(5),269-284; Nat Rev Nephrol 2011,8(1),22-33; Clin Chim Acta 2013,422,59-69; Adv Clin Chem 2015,68,153-175. Please summarize the metabolomics application in renal disease to improve manuscript quality.
2.	Folic acid-induced AKI-to-CKD transition should be compared and discussed with other models such as ischaemia–reperfusion injury (IRI), cisplatin induced nephrotoxicity or aristolochic acid nephrotoxicity reported by several studies such as Free Radic Biol Med. 2019,134,484-497; Sci Rep 2015,5,12936; Bioanalysis 2015,7(6),685–700; Redox Biol 2016,10,168-178; Adv Clin Chem 2014,65:69-89; Chem Biol Interact 2016,252,114-130.
3.	Chemicals and Reagents should be provided in this section. Please include both the manufacturer’s name and location (including city, state, and country) for specialized equipment and reagents throughout the manuscript.
4.	What method was used for identifying metabolites? The identification method of metabolites should be provided including available database.
5.	What method was used for normalizing metabolites in sample?
6.	Better describe the metabolomics data, how many were increased and how many decreased? This information is essential to enable the reader to determine the significance of the data presented for biomarkers.
7.	There is no scale bar on the histology slides in Figure 2.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: METABOLOMIC AND BIOCHEMICAL CHARACTERIZATION OF A NEW MODEL OF THE TRANSITION OF ACUTE KIDNEY INJURY TO CHRONIC KIDNEY DISEASE INDUCED BY FOLIC ACID
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have improved the manuscript, so I suggest the manuscript should be accepted for publication.
Experimental design: Experimental design is good.
Validity of the findings: Validity of the findings is good.
Additional comments: The authors have improved the manuscript, so I suggest the manuscript should be accepted for publication.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: A FUNCTIONAL MAGNETIC RESONANCE IMAGING INVESTIGATION OF THE AUTONOMOUS SENSORY MERIDIAN RESPONSE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The method and analyses are clear throughout. My only comment here is that the hypotheses could be more thoroughly explained. Specifically, why did the authors expect to see increased activity in sensorimotor regions for ASMR participants? Several brain regions are also mentioned that are expected to be correlated as these are associated with emotional responses – are these for emotional responses in general or emotional responses we’d expect to see triggered in ASMR?

It would also strengthen the paper if the authors explained more why an imaging approach is helpful i.e., what this approach would add that we can’t get from cognitive or questionnaire-based measures.
Experimental design: The study employed an experimental design with good controls.
Validity of the findings: The findings look to be well reported and well explained.
Additional comments: I appreciate the opportunity to review this paper. This manuscript reports a study examining the neural underpinnings of ASMR using fMRI. Seventeen ASMR participants were compared to matched controls whilst watching ASMR videos and control videos. The authors find greater activation in ASMR participants to ASMR videos in areas representing emotional responses and sensorimotor activity (compared to controls). The study had a good design and built on prior work that has been done in this area but with control participants, control videos and a slightly larger sample. This is an emerging and topical area of Psychology and I very much welcome research in this area. The researchers ask a good question and the manuscript is well-written and well-reported. Good avenues for future research are given, as well as interesting speculation about the role of these brain regions in ASMR.

Minor comments for clarity:

Introduction:
-The abstract gives a good summary of the results, however, in the last line it says: ‘Together, these results highlight the fact that ASMR involves an unusual integration of activity in brain areas related to sensation, emotion, and attention’ – could the authors find a clearer word other than ‘unusual’?
The sentence: ‘These “tingles” are often accompanied by a calming feeling that many individuals report as being emotionally positive’ needs a reference (perhaps Poerio et al ?).
-On commenting on the Smith et al., (2017) study, the authors mention their findings are consistent with other studies of atypical sensory experiences. Could the authors specifically name any examples here?
-When reporting on Poerio and colleagues – could the authors add that the increase in skin conductance responses (SCR) and a decrease in heart rate was only found in ASMR participants and not controls?
-When mentioning that ASMR could also be an arousing experience, could the authors word this as ‘physiologically arousing’ to avoid any links with sexual arousal as this has been a misconception in the media?
-‘…Questionnaire-based study of the curiosity component of mindfulness’ is not clear.

Discussion:
-The authors mention ASMR participants show more activity in the ‘paracentral lobule’ but do not explain this further. What is this region responsible for? More explanation for a non-expert in cognitive neuroscience would be helpful.
-The discussion of the role of the potential role of the thalamus was really interesting. The authors mention possible ‘atypical sensory integration’ – could the authors be more specific here about they suggest may be happening here?


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: A FUNCTIONAL MAGNETIC RESONANCE IMAGING INVESTIGATION OF THE AUTONOMOUS SENSORY MERIDIAN RESPONSE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is clearly written and easy to follow. Appropriate references are provided. Raw data is not shared. Instead the statistics of the voxels in the clusters that identified using a cluster threshold estimator are provided as supplementary material.

I have some suggestions that may help to improve the structure of the manuscript:

The authors may reconsider the order of paragraphs in the introduction. The second paragraph deals with resting-state fMRI, the third paragraph with physiological changes and the fourth again with fMRI but now task-related activation. It would make sense to discuss the fMRI results together.

The rationale for the study is not entirely clear. One previous study (Lochte et al, 2018) has investigated task-related fMRI activity in ASMR, although without control participants. Was it the aim to replicate their findings using a larger sample and including a control group? If so, this should be made more explicit.

This also relates to the hypothesis that ASMR, but not control, participants would show increased activity in sensorimotor regions. Why did you expect increased activity in specifically in sensorimotor regions if Lochte et al. found increased activity in a number of other regions?

It would be helpful to start the Discussion with an overview of all results, rather than selectively starting with discussing results that align with the hypothesis. How do these results compare with the previous study by Lochte et al.? After discussing the general findings, findings in individual regions can be discussed in more detail.

Line 112: It seems the authors did not pre-register their hypothesis. I would therefore suggest to tone-down "We therefore predicted", e.g. into "We therefore expect"

Line 243: "are represented in" is rather speculative. I would suggest staying closer to the results, e.g. "are associated with increased activity in the"
Experimental design: The main analyses are a within-subject contrasts between ASMR-related and control videos performed separately in both groups and a between-subject contrast between the ASMR and control group for ASMR-related video only. The choice for these tests should be better justified. In particular, wouldn't an interaction effect between group and video be a more appropriate test?

The authors should provide some justification for the sample size used in the study.
Validity of the findings: The within- and between-subject contrast are presented in separate figures and it is not very clear to what degree these regions overlap. An additional test for interaction effects may help (see above).

It would also be insightful to present the underlying data for key areas of interest, for example, by plotting the betas in both groups and for both types of videos. Ideally, these figures would show both the group averages as well as data from individual participants (e.g. using a scatter plot).

Line 241: "The challenge for future studies is to delineate the time course of these responses" Why is this a challenge for future studies? The authors could plot the BOLD response in key regions of interest in both groups and in response to both types of videos.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: A FUNCTIONAL MAGNETIC RESONANCE IMAGING INVESTIGATION OF THE AUTONOMOUS SENSORY MERIDIAN RESPONSE
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: This manuscript deals with the functional neural basis of the ASMR experience. The data shows increased activity in sensori-motor and affective areas of the brain in ASMR-responders.

First, please let me apologise for running late with my review. This is entirely my fault, and does not reflect on the quality of the submission.

I have no major problem with the way the study was conducted, or with the interpretation of the data. I have a few comments for clarification:

1. Line 51. 'Davies' should be 'Davis' (I get that a lot).
2. Line 192+. I am not familiar with BrainVoyager analysis. Are the contrasts able to detect decreases in activation, or are they only sensitive to increases? This is important, as I would be interested to know if ASMR-sensitive people are suppressing brain activity during the experience.
3. Is there enough data to correlate the change in activation with the subjective tingliness of the ASMR rating? That might get at the role of each brain area in mediating ASMR. The authors state (Line 254) that there is little variance in the subjects' responses, but could there be enough for a non-parametric analysis?
4. Line 247+. The authors suggest that activation in visual and auditory cortices may relate to the emotional content of the exerience. Wile this may be true, could it relate more closely to the content of the specific video? For example, more auditory activity in a more whispery video?
5. Line 259+. The authors specualte about the role of dorsal anterior cingulate cortex. Could I suggest that there may be an interesting interaction here with the salience network? The SN switches between the default mode and the central executive networks, so the dACC may be a gateway to allow ASMR-sensitive people to switch into the right state. I am an author on a paper on this topic that I confess I don't completely understand (the DCM part, at least), but it may be a good starting point if the authors are interested: https://doi.org/10.1016/j.neuroimage.2014.05.052