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: TVA-BASED MODELING OF SHORT-TERM MEMORY CAPACITY, SPEED OF PROCESSING AND PERCEPTUAL THRESHOLD IN CHRONIC STROKE PATIENTS UNDERGOING COGNITIVE TRAINING: CASE-CONTROL DIFFERENCES, RELIABILITY, AND ASSOCIATIONS WITH COGNITIVE PERFORMANCE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper is clearly written and conforms to professional standards. The “Introduction” section provides a solid context. Nevertheless, I have some concerns:

 - I think you could improve on explaining what exactly is assessed by the whole report task. In which way do the three TVA-parameters - threshold, speed, and VSTM capacity
– represent attentional abilities? In the “Introduction” section, several different abilities are mentioned, e.g. sustaining and focusing, which are quite different in neuro-cognitive terms. In particular, you talk about selection between competing stimuli (line 54), or between relevant and irrelevant information (line 69). As a result, it becomes not quite clear to which of these different aspects of attention the whole report task refers to. All the more, when considering the fact that the whole report task does not include any irrelevant stimuli. Perhaps, you might consider referring to a concept of attentional capacity which comprises speed and storage aspects, and is a core determinant of cognitive performance in general.

- lines 52/53: The background could be strengthened by providing a reference for “the distributed functional neuroanatomy supporting the range of attentional sub-functions”; see e.g. http://dx.doi.org/10.1016/j.tics.2017.01.011

- lines 78/79: Please mention that the letter displays are only presented for very brief exposure durations.

- lines 80/81: I am not sure whether the reader not familiar with TVA is able to understand the core idea of TVA from a single sentence. Thus, you should provide some more information on the TVA basics.

- line 83: Please mention already at this point, that the CCT was combined with tDCS. Otherwise, the later appearance of tDCS as a procedure in line 108 is extremely puzzling. Also include tDCS in Figure 1.

-Table 1: the abbreviation “lm” (case-control-comparison for the TVA parameters) is not explained. Presumably, it means “linear modeling”. Please specify!
Experimental design: - The rationale behind your fourth hypothesis (line 103: higher attentional abilities at baseline associated with larger cognitive improvement during CCT) requires some explanation. After all, lower levels of ability might, in principle, leave more room for improvement, which would predict that lower levels take more gain from training. Perhaps, your hypothesis is related to the concept of “cognitive reserve”?

- Please provide details of the experimental set-up and procedure! For example, did the experiment run PC-controlled, in a darkened room? What was the viewing distance? Size of the stimuli? Duration of the assessment? Etc.

- The statement from the discussion section (334/335: constraints for patient recruitment) should be included into the description of the patient sample.

- Were basic visual functions like visual acuity and contrast sensitivity assessed? If not, this should be mentioned as a limitation.

- Also, there is no information on psychiatric disorders in patients, in particular symptoms of anxiety and depression. This should also be considered as a limitation.
Validity of the findings: I thank the authors for their clear presentation of the methods and results. However, some points should be considered:

- While the healthy control group was matched by age and sex, this was not done with respect to education, and mean educational level was significantly higher in the healthy control group. In the statistical analysis, you used age and sex as covariates. The reason for this is not immediately clear to me, given the fact that the groups to be compared do not differ with respect to these variables. In contrast, although there was a significant difference with respect to education, this relevant variable was not included as a covariate in the analysis. Why is that? I would recommend repeating your analyses with education included as a covariate to see whether the results were affected by this group difference.

- I am not sure whether Figure 2 is really necessary: It is unclear how the association between age and TVA parameters relates to the hypotheses of the study. The case-control-comparison of TVA parameters is based on a group comparison, and both groups were well matched for age, as stated above. And for the longitudinal analysis for assessment of reliability, age also seems not to be a relevant factor. So, I would suggest skipping Figure 2 and the related statistics.

- There is no information on language disorders or visual field defects in the patient sample, whether these were criteria for exclusion or not. These are relevant issues in stroke patients. Please provide more information so that both the clinical feasibility of the TVA based assessment, and the validity of the findings as true attentional disturbances can be better assessed.

- With respect to the study aim of specific assessment of attentional sub-components, it appears as a problem that all three TVA-based parameters were affected. Does that mean that the different parameters are more or less indistinguishable indices of the same attentional deficit? Please provide the parameter inter-correlations, whether they are sufficiently independent from each other statistically.

- Patients were significantly impaired with respect to standard cognitive screening instruments (MMSE, MoCA). Therefore, the patients cannot be said to represent a “high-functioning group with relatively mild cognitive deficits” (line 330). Rather, it was quite a heterogeneous group with respect to cognitive impairment, with some patients severely impaired. You should also avoid concluding that TVA testing is “sensitive to subtle deficits” (line 289), because the data are not appropriate to support such a conclusion. It would, however, be interesting to see whether TVA parameters are related to global cognitive status, and, thus, reflect the degree of cognitive impairment to some degree. So, please provide correlations between parameters and cognitive screening instruments.

- In the “Discussion” section, you mention that baseline processing speed was related to “larger cognitive benefits of cognitive training” (lines 280, 312, 357). Such a statement is not correct, because there was no control condition for cognitive training, and the increase in processing speed might just be the result of several repetitions of the whole report. What can be stated is that parameter C appears to somehow indicate larger plasticity. Please revise!

- In line 299, you suggest that the failure of NIHSS and TOAST scores for explaining some of the parameter variance might be due to the complexity of the clinical etiology of attentional impairments after stroke. However, you should consider the possibility that associations would be revealed, if a different stroke classification was applied: For example, a differentiation according to the main cerebral arteries involved (anterior, middle, and posterior cerebral arteries).

- Lines 319-327: tDCS was not an a priori hypothesis, and also does not provide any additional information relevant for the scope of the paper: So; I would recommend skipping this paragraph.

- At the end of the “Discussion” section, please elaborate a bit on the implications for the clinical application of a TVA-based assessment in stroke patients! I think, this issue is under-represented. For example, what can the TVA-based assessment achieve that cannot be accomplished by cognitive screening procedures?  And do these possible advantages justify the extra time required for assessment?
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: TVA-BASED MODELING OF SHORT-TERM MEMORY CAPACITY, SPEED OF PROCESSING AND PERCEPTUAL THRESHOLD IN CHRONIC STROKE PATIENTS UNDERGOING COGNITIVE TRAINING: CASE-CONTROL DIFFERENCES, RELIABILITY, AND ASSOCIATIONS WITH COGNITIVE PERFORMANCE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have done a great job improving the manuscript and clearing up any ambiguities or lack of reporting that were pointed out in the review.
Also, revised and new versions of figures and tables add significantly to the readability of the article.
Experimental design: The experimental design has been described more clearly and the hypotheses now appear relevant and aligned with the design and the possibilities/limitations afforded by this. At the same time, it is now clear that the study addresses a knowledge gap in the literature.

The suggestions for improving the analyses have all been incorporated and the results and discussion sections have benefitted substantially from this.
Validity of the findings: I only have two minor comments:

1) I was happy to see that the authors included a remark referring to none of the patients as having severe visual or linguistic impairments in both the methods section and in the discussion. In the latter it was mentioned as a potential limitation that this was not formally assessed. To aid the reader in understanding the possible impact of e.g. visual impairments in the current study, I would like to see a single sentence on the validity of the findings as attentional impairments and not "just" visual defects.

2) In the discussion it is stated "Further, the lack of control group in the longitudinal study does not allow us to separate the potential benefits from CCT on attention from the learning effect from repeated TVA assessment". I would encourage the authors to discuss whether the putative benefits of CCT are over and above the improvements to be expected from repeated TVA-based assessment, based on previous studies looking at this.
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: TVA-BASED MODELING OF SHORT-TERM MEMORY CAPACITY, SPEED OF PROCESSING AND PERCEPTUAL THRESHOLD IN CHRONIC STROKE PATIENTS UNDERGOING COGNITIVE TRAINING: CASE-CONTROL DIFFERENCES, RELIABILITY, AND ASSOCIATIONS WITH COGNITIVE PERFORMANCE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The paper now reads well and the authors have worked hard to incorporate the previous literature into this version of the manuscript.
You may wish to include this paper as a previous study using TVA to measure training effects in stroke patients  Peers et al.  Neuropsychol Rehabil. 2020;30(6):1092-1114. doi:10.1080/09602011.2018.1554534
The paper is well structured and figures and tables are clear.
The hypotheses have been re-worked and are now clearer
Experimental design: I am still very concerned about the experimental design and the conclusions you draw from this data.   Whilst great efforts have been taken to collect longitudinal data from a good sample of stroke patients whilst they complete cognitive training, the lack of a control arm really limits any conclusions on the sensitivity of TVA to measure change in patients.  I am pleased to see that you attempted to examine this issue more closely by looking to see whether change in performance on CCT was associated with specific changes in TVA parameters.  Your analysis suggesting that improvements in CCT were associated with increased K, decreased perceptual thresholds, but also increased errors, suggests to me that you are measuring a change in speed accuracy trade-off rather than a more profound change in cognitive function as a result of an intervention. I feel it would be better for you to focus the conclusions on reliability rather than discussing sensitivity as I really don't think it can be adequately addressed without the control arm.
Validity of the findings: I think this is well conducted work and if you were to simplify the message to indicate that TVA is reliable measure and is feasible for use in studies in patients with a range of severity then it is important work.  I am concerned about the strong claim you make about sensitivity as I am not convinced that this can be addressed adequately with the current data.
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: UNSUPERVISED INFERENCE APPROACH TO FACIAL ATTRACTIVENESS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Overall, this is an interesting approach. I appreciate the earlier authors’ development of a new method to extract human preference behavior in relation to faces. It’s a clever and fairly naturalistic approach. In the current work, the predictability of gender difference is an interesting and significant addition. However, I see issues with the interpretation of the present results, and also underlying issues and lacunae in the psychophysical procedure.

1.	The model introduces symmetry to otherwise asymmetrical faces by applying the same transform to both sides of the face. This is somewhat unavoidable but it has yet to be shown that, given freedom to manipulate both sides of the face, people don’t introduce small asymmetries, if only to make a face less “uncanny.” In any case, the present method does not help disentangle the influence of symmetry. Nor is it clear that people really “like” the sculpted faces they make. I would have had users compare each user-sculpted face to a symmetrized version of the same (unaltered) face—individuals should prefer the face they sculpted (maybe with some control for familiarity). If this is not the case, the MaxEnt models for individuals aren’t very meaningful.
2.	Also it is not clear that people can see the changes they make in the sculpted faces.
a.	Stimuli are B/W (compressed?) 300x400 pixels, shown at unreported viewing distance, and there seems to be no control for individuals’ optical errors (corrected to normal?). Maybe people selected preferred images in each pair based on visibility of difference compared to the previous trial. In any case, no one would confuse these small, low-res images for real faces.
b.	Subjects were apparently uncompensated and mostly undergraduates so it’s not clear how careful or motivated they were. Also, what were the instructions? Choose the face you like best? Or the “choose the most attractive face”? These might be different: the first question is about personal preference while the second could be about cultural norms. (also how is gender assessed? Again there are culturally normative effects possible here).
3.	With the generative models, why not generate new sculpted faces tailored for each subject and have that subject choose between that face and, e.g., a face sculpted from the preferences of someone else of the same gender? The subject should choose the face sculpted from their own preferences. As it is, the generative model could just be overfitting an individual’s idiosyncracies of adjustment rather than preference (except for the gender difference).
4.	Showing model accuracy for gender of the observer doesn’t really follow or support the premise of the work, which is that individual preferences are systematic. I would refocus on the gender result rather than claiming that you are modeling individual preference.

Minor comments

Lots of grammar issues. A non-exhaustive list:

Citations should be in parentheses.
Line 40: Grammar/typo
Line 45: What phenomenon? Unclear sentence
Line 47: Not sure what “On the other hand” refers to.
Line 161: precedent: preceding


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: UNSUPERVISED INFERENCE APPROACH TO FACIAL ATTRACTIVENESS
Review round: 1
Reviewer: 2

Output:
Basic reporting: I find the manuscript to be interesting, but the motivation murky and findings are a bit unclear.

The manuscript can use a bit more editing. I found a misspelling of gender "genender" that should have been picked up by spell checker.
Experimental design: The research question itself is somewhat interesting, but on the whole I don't understand why there would be an expectation that facial deformations would be preferred across people or not. I don't understand why there is a clear gender difference, or what the difference is. The theoretical motivation is lacking.
Validity of the findings: In the supplemental material the authors state that the model is not overfitted, so perhaps the higher order interaction is replicable, but is it understandable?
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: UNSUPERVISED INFERENCE APPROACH TO FACIAL ATTRACTIVENESS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript „Unsupervised inference approach to facial attractiveness“ deals with probalistic models that predict the gender of persons that created faces to their maximum attractiveness in virtual face spaces.

The language of the whole manuscript is extremely vague. Therefore, it was quite often hard for me to follow the authors‘ thoughts. E.g., „it has been conjectured that this approach does not capture the complexity of the phenomenon.“ (Abstract). This might be true, but I cannot verify this claim since the authors did not give precise information on why the complexity oft he phenomenon is not captured. Another example: Line 43ff: If you criticize the natural selection hypothesis, please explain your criticism to the reader: „that it does not take into account the phenomenon in its various complex facets“ is no proper critique. Similar passages can be found throughout the manuscript and make it very hard to follow (or to criticize).

To the same point: In my opinion, there is not a sufficient literature review. Quite a few important studies are cited, but the manuscript lacks clarity on the relevant (detailed) results of those studies.

The manuscript needs a language check, preferably by a native speaker. There are numerous misspellings and grammatical errors. Furthermore, I found the citation style rather confusing (only the year oft he citation is in brackets) – this made the manuscript rather difficult to read.

The introduction already includes the main results.

The research question is relevant, especially taking into account that the higher accuracy of the non-linear model includes implications on the nature of visual processing of facial attractiveness. While these implications remain to be tested, the results are in itself quite promising.
Experimental design: From my point of view, the study is well designed. However, methods as well as results are not presented in a way that makes understanding easy for the reader. Descriptions are quite technical without any further explanation.

(1)	The Restricted Boltzmann Machine model is not sufficiently explained.
(2)	The manuscript lacks a technical comparison between all three methods.
Validity of the findings: I am not sure whether I missed it, but I did not find any information on the number of subjects that were included in the analysis.

The authors state that it should be a next step to test the results with other datasets. I completely agree. However, I think the authors provide enough data for a coherent study.

The high accuracy is surprising and extraordinary.
Additional comments: The strength of the manuscript is that it compares several methods to predict the gender of a person based on their face attactiveness preferences. I like the use of the Maximal Entropy Model in this area of research, especially since it also provides some quantitive insight.

The weakness is the structure of the manuscript itself as well as the language. Especially in the introduction, it is often not clear which point the authors‘ are making exactly. Within the  materials, the authors provide lots of detailed information, but I lost track some times since I am not an expert in MaxEntropy.

I’d be highly interested in the effect of sexual orientation on the results, but I guess this information is not available in Ibanez-Berganza et al. (2019).

I’d like to encourage the authors to work on the structure and the language of the manuscript in ordert o make it more accessible. The approach itself is very promising and the results are more than interesting.

Minor points:

Please explain Figure 2 in more detail (longer caption). I did not fully understand what is demonstrated in this figure.

The terms beauty and attractiveness are not distinguished.

Abstract: What are „detailed and global facial features“?


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: UNSUPERVISED INFERENCE APPROACH TO FACIAL ATTRACTIVENESS
Review round: 2
Reviewer: 1

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: N/A


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: LONG-TERM PARTICIPATION IN COLLABORATIVE FISHERIES RESEARCH IMPROVES ANGLER OPINIONS ON MARINE PROTECTED AREAS
Review round: 1
Reviewer: 1

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: This manuscript looks at the influence of participation in the CCFRP on the perceptions of anglers towards MPA management and fisheries data. It uses an online survey of 111 respondents to  examine their self-reported changes in opinions. Overall the manuscript is very well written and structured and I think would make a valuable contribution to the field. It touches on an important point, the fact that citizen science isn’t just about the science but also public outreach, and sets out to test hypothesis in line with this. I think the conclusions about the importance of long-term involvement are really good to share.

There are however a few major issues that I think need to be resolved before this manuscript could be accepted. Therefore I am recommending a major revision. Below are a series of points that require addressing. While most are relatively minor, there are two issues that are major.

Major comments:
1.	First and foremost, I don’t think your data supports your conclusions about whether long term participation improves opinions on fisheries data quality. Looking at figure 5, it’s hard to really accept your conclusions when only 51% of those with preexisting opinions changed towards the positive. The nature, and limitations, of survey data like this is that it is difficult to analyze (i.e. there are no means and SD here that you can test for this specific question), therefore I don’t think it’s really fair to say that the program improved opinions on fisheries data quality. Given there were 111 participants, and how close these numbers are, there is no way to be certain that if more people were surveyed, or less, that the 51 vs 49% wouldn’t change. I therefore think the entire manuscript, from the title to the discussion, needs to be adjusted accordingly. Figure 6, and the opinions about MPA looks solid, but not the results presented in figure 5. And as your title claims, this is effectively half of the story.

2.	The second major point has to do with limitations from these kinds of studies, which I don’t think was adequately addressed anywhere in the manuscript. I would like to see a section, perhaps in the discussion, mentioning the caveats or limitations of this approach and data. The issue has to do with attributing causation that changes in opinions occurred as a direct result of the program, and not other confounding factors. This study uses a reflexive counterfactual (See reference below for definition, although there are other papers which may be more suitable to reference), whereby the study relies on each respondent having a clear understanding of causal links. i.e. the issue here is that after the fact, asking people whether a program has been the thing which has changed their opinion relies on them understanding other potential factors that may have also changed their opinion, and also accounting for whether they were already conservation minded. In addition to the fact that the program itself is the one doing the asking, which may bias peoples answers. In a perfect world your hypothesis would have been tested by sampling behaviors (or opinions of management, but not opinions about changes in opinions to management) prior to and following their participation in the program to look for differences. In this case this wasn’t possible, which is okay, but I think this needs to be addressed as a limitation of this kind of data. It is relying on peoples sometimes imperfect memories, after the fact and asked by a group with a potential conflict of interest. Within this, a second caveat is the fact that a biased group of people likely answered the survey, they had to be engaged enough to answer it, so it could have easily been a biased population. I don’t think all of this warrants disregarding the results, but these limitations should be articulated, and the conclusions adjusted for these caveats.

Smallhorn-West P, Weeks R, Gurney G, Pressey B (2019) Ecological and socioeconomic impacts of marine protected areas in the South Pacific: assessing the evidence base. Biodiversity and conservation

Minor comments:
•	Reference for figures should be at the start of when they are mentioned, not at the end (throughout, but e.g. fig 2b should be on line 233, not 236)
•	Figures 2 and 3: I think you could change the shading order. If darkness is meant to be hypothesized conservation knowledge, then dark would be marine resource management, mid fishing industry and light no experience or vice versa.
•	Figure 3: If possible put effective, Not sure and ineffective in a,b and c somewhere to see in the graph not just the caption
•	Figure 6b: % should be same as in the text
•	Figure 7: Title should have relative to time at the end of the sentence. Also not sure why only positive graph has the dashed line.
•	Table 1: include other gender categories
•	Line 97 MPA network, not MPA.
•	Figure 5 vs. 6: again if you remove 5 this won’t be an issue, but I don’t understand why the same method, and same graph, wasn’t used for both fisheries data and MPA opinions.
•	In future, it could be useful to have specific things about MPAs that were being asked about, as well as overall opinion (e.g. performance, social impacts…)
•	Line 275: This sentence seems redundant, as a positive change necessitates the others going down.
•	Line 313: First sentence of discussion doesn’t mention the fisheries data opinions at all, just MPAs. These seem like they were of equal importance so would include both (since both are in the title). But again may need to be adjusted if you keep the fisheries data sections.
•	Line 391 is confusing, why does the fact that they are rockfish imply the stocks are healthy?

It’s great having the time analysis, I think this is a solid conclusion from this work and a really useful point to make. Great job! At the end of the day, I think the conclusions about the MPAs are sound, but again not so sure about the fisheries data ones.


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: LONG-TERM PARTICIPATION IN COLLABORATIVE FISHERIES RESEARCH IMPROVES ANGLER OPINIONS ON MARINE PROTECTED AREAS
Review round: 1
Reviewer: 2

Output:
Basic reporting: - The paper was well-written and the research was clearly explained and straightforward to follow.
- References provide adequate background and context for the scope of this research (i.e., collaborative fisheries research/citizen science related to CA, the CCFRP, and/or CA MPA attitudes and opinions).
- Article follows professional article structure. Nearly all tables and figures are referenced in the text (see 4. General Comments for exceptions). Raw data and analytical code was shared.
- Results are relevant, timely, and of interest, particularly to collaborative fisheries research programs and more general citizen science efforts. This research is a positive contribution to this literature.
Experimental design: - The research is a result of primary data collection utilizing an existing database (sample frame) of volunteer anglers. The research is original in its scope (i.e., collecting demographic variables and data quality and MPA attitudes from this sample frame), and fits with the “Aims and Scope” of this journal.
- The main purpose of this research, to collect demographic and attitudinal data about MPAs, fisheries data quality, and CCFRP experience from volunteer anglers, is stated clearly and is relevant to collaborative fisheries research programs and perceptions of spatial management (e.g., MPAs). The paper mentions how this study contributes to the paucity of published literature related to California-specific attitudes and perceptions related to MPAs, fisheries data quality, and the CCFRP program.
- Methods are described clearly and should be replicable, particularly given the data and R code are available in the supplemental information.
Validity of the findings: - Discussion and presentation was focused on significant results.
- Data and analytical code in R were provided and appeared to be robust.
- Conclusions were quite clear, were relevant to the original research intent, and were supported by the Tables and Figures. The paper was fairly tight (i.e., little if any extraneous narrative) and focused on the primary and significant results.
- Limited speculation is characterized with phrasing such as, “It is also possible…” (lines 398-399).
Additional comments: Line 50: Is “(California)” necessary after “1999”? “California” is mentioned multiple times in this sentence.

Line 158: What are the work experience categories? I appears to be defined for the first time in lines 219-220.

Line 202: Can you briefly characterize the 15% response rate relative to other online survey efforts found in the literature? It is unclear whether 15% is average, high, or low for an online survey in general or one that is fisheries or environmentally-focused. Perhaps survey response rates are mentioned in one of the papers already referenced? E.g., Baldassare et al., Loper, Ordoñez-Gauger et al., Rubio et al.

Lines 284-286: the order the three calculated measures of participation are listed here as year, workshops, trips but in a different order in lines 183-185 (year, trips, workshops). Small detail but I suggest using a consistent ordering throughout the paper. Also in lines 460-462 as well as in Table 2. Easiest fix would be to re-order in lines 183-185, as the rest of the paper has them ordered as year, workshops, trips.

Line 296: to aid interpretation of the statistics (e.g., RRR value) in line 297,it would be helpful to mention that “positive change in opinion” is the reference category (or referent group).

Line 356: rather than comparing the number of participants in the MLPA process to the total CA population (39 million), it may be more useful to compare to the number of coastal county residents (for example) or to the number of people living within a certain distance from the coast (e.g., 100 miles). These may be a more “fair” comparison due to their easier access to the coast and therefore to the MLPA process which, I assume, occurred primarily on the coast? However, using these other values will not change your primary point: that a relatively small proportion of Californians participated in the MLPA process. So this is definitely a suggestion but not a necessary change.

Lines 372-375: I found the beginning of this paragraph and these lines in particular very confusing. Which “two programs”? And why is it “… likely that the 111 respondents in our study represent an accurate sample of those who plan to continue with the program”? How this conclusion was reached is very unclear.

Line 388: was unsure what “accurate consensus” meant until I reached line 398. Perhaps define “accurate consensus” up front so that we understand it to mean consistency between what is believed and what actually is the state of things (if I understood it correctly!).

Line 417: missing a “)” after “Hexagrammidae)”

Lines 426-427: “i.e.” vs. “i.e.,” Throughout the paper, “i.e.” seems to be used but “i.e.,” shows up here. Choose one for consistency.

Lines 449-450: Is it possible that more conservation-minded volunteers were also more likely to respond to your survey? This gets at possible bias in your response rate, e.g., those who responded may have been more conservation-minded than those who did not respond (nonresponse bias). Is there any data on those who did not respond to your survey that could be used to test for nonresponse bias? If not, it would be worth mentioning directly in the same paragraph as the reported 15% response rate (line 202), when you characterize your response rate relative to other online survey efforts.

Lines 469-471: is it possible that volunteer anglers who participated in the Volunteer Appreciation and Data Workshops were more likely to return in subsequent years to volunteer? Did you look at this? (i.e., how participation in these workshops or average number of trips might be related to continued participation)

Lines 492-495: awkward sentence, please restructure and/or split into two sentences. E.g., “Overall, these volunteers have a positive view of the data collected for resource management and the MPAs they help to monitor. This can be attributed, in part, to long-term participation in the program.”

Lines 496-500: this is an important conclusion and contribution to this literature. Sustained volunteerism can contribute to attitude change.

Table 1 is not referenced in the text.
Articles S2 and S3 are not referenced in the text.


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: LONG-TERM PARTICIPATION IN COLLABORATIVE FISHERIES RESEARCH IMPROVES ANGLER OPINIONS ON MARINE PROTECTED AREAS
Review round: 2
Reviewer: 1

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: Thank you for taking the time to revise the manuscript and give detailed responses to the reviews. I think overall the manuscript is almost ready for publication. There are a few minor issues I think would be good to address first, but they shouldn’t take too much time.

Major comments:
My two main comments are with figure 5 and 6, which I still find confusing.

Figure 5 – Going through the questionnaire I can see why the figure is like this, but until I did that it was unclear. I still think this is misleading, and even more so than before as now if you aren’t careful you will think that the program has made huge changes in people opinions. But the reality is that half of those who had opinions prior weren’t changed, and unlike below you can’t tell if this is just because they were already positive. So if you are going to do a column I’d have it will negative change, no change and positive change. Or what would be simpler is to just provide the pie chart with four categories: no opinion before, negative change, no change and positive change.
The result here is that half of people’s opinions weren’t changed by the program, don’t try and hide this. But unlike below we can’t tell why that was.

Figure 6 – I also wonder if there is a better way to display this figure. Unless I also read the text I am left thinking that 49% of people did not change their opinion, which is true, but this is because they already had positive opinions. You should aim to let people interpret the figures without having to read the text in detail. So sort of opposite to figure 5, I wonder if here you could actually just show a pie or column of those only with a change in opinion, rather than having the no-change part in the pie chart, because unlike figure 5, they already have this information in the bars. I appreciate the difference of what is possible between these figures, so how can you make them as clear as possible?

Minor comments:
Line 139 – Would it be possible to add a few lines explaining what you mean by Margins of Error (MOE) and how this works? I can check the referenced paper, but a few lines would be good to provide an overview.

Line 154 – Smallhorn-West et al. 2019. Again though there may be better references on reflexive counterfactuals within that paper. See Franks P, Roe D, Small R, Schneider H (2014) Social assessment of protected areas: early experience and results of a participatory, rapid approach. IIED Working Paper. IIED, London

Line 155 – I think a-d are a bit of a stretch on limiting non-response bias. Sure the demographic questions do but not the first part. Anonymity equally means you can’t determine whether there is non-response bias easily. I’d just leave this as a limitation of the manuscript. No paper is perfect and this is a key caveat of yours. I think here, and also at least once in the discussion, you should explicitly state this caveat and its potential limitations, but end by saying something like ‘nevertheless, despite these limitations this study/these findings are still useful because…’

Line 166 – Again, it’s also okay to say this is a limitation. Plenty of studies use this approach, but just be clear about what it means.

Line 266 – So this clearly shows that there is in fact a bias in the population, not by demographics that you measured above, but that respondents consider themselves more conservation minded than their peers.

Line 492 – This heading is really confusing – maybe “Why volunteers may be less opinionated about fisheries data quality than MPA effectiveness” or something like that.

Lastly, as a point of clarity when reading through I’ve found that in my head it all starts becoming clear when I realize there are two things being looked at in aim c (from the introduction): fisheries data quality and opinions about MPAs. First, in the last paragraph of your introduction, make sure everything is in the same order you present it in. Second, it could help with the clarity to just restate this using similar terminology in the methods, results and discussion about i) change in opinion on fisheries data quality, and ii) change in opinions on MPAs. E.g. Line 312 heading title is confusing. Make this heading Change in opinions and then two subheadings i) fisheries data quality (not just data quality) and ii) MPAs.


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: ASSESSMENT OF NATIONALLY REPRESENTATIVE DIETARY STUDIES IN THE GULF COOPERATION COUNCIL: A SCOPING REVIEW
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript describes a review to collect, quantify and critique the quality of data on the dietary studies conducted in GCC countries by using an objective scoring system approach.
It was well written and easy to follow. However, the authors could avoid the use of 'we' in the write up and rather use reporters' speech.
Experimental design: The study design/methodology is clear. However, it would be useful to justify why only two databases (PubMed and Web of Science) were used for the search.
Validity of the findings: The authors indicated the limitations of this review due to the fact that only two main databases were used. Thus the limited number of studies might have affected the findings.
Additional comments: The review is interesting and easy to follow. The recommendations are sound and would be useful. However, it would be useful to extend the review including other search database such as DOAJ, GOOGLE SCHOLAR and SCOPUS.


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: ASSESSMENT OF NATIONALLY REPRESENTATIVE DIETARY STUDIES IN THE GULF COOPERATION COUNCIL: A SCOPING REVIEW
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is well written for the most part. I made some recommendation on some words that should be replaced and some sentences need to be rephrased or separated to ensure good flow. See some examples below:

1.	Line 2 and 3: I recommend writing GCC in full in the title
2.	Line 39-42: should be divided into two complete sentences. Replace “i.e” with “that is”
3.	Line 48: replace “e.g” with “such as”
4.	Line 53-54: please rephrase this sentence “However, dietary studies have been limited; the research output from Arab countries constitutes ≈ 1% of global research (9).”
5.	Line 171: replace “sugared” with either “sweetened” or “sugary”

The authors have provided relevant literature references, standard article structure and the introduction clearly introduced the subject and the motivation behind it.
However, I think the introduction would be more valuable to readers if more information are provided on the subject of obesity in the GCC, and some of the factors limiting research quantity and quality on this subject.
It seems also that the authors did not point out any research similar to what they have conducted. This makes it difficult to fully assess the quality of this study.
Experimental design: It is a bit unclear if this article is within the Aims and scope of the journal. Although, the manuscript has been considered as a literature review, the structure is closer to a research article (because it has methods, results and discussion which are mostly absent in a typical review manuscript). The manuscript also looks like a meta-analysis. I'll leave it to the editor to determine if this is actually a research and review article and my feedback will based on evaluation of the manuscript as a literature review.
I don't think the manuscript is detailed enough to be considered a review of the literature. Most of the cited literature were not explored in detail. To make it better, the authors could include all the published articles they found in their search into this review (regardless of their strength and weaknesses) and pointing out those studies could be improved. That, I think would a better read.
Validity of the findings: The findings of the search of the literature conducted by the authors were clear and the conclusions identified gaps and future direction.
Additional comments: No comment


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: ASSESSMENT OF NATIONALLY REPRESENTATIVE DIETARY STUDIES IN THE GULF COOPERATION COUNCIL: A SCOPING REVIEW
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have managed to address the review comments and improved the manuscript.
Experimental design: Satisfactory!
Validity of the findings: No comment.
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: ASSESSMENT OF NATIONALLY REPRESENTATIVE DIETARY STUDIES IN THE GULF COOPERATION COUNCIL: A SCOPING REVIEW
Review round: 2
Reviewer: 2

Output:
Basic reporting: Improvements recommended during the first review has been applied
Experimental design: Study design has been improved with the addition of the supplemental files
Validity of the findings: Conclusions and next steps were clearly stated
Additional comments: No comment


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: RANDOM FOREST ALGORITHMS FOR RECOGNIZING DAILY LIFE ACTIVITIES USING PLANTAR PRESSURE INFORMATION: A SMART-SHOE STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comments
Experimental design: no comments
Validity of the findings: no comments
Additional comments: The paper is well structured and has systematic exploration of using plantar pressure for activity classification. However, due to  excessive details about sensor and feature selection, the paper is a little difficult to understand specifically for results. Here are some comments:

1) I generally recommend the authors to remove the descriptions about energy expenditure in the paper, considering the paper does not work on algorithm related to energy expenditure and the paper focuses on activity classification only.

2) I recommend the authors to rewrite result section. The authors used all sensors and features configuration to determine optimal window size. And then use the determined window size for the following sections. This raised a question that maybe in other configuration of sensor and features, this window size is not optimal. Please give more explanations about this. Why do the authors simplify the selection of window sizes while selecting features and sensors?

3) In abstract, please give a concise description for validation method? Like cross validation or hold-out validation?

4) In Line 40-43, all prediction accuracy percentage is obtained under window size of 20 seconds?

5) For one category of activity, sitting, there could be some confounding factors which influence the measurements? Could the author release information about height of the chair? As we know, if the subject's lower leg is shorted than the height, the foot will be not on the ground while sitting and plantar pressure is 0. In some cases, the foot could be on the ground.

6) In line 74-75, nature of acceleration data does not allow refining of the classes until all daily life activities are identified. It is unclear and why?

7) In 232-233, the authors mentioned 20 train-validation runs? so all runs is on training dataset (6 subjects)? Is it cross validation? If the reviewer's understanding correct, the validation dataset (11 subjects) might be better called testing dataset to avoid confusion?

8) From 240-274, the window size, number of sensors and features are all determined by training dataset? Please ensure not to touch the validation dataset while doing sensor and feature selection and hyper-parameters configuration. The dataset deriving reported accuracy percentage should not be used in model configuration.

9) From line 282-284, the authors first mention the best accuracy is achieved at 45s, and then what does best forest mean at 30 seconds? And then why the author select 20 seconds as the optimal window size. Please give clear explanations of rules about selection of window size.

10)  In number of sensors and features subsection, the protocol of evaluation is not clear. Did the authors first determined sensor number while using all features? And then fixing the optimal sensor number and then work on feature selection? Is this understanding correct? It seems there are a lot of combinations of sensors and features? For 7 sensors, the total number of combinations is 7*6*5....*1. If considering the feature number, the combination is more various. The reviewer accept some degree of simplification, but please give more clear explanations.


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: RANDOM FOREST ALGORITHMS FOR RECOGNIZING DAILY LIFE ACTIVITIES USING PLANTAR PRESSURE INFORMATION: A SMART-SHOE STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The rational for this study is clearly presented, with appropriate links to literature in the field. Authors provided sufficient field background, relying on adequate references.
Experimental design: Authors used meaningful methods, which are well described. I only have two questions:

1. Did participants perform the 9 tasks in a pre-defined order or randomly-selected order? This can possibly influence the performance of algorithms to recognize activities.

2. To train algorithms, authors used a five-different subject-independent training–validation assignments. Would a higher number of subject for training have changed the performance of algorithms regarding good predictions?
Validity of the findings: Results are presented with details; text, figures and tables complement each other. Even the algorithms showed acceptable performance, there are room for improvement. This inspire my following question:

The average good prediction was 0.89, which is good but not perfect. Would a more heterogenous sample have contributed to increase the performance of the algorithms?
Additional comments: This study reports results on the performance of random forest algorithms for the recognition of daily life activities using plantar pressure information collected with a smart-shoe. For these goals, authors enrolled 17 female healthy subject with mean age of 26 ± 9 years old who took par in the experimental study. Their results confirmed the possibility of high-performance human behavior recognition using plantar pressure data only. The study is interesting. The manuscript is well written and conclusions are supported by reported results. There are only few aspects I would like authors to comment and possibly consider the above questions to improve the quality of their 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: RANDOM FOREST ALGORITHMS FOR RECOGNIZING DAILY LIFE ACTIVITIES USING PLANTAR PRESSURE INFORMATION: A SMART-SHOE STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: NA
Experimental design: 1) In Figure 4, the color bar in stage 2 is unclear. What does "expected to perform" mean? It should belong to "RESULTS"
Validity of the findings: NA
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: TRANSCRIPTOME ANALYSIS OF DIPLOID AND TRIPLOID POPULUS TOMENTOSA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Bian et al. use gene expression dataset obtained from RNAseq and qRT-PCR to investigate patterns of gene expression difference between diploid and triploid species of P. tomentosa. Their study is based on previous work showing differences in growth and stress resistance between the two species of Populus. They noted several transcripts that were DE between the diploid and triploid Poplar that were enriched for plant-pathogen interaction pathway, stress resistance and several growth related transcripts too.

Overall, this manuscript describes patterns of gene expression in the diploid and triploid species of poplar. However, I think because the authors were very focussed on finding growth related transcripts being upregulated in the triploid, they have missed the opportunity to explore certain pathways that may not directly be related to growth and superior performance but can have key implications for tree breeders. Besides, superior growth in the triploid poplar need not always be related to upregulation of growth related transcripts across all developmental stages. With regard to exploring other pathways, their study shows the plant-pathogen interaction pathway to be enriched among sets of transcripts that were DE. Genes in this pathway are known to be diverse and large in plants and are known to be involved in  reproduction isolation across Arabidopsis and Poplars too. While investigating neo-functionalisation and sub-functionalisation of genes belonging to this pathway in the triploid Poplar maybe beyond the scope of this work, it would be useful to speculate on this in the discussion. A simple summary of how many genes in this pathway have zero expression in the triploid poplar or are associated with different GO node terms relative to the diploid would be good. Further, the enrichment of DE transcripts in this category could provide useful information to tree breeders intending to generate heterotic F1s. The pathway enrichment approach also shows several other interesting candidates that would be worth future elaborating on and relating to previous studies demonstrating higher stress resistance noted in the triploid poplar. Another place to elaborate would be the DE of MDH & CYCD3 genes as evaluated using qRT-PCR. I think it would be useful to relate their finding of higher expression levels to higher rates of photosynthesis which in turn contributes to higher timber yield. Maybe relate to other studies that have demonstrated a relationship between the rate of photosynthesis and faster growth and higher timber yield or have evaluated the rate of growth in mutants of MDH and CYCD3.

I would also have liked to see a qRT-PCR on lignin production related transcripts since it is a key trait used by tree breeders. If that is not possible, evaluating patterns of DE for some of the lignin production related transcripts using the RNAseq data would also be useful.

Specific and minor comments:

Line 49: this sentence seems incomplete, should it be a continuation of the previous sentence and not a new sentence.
Line 58: please provide a reference for genome duplication due to hybridization.
Consider changing line 73 to read as : RNA was extracted using the Tiagen kit.
Line 74: change “performed” to “generated”
Please provide the settings used while running Trimmomatic and Soapnuke. For instance, was trimming of polyA tails conducted, what was Q score cutoff, length cutoff etc. in Trimmomatic.
Line 114: This is the first instance where the authors talk about CDS & SSR, please mention in the methods section how these were detected.
Were the GO annotations performed using protein sequences or using nucleotide? I am assuming protein sequences were used for this.
Line 124: Detection of transcription factor families is not mentioned in the methods. Is this based on the annotations, if so please clarify.
It is unclear to me what the authors mean by “involved in the transcriptome” mentioned at line 126.
Line 137: This sentence is unclear. Does 22k refer to the set of DE transcripts that had GO annotations, or does it refer to the set that was not DE? Please clarify.
Line 150-153: Not clear.
Line 159: This is confusing. Earlier you mention that there are in total 32k DE transcripts, so what does this 12k refer to?
Line 177-178: Please elaborate what you mean by “was obviously different from transcriptome analyses”.
Line 193: Please provide a citation for this statement.
Please rewrite line 193 to 196. In line 193 it is not clear whether the authors are referring to larger leaf sizes for polyploid plants. Similarly for line 194, consider rewriting to:
Huang et al (1990) have demonstrated larger branches, leaves and fruits in the triploid variety of pear compared to the diploid variety.
Line 202: what are the authors comparing to?
Line 214-217: These sentences as written are not clear. Please consider elaborating what you mean by cryptic. It is also not clear how the various studies listed here are related to gene expression differences noted in your study.
Table 2 & 3 needs to be formatted correctly. Also consider using superscripts to describe what level1 and level2 are.
Please check if fig 3 is representing Up and down regulated transcripts after FDR.
Fig 6: It is very difficult to see the bars for expression levels using the transcriptome dataset, which is expected given the higher sensitivity of qRT-PCR. I would suggest changing the y-axis to a log scale or presenting these as two separate panels. The y-axis is also not labelled.
Experimental design: Are D1, D2, D3 & T1, T2, T3 representing biological replicates or technical replicates? Please clarify at the first mention and also in the methods for DE.

There are also several other aspects of the methods that need to be elaborated on and I have listed them above under "specific & minor comments".
Validity of the findings: --FPKM not ideal for across sample comparisons (unless the cross sample scaling was performed prior to getting FPKM). FPKM is ok to compare gene expression within the same sample. I would suggest using TMM which is easy to implement and robust.
See:
https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3608160/
https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5411036/
https://genomebiology.biomedcentral.com/articles/10.1186/gb-2010-11-3-r25

--Please provide more details for the DE section of the methods. It is important to mention that the data was normalised and the approach used for normalisation and whether the transcripts were filtered for minimum count prior to assessing differential expression.

--I am curious as to why the authors decided to use phyper against several other methods specifically designed for conducting GO category enrichment. But more importantly, please mention whether the test conducted was two tailed or one tailed for enrichment. Based on the figure, it seems the test was one tailed.
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: TRANSCRIPTOME ANALYSIS OF DIPLOID AND TRIPLOID POPULUS TOMENTOSA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Although the authors used a proofreading service, this manuscript could benefit from another proofreading by someone familiar with the field. The English used in the article is, in general, good. However, there are enough instances where the meaning of the authors is ambiguous that the overall clarity should be addressed.

The authors primarily focus on the need for better approaches to crop improvement of tree species from an applied point of view (i.e. discussing the superiority of triploid P. tomentosa for timber qualities and growth vigor). Given that PeerJ has a relatively broad audience, the authors may need to explain some assertions they currently take for granted. What defines good wood quality? Fast growth and long life as compared to what? Other trees in northern China? Trees worldwide? Commercial trees? The second paragraph of the introduction does a better job of describing the difficulties of performing genetic improvement of tree crop species, but I think it would benefit from a considerably more comprehensive literature search.

In general, there is not sufficient background provided in the introduction, and references are sparse. Additional scholarship should be done, particularly focused on diploid vs polyploid traits in crop species. The third paragraph describes differences between triploid and diploid P. tomentosa, but misses an opportunity to better motivate their work. There is a wide literature comparing diploid and polyploid individuals for a variety of crop species that would be relevant here, but the authors choose to focus on P. tomentosa alone. A broader discussion of why polyploid plants often exhibit traits that are commercially beneficial, especially with respect to differences in gene expression, would be beneficial here.

Minor comments/suggestions:
Line 35: Briefly explain what good wood quality is.
Line 45: "the tree transcriptome" or "tree transcriptomes"
Line 51: omit ploidy
Line 52 and line 182: although not exactly wrong, "obviously" is not a commonly-used word in most scientific literature (generally one's data should make something obvious). I would omit this.
Line 57-58: "the transcriptome analysis was subjected to an analysis of the differences between diploid and triploid P. tomentosa" is a bit awkward and unclear. Differences in what?
Line 68: "o'clock"
Line 195: "found to be huge in triploids on branches" this is unclear
Line 197: "allotriploidy of P. tomentosa was better than diploidy" It would be better to say that the triploid had greated values of these traits. "better" implies a value judgment.

It is definitely possible that I did something incorrectly, because I'm not very familiar with the BIG database, but I could not download the raw data. However, I can see that this project is listed in the database. Someone with greater familiarity may be able to pull down the raw reads.
Experimental design: The methods as written are rather sparse, and it is difficult to get a good idea of what was done, or to understand if the protocols used are appropriate. As currently written, they would not be sufficient to replicate the experiment.

Where the trees native to the area sampled, or where they planted? If planted, is there any way to determine where these genetic stocks originally come from? Are the trees precisely one-year-old, or is there variability in their ages (and if so, how much?). How much material was sampled from each individual? The methods also appear in some cases to be out of order. Was RNA extraction done by the authors? What were the operating parameters used for data filtering and analysis? How was annotation performed? What pipeline was used (and if none was used, how was annotation done)? How was tissue culture performed on plants to be used for RT-qPCR? Although the authors do refer to other papers for some methods, a brief description of the methods (RNA extraction, RT-qPCR protocol, data processing)

Line 69: "top-to-bottom fifth leaf". This phrase is somewhat confusing, and if I am interpreting it correctly, raises a question about the protocol. Does this mean the fifth leaf down from the tip of a branch, or the fifth leaf up the stem from the base? If it means the fifth leaf down from the top, are the authors certain they sampled analogous leaves from each individual? Generally, similar experiments count leaves or nodes from the base of the plant, but it's not entirely clear what the authors did and if it was appropriate.

Line 210-213: "We compared the data of carbon fixation pathways in previous photosynthetic organisms and selected the up-regulated malate dehydrogenase (MDH) for the RT-qPCR validation, and the expression levels of MDH gene were up-regulated in triploid P. tomentosa plants, compared to the diploid ones." Which photosynthetic organisms?
Validity of the findings: The discussion and conclusions, as with the rest of the paper, are quite short, and do not spend enough time discussing the results of the experiments and how they fit into the broader literature. For example, it seems unusual that P. tomentosa would match the assembled transcriptome to such a low degree (3.26%) given that the individuals studied are supposedly P. tomentosa. The authors do not mention this in their discussion, but I feel it merits pointing out and explaining.

Although the authors do spend some time mentioning previous work on polyploids, they mainly list species on which similar studies have been done. A more thorough description of which studies found over-, under- or mixed expression would be nice, as would some discussion and speculation on the role of allopolyploidy in particular in P. tomentosa. Some discussion on if the authors think upregulation of MDH and CYCD3 in the triploids is biologically meaningful, or simply due to chance would be useful in the discussion.
Additional comments: This work is interesting, and will be useful to tree geneticists and tree crop specialists, and shows how variable gene expression can be in young tree tissues. However, the brevity of the manuscript means that a lot of useful detail and important scholarship is missing. I encourage the authors to add additional detail to the methods section in particular.


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: INFLUENCES OF HEEL HEIGHT ON HUMAN POSTURAL STABILITY AND FUNCTIONAL MOBILITY BETWEEN INEXPERIENCED AND EXPERIENCED HIGH HEEL SHOE WEARERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This study aimed to investigate the influence of heel height and high-heeled shoes wearing experience on the postural stability and functional mobility. Different heel height shoes were worn in experienced and inexperienced females to perform sensory organization test, motor control test and limits of stability test. Interesting findings were presented, however, there are still several points were not clearly clarified, and these issues should be addressed before a further recommendation could be made.

Specific comments:
1. Line 38, in the conclusions of Abstract, authors repeated the key findings of the current study, just wondering if any practical or clinical implications could be made from findings of this study.
2. Line 53-54, formatting issue, please check and revise throughout the manuscript.
3. Line 56-58, this statement is not clear, also grammar mistake, please correct.
4. Line 88-90, the statement is not clear, please rewrite.
5. Line 143-147, authors used 0-100 to define the strategy scores to quantify the hip and ankle strategy, any reference to support this scoring system, and what is the reliability and repeatability of this scoring system.
6. Line 152, the Motor control test (MCT), the test protocol is not clear from the current text description, kindly suggest adding the Figure to assist illustration of the test.
7. Line 156, how was the ‘amplitude’ scaled? By what parameters?
8. Line 198, authors presented the demographic information in the Table 2, please also include other anthropometrics, such as leg length, foot length and width, which might also affect the stability and postural control.
9. Line 286-287, it is an interesting statement here that experienced HHS wears did not show ‘better’ postural control than inexperienced wearers. Please elaborate more details on this point. And how to define the ‘better’ in postural control?
10. Line 299-301, authors mentioned more hip strategy was adopted than the ankle strategy. It is an interesting and key statement here, please discuss more on this point, as the current description is not clear.
11. Line 341-343, authors discussed that the balance control is not sensible to the body weight and height. Same as #8 comment, wondering the leg length, foot length and width may affect the postural control.
12. Line 408, how to define the ‘better’? please use academic expression.
13. Line 411, authors did not include any test or discussion on the falling risk with high heel shoes. Suggestions shall originate from the main content of the study. Please revise.


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: INFLUENCES OF HEEL HEIGHT ON HUMAN POSTURAL STABILITY AND FUNCTIONAL MOBILITY BETWEEN INEXPERIENCED AND EXPERIENCED HIGH HEEL SHOE WEARERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comments
Experimental design: no comments
Validity of the findings: no comments
Additional comments: Please refer to the attched file for details.


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: INFLUENCES OF HEEL HEIGHT ON HUMAN POSTURAL STABILITY AND FUNCTIONAL MOBILITY BETWEEN INEXPERIENCED AND EXPERIENCED HIGH HEEL SHOE WEARERS
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 made a good revision, it is suitable to be accepted now.


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: INFLUENCES OF HEEL HEIGHT ON HUMAN POSTURAL STABILITY AND FUNCTIONAL MOBILITY BETWEEN INEXPERIENCED AND EXPERIENCED HIGH HEEL SHOE WEARERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
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: EFFECTS OF CLAY MATERIALS AND MOISTURE LEVELS ON HABITAT PREFERENCE AND SURVIVORSHIP OF FORMOSAN SUBTERRANEAN TERMITE, COPTOTERMES FORMOSANUS SHIRAKI (BLATTODEA: RHINOTERMITIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: All of the main points are met. No comments.
Experimental design: No comments. All the points are sufficiently met.
Validity of the findings: No comments.
Additional comments: I found the manuscript to be clearly written, and the science overall relatively sound. I really could not find any critical issues. The one item that could be detailed better in the writing relates to use of the terms "dry" and "wet" to describe the moisture levels compared in experiments. 25% moisture is not necessarily "low" moisture, but is more intermediate, and in some ecosystem or soil types it can be the highest level encountered (e.g., sand). Better ways to refer to "dry" and "wet" throughout the manuscript would be low and high since dry and wet is less descriptive. In general I felt the experimental designs and setups were sound, and the interpretations relatively straightforward. The conclusions are appropriate based on the results. Previous reports are both acknowledged and appropriately discussed relative to the current results. I feel some minor revisions around how moisture levels are described should be sufficient to get the final paper ready 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: EFFECTS OF CLAY MATERIALS AND MOISTURE LEVELS ON HABITAT PREFERENCE AND SURVIVORSHIP OF FORMOSAN SUBTERRANEAN TERMITE, COPTOTERMES FORMOSANUS SHIRAKI (BLATTODEA: RHINOTERMITIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is fine. The English is good and there are no serious flaws with the structure or readability of the paper. I have identified below where some change of emphasis in the methods would be helpful
Experimental design: This is clear but complicated. I hope that the illustrations can go close to the methods, as a diagram is always useful for clarity.
Validity of the findings: The findings are interesting and add something useful to our knowledge of how termites move soil around. It is important, however, that a reader does not take away the impression that all lower termites move soil around. Only those that forage outside the nest do it. This means that the families Kalotermitidae, Archotermopsidae, and Stolotermitidae do not produce soil sheeting or shelter tubes.
Additional comments: A little more could be made about the choice of the minerals. At the moment, the introduction does not tell us anything about the clay minerals or their water-holding capacities. A few lines explaining why each clay mineral was chosen would help make the paper clearer


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: EFFECTS OF CLAY MATERIALS AND MOISTURE LEVELS ON HABITAT PREFERENCE AND SURVIVORSHIP OF FORMOSAN SUBTERRANEAN TERMITE, COPTOTERMES FORMOSANUS SHIRAKI (BLATTODEA: RHINOTERMITIDAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: The use of English language is appropriate. Still, the manuscript could benefit from some more proofreading and logical consistency Eg.
- check for missed articles "the Unites States [of America], China,...", with "a wooden mortar and pestle"

- use "tree vascular tissue" instead of "plant"

- "was ground"

- "(none of the termites stayed on the outer wall of the wooden cylinders or on the surface of the substrate)"

- I think you should consider citing "Oberst et al, Termites manipulate moisture content of wood to maximise feeding, Biology Letters, 15(7). 20190365. https://doi.org/10.1098/rsbl.2019.0365" since they considered similarly to you the influence of moisture levels on foraging of lower termites (Coptotermes acinaciformis).  Also, when it comes to the discussion, this paper should be discussed and the lower and upper bounds of moisture levels relevant to termites (Gautam and Henderson need to be also more discussed in this context). T. A. Evans, T. Z. Dawes, P. R. Ward, N. Lo, Ants and termites increase crop yield in a dry climate, Nature Communications 2 (2011) 1–7 provide a valuable reference for ants and termites increasing soil quality especially in more arid climate zones.
Experimental design: I think the experiment is interesting since it focuses on clay properties, but some critical considerations were not taken, and the data /information provided is not fully discussed. Central in the experiment is the choice of clay materials and the number of termites chosen as well as the consequences resulting from that. Especially the novelty of the paper – which lies in using different clay materials is insufficiently presented and the analysis is not going deep enough. The number of termites and their behaviour and ecological and behavioural consequences due to the artificial situation constructed is not discussed in the extend required.

-	Table 1 should be extended in that it is less of interest which company produces those clays, but rather what the different properties are, eg particle size, mineralisation, chemical composition and ionisation. Water retention has been reported, but then the table as well as all figures should be sorted according to the property investigated based on the hypothesis of the authors (eg water absorption)

-	Also, the number of termites seem very small in order to generate a more natural condition – certainly 400 termites are very stressed and limiting the moisture results in changed behaviour. Also, the number of termites has an effect on the moisture in turn and this changes the behaviour – hence, separating single factors is difficult if not impossible. The authors should have shown the same effect for a larger number of termites (why is colony 1 not considered in experiment A? A clear sign of stress in termites).

-	Please describe more in detail how you ensured the quality of the termites collected (I assume due to baiting only mature workers and soldiers were taken) and discuss why colony 1 in experiment A was not considered. I find the ratio very low 1 to 4 % soldiers only? This indicates to me that the baiting station was not property contacted yet (in lower termites of Cop. formosanus it is usually 5-10 % - and rather on the higher end towards 10% see  eg The proportion of soldiers in termite colonies: a list and a bibliography (Isoptera) [1977]. Haverty, M.I
Validity of the findings: I do not doubt that the results are valid, but the findings need to be very critically discussed considering the situation / context of the experiments. More validation is required with regards to the clays used and more hypothesis should be developed based on other properties than moisture only. The authors should consider running a small field trial and monitoring their results and conditions using data loggers very carefully. Also an experiment with more termites and a larger arena could be used as alternative as I believe that in practice too many factors might influence the results so that the choice of termites in terms of clays cannot be observed. However, if in the field this preference can be observed it is a very strong indication for the correctness of the authors’ hypothesis.

-	The authors discuss attapulgite and chlorite but why not bentonite? Certainly, the choice of termites is depending on the humidity levels and certain configurations have been found to be advantageous for termites (it is not ‘the more moisture, the better’ – see Gautam and Henderson (2010) or also Oberst et al (2019)).
-	The conclusions drawn that bentonite can be used when its drier and attapulgite and chlorite if moist, is flawed, since moisture and humidity levels in reality fluctuate a fair bit and vary locally as well. I question therefore the practicality of the author’s hypothesis. The authors mention in the discussion specifically attapulgite and chlorite? Why not other clay materials? Why not soils? Apart from the logical fallacies, conclusions drawn from this part seem a bit out of the blue and their connection to previous parts appears arbitrary.
-	Also, the wood consumption has not been properly discussed. The results from that part are missing in the result section and should be brought into context with Gautam and Henderson and Oberst et al. which studied in length the wood consumption under different moisture levels and in different situational context.
-	I am missing a more comprehensive discussion of other potential factors influencing termite preference in the given situation with regards to other clay properties. The authors started discussing this a bit when they mention fertility of vegetation patches in the desert, but this was not satisfactorily elaborated on.
-	Also “N. E. Carey, D. S. Calovi, P. Bardunias, J. S. Turner, R. Nagpal, J. Werfel, Differential construction response to humidity by related species of mound-building termites, Journal of Experimental Biology 222 (2019). doi:10.1242/jeb.212274. “ should be considered and discussed.
-	It should be very clear in the introduction, what is known about the influence of different clay materials; clays are also categorised according to their particle size which has not at all been discussed. The authors need to thoroughly justify their choice of clay materials. Why did they not look at also silt materials? Silt materials are often reported to be preferred over clay materials, since the shrinkage of silt is less than that of clay. Could this be related to the different purpose of using soil, clay, silt etc; of the different context (building material versus sheeting material, construction for the inner nest versus material used as outer shell etc) – this needs to be discussed, needs a foundation in the methods and then but properly introduced as well as well.
Additional comments: I believe that some of the figures are not necessary, eg 2B or 3B seem redundant (not much value in seeing the extra layer of soil in C, or better, no value in seeing the setup without the soil).  Some figures may be combined; overall the paper could be more focussed; maybe more in the form of a letter or short paper to initiate discussions about the influence of different soil types and their properties on termite foraging decisions considering different situational context.


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: RELIABILITY OF A STANDING ISOKINETIC SHOULDER ROTATORS STRENGTH TEST USING A FUNCTIONAL ELECTROMECHANICAL DYNAMOMETER: EFFECTS OF VELOCITY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Thank you for your appropriate selection of references. However, the following needs addressing for consistency:
An abbreviation must be written in full the first time it appears in the text. Line 56 requires this to be done for ICC’s, SEM or CV. Hence when described in lines 154 and 155 they can just have abbreviations. Line 67 FMD?
When using APA style of referencing (6th ed.) in text citations for three to five authors needs to be in full when first cited and then when reappears within text can be abbreviated to first author et al., date. This applies to lone 50, line 63, line 160, line 193, line 194, line 199, line 211.
The English language should be improved to ensure that an international audience can clearly understand your text. The current phrasing makes comprehension difficult from the section titled “familiarization protocol” through to the end of the paper. Other faults are detailed below:
Line 65 “Within these isokinetic devices are considered as the gold standard” does not make sense.
Line 80 “. . new technology that allows to evaluate the strength..”” is not correct English grammar.
Line 82 has numerals 4 and 3 inserted for no apparent reason.
Line 83 “ has been not studied yet”  should read “ has not been studied yet”.
Line 89 “ . . for the assessment of isokinetic test.” An assessment is a test??
Line 91  delete “low speed would be more reliable….”as this is hypothesis (II).
Line 97  Should read “ Thirty-two asymptomatic male volunteers’. . . . “
Line 99  remove” s” from dynamometers.
Line 108   remove “s” from rotators.
Line 109  add “s” to session
Line 111  remove “s” from protocols
Line 119 add “d” to couple
Line 294  Strength is spelled incorrectly.
Experimental design: The introduction must include further background for the reader regarding the equipment used for this study, being the Functional Electromechanical Dynamometer. I suggest you expand on the description/background of your device. Currently, there is only one sentence reporting this in Line 80 “new technology that allows evaluation of the human being in the  Functional Electromechanical Dynamometer (Dvir & Muller, 2019), with only isometric strength of the shoulder rotators and hip abductor strength previously studied."

As the reviewer of this manuscript I then read the reference provided by Dvir and Muller, 2019 and established the following:

"These dynamometers typically consist of an electrical motor coupled to a linear transmission, which moves a slider with footplates or special handles. For dynamic action, MIDs (Multiple joint Isokinetic Devices) enable either concentric or eccentric exertions, and the basic input parameters are therefore the range of motion (in millimeters or centimeters) and the velocity (in m per sec or cm per sec), whereas the main output parameter is the peak force (PF) in Newton (N). Multiple-joint isokinetic dynamometers are used especially for testing and conditioning of coupled ankle-knee-hip extension, known as leg press (LP), coupled shoulder flexion and elbow extension (or their reciprocals), and its reverse action, known as bench press (BP) and vertical lifting.
It appears the device used in this study is:  referred to as the unconstrained design, provides concentric or eccentric resistance to a free, multiarticular whole-body motion, using a cable or a rod without providing proximal stabilization. The stand-alone cable variant, manufactured by Haefni Health Systems (Granada, Spain), incorporates a spool around which a cable is wound. In concentric exertions, the cable is normally drawn away from the spool, whereas in eccentric actions, the opposite cable spool motion is taking place."
Validity of the findings: Thank you for the appropriate use of test protocol and statistical analysis. However, further detail is needed in the methods section of your paper to make clear to the reader the validity of your findings.
As the reviewer of this manuscript I read the reference provided by Dvir and Muller, 2019 and established the following:

"By virtue of their design and operation, MIDs offer a more functional approach. Nevertheless, users of MIDs should be aware of the implications associated with scaling, specifically that a constant linear velocity will not result in a concomitant constant angular joint velocity and therefore a simple comparison is not valid. Furthermore, for the same linear velocity, people of taller stature will experience lower angular joint velocity compared with their shorter counterparts and thus, as far as concentric efforts are concerned, strength capacity might be overestimated in taller athletes or patients. However, this discrepancy is especially pertinent to the issue of reference values (norms), where strict uniform testing and conditioning must apply to all participants. Given the generally high reproducibility of MID-derived findings as indicated by well-conducted studies, ensuring same input parameters such as RoM, velocity, and participant positioning should be quite sufficient for valid data interpretation in terms of bilateral differences or changes in the course of rehabilitation or training. By contrast, inter-individual comparisons will require consideration of the previously described limitations."

Therefore, confirmation of the following is required to confirm the validity of the findings:

Why is “the pulley system and subjection system of own manufacture” – detailed under Instrument. This greatly affects the validity of these findings. Are they the same as those used in the previous studies quoted looked at isometric shoulder testing and hip abduction testing?

Why were the subjects positioned standing or sitting to determine range of movement when all testing was performed in standing. This raises the concern that variances in height of participants has skewed the results.

A 90 minute period of familiarization seems excessive. Although the participants recruited had no experience in the use of dynamometry, this time allows each participant to have learned and practised the required tests to an “expert” level.

Dvir and Muller (2019) report this "functional electromechanical dynamometry is for testing coupled movements such as shoulder flexion and elbow extension (otherwise known as bench press)". Why then was only shoulder rotation reported?

Interestingly, when citing previous isokinetic dynamometry studies which used the standing position they were thirty years ago whereas studies cited for supine and sitting positions are within the past ten years. This raises the question of why standing has not been continued as a testing position.
Additional comments: Thank you for your well constructed reliability study, with appropriate test protocol and statistical analysis, even though it has very limited external validity. Before considering this manuscript as suitable to be recommended for publication , you need to substantiate the validity of your study by further explanation on the equipment used and  explanation on 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: RELIABILITY OF A STANDING ISOKINETIC SHOULDER ROTATORS STRENGTH TEST USING A FUNCTIONAL ELECTROMECHANICAL DYNAMOMETER: EFFECTS OF VELOCITY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language could be improved.
The introduction demonstrates how the work is related to the broader field of knowledge.
The structure fits the Journals' instructions.
Although the figures are relevant to the content, some important information (which could be presented as figures) are missing.
Row data have been made available.
Experimental design: The presented research fits the Journals' scope.
The research question is limited to the reliability of the novel device, without previous information about the concurrent validity. In addition, test-retest has been explored without providing information about within-session reliability.
Some parts of the methods sections should be presented in more detail (see general comments)
Validity of the findings: The impact and novelty of the study are limited (see general comments).
The conclusions are questionable (see general comments).
In some part of the discussion, speculations are made without evidence based on the presented results.
Additional comments: GENERAL COMMENTS
Thank you for the opportunity to review the manuscript entitled “Reliability of a standing isokinetic shoulder rotators strength test using a functional electromechanical dynamometer: Effects of velocity”. The authors aimed to determine the absolute and relative reliability of concentric and eccentric internal and external shoulder rotators with a functional electromechanical dynamometer (FEMD). They concluded that all procedures examined showed high to excellent reliability for clinical use. They recommended that the velocity of 0.60 m·s-1 should be used for asymptomatic male patients because it demands less time for evaluation and patients find it more comfortable.
The topic addressed in the manuscript is relevant to the journal’s readership. Although the structure of the manuscript follows the Journal instructions, the main limitation of the article is related to the fact that the reliability of the novel device has been explored without prior reports regarding its validity. Also, within-session reliability was not explored.
SPECIFIC COMMENTS
Abstract
Line 22: In: “… relative reliability of concentric and eccentric internal and external shoulder rotators …” should be changed to: … relative reliability of concentric and eccentric internal and external strength of shoulder rotators …”
Introduction
Line 43: The first sentence seems to be incomplete: What is periodically assessed?
Line:
Methods
Since the main aim of the article was to explore reliability of the novel device, the figure of the test setup, as well as the signal profiles (force, velocity and angle over time) through the range of motion and at various constant velocities, are necessary to illustrate the factors (biomechanical conditions) which could affect the strength measures and therefore the explored reliability.
Line149-150: “The three highest repetitions of the mean force for the concentric contraction and for the eccentric contraction were taken to calculate the dynamic force.” Please explain how the dynamic force was calculated (average?).
Results
Please elaborate results in more details.
Discussion
The findings regarding systematic bias are not discussed.
Line 188-189: The position could not be reliable, only the test outcome obtained in a certain position.
Line 197-202: This is an interesting point. However, due to a large number of degrees of freedom, without fixation, it’ hard to isolate muscles responsible for the specific movement. Please comment.
Line 202-207: See the general comment regarding the validity.
Line 209: At the beginning of the sentence please substitute “Other” with “Second”.
Line 209-222: One of the main advantages of the isokinetic dynamometry in general, is the ability to assess partly independent mechanical qualities of the tested muscle through the range of different constant velocities (Van Roie et al. 2013, Grbic et al 2017). Therefore suggesting the application of only one condition due to higher reliability (although the authors are claiming that other application of other velocities are highly reliable) is questionable.
REFERENCES:
Van Roie, E., Bautmans, I., Boonen, S., Coudyzer, W., Kennis, E., & Delecluse, C. (2013). Impact of external resistance and maximal effort on force-velocity characteristics of the knee extensors during strengthening exercise: a randomized controlled experiment. The Journal of Strength & Conditioning Research, 27(4), 1118-1127.
Grbic, V., Djuric, S., Knezevic, O. M., Mirkov, D. M., Nedeljkovic, A., & Jaric, S. (2017). A novel two-velocity method for elaborate isokinetic testing of knee extensors. International journal of sports medicine, 38(10), 741-746.


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: RELIABILITY OF A STANDING ISOKINETIC SHOULDER ROTATORS STRENGTH TEST USING A FUNCTIONAL ELECTROMECHANICAL DYNAMOMETER: EFFECTS OF VELOCITY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Thank you for taking the time to edit your original submission. The English language is much improved. Detail on the equipment used and methodology is now clear and succinct.


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: RELIABILITY OF A STANDING ISOKINETIC SHOULDER ROTATORS STRENGTH TEST USING A FUNCTIONAL ELECTROMECHANICAL DYNAMOMETER: EFFECTS OF VELOCITY
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have improved the manuscript substantially.
Experimental design: All details regarding the experimental design are sufficiently addressed.
Validity of the findings: The findings are well stated and linked to the results and the research question.
Additional comments: No further 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: OPTIMISED BIOMOLECULAR EXTRACTION FOR METAGENOMIC ANALYSIS OF MICROBIAL BIOFILMS FROM HIGH-MOUNTAIN STREAMS
Review round: 1
Reviewer: 1

Output:
Basic reporting: An interesting and important study! This manuscript was well written and organized. I do like the work, but I think this manuscript would benefit from revisions on figures, especially.
Experimental design: The experiments were well designed.
Validity of the findings: Generally good. The figures can be improved a little bit to clarify the results. Referring to the comments below.
Additional comments: L22: “GFS ecosystems”
L114: add “,” after "abundance"
L135-150: some of the tenses were wrong, which should be past tense.
L218: delete “of”
L239: delete “in”
L252: change “extracted” to “extractions”
L278: delete “were observed compared”
Figure 1: it is better to add the significant difference results in the plot using different letters, stars, or just P-values, or like Figure 6a. Moreover, it would be good to briefly explain what the methods -1,2,4 are, so the readers can understand the figure without referring to the main context.
Figure 2: briefly explain method-4.
Figure 3: is this figure really necessary? Or combine this figure with others?
Figure 4: it is weird to have a table in a figure. It is easy to convert the table as annotations in the figure.
Figure 5: (1) there seems no reason to use different plots in figure with boxes and bars together. You can use either one. (2) the variables’ name is better to show on the top of the plot not on the X-axis like Figure S1. The legends (extraction methods) can be added to the X-axis.