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: GLOBAL MARINE BIODIVERSITY IN THE CONTEXT OF ACHIEVING THE AICHI TARGETS: WAYS FORWARD AND ADDRESSING DATA GAPS
Review round: 1
Reviewer: 1

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: Comments to ms by Saeedi et al. (see also annotated manuscript):

General evaluation: This manuscript explores the different strategic goals of the AICHI protocol for biodiversity discovery and prediction. In general, this can probably be a useful overview, offering some suggestions for future research and conservation strategies. However, during my reading I had the impression that the treatment of the different priorities/goals is a bit superficial and subjective – there might be options to overcome this by using some approach (see below) to make this a bit more objective (keeping in mind that there will always remain some subjectivity in this kind of forum pieces). Additionally, I think that it would be good to characterize this piece from the outset as a forum or opinion piece – possibly this could be highlighted in the title.

A general impression: from reading the different sections on the 8 research priorities, I had the feeling that the evaluation about achievements was that in many cases things were in poor or (maximally) fair state, but then in the final conclusion sections the authors say “we judge seven have seen fair to good progress”. Clearly, my impression after reading the sections maybe as subjective as the judgement by the authors. It would be really good if the authors made an attempt to make these evaluations of the 8 priorities/goals a bit more objective. I think they could define several categories (e.g. very poor, poor, fair, good, very good, excellent) and then for each of the 8 priorities/goals conclude each section by saying something like e.g. “Based on the above considerations and criteria, we evaluate that the achievement of this priority/goal is fair.” And then, in the final conclusion section, they could provide an overview table that summarizes all these judgements. I fully understand that a rigorous and objective evaluation would probably be a major task and would go beyond this overview, but I do think that there are some options to achieve a somewhat more objective approach. As expressed in this paragraph, there is some contrast between the reading and the concluding judgement, and an effort should be made to avoid this apparent contrast.

I would also recommend to place a bit more emphasis on coastal zones in areas of the world’s oceans that continue to be very poorly studied. In many parts of the world our knowledge of local (coastal) biodiversity is poor, and there are many obstacles to improve that situation (economical, political, taxonomic expertise, etc.) and that should be highlighted, especially given that most anthropogenic stressors severely impact the coastal zones. While the mentioning of the deep sea gaps and threats is certainly important, a better balance between deep sea examples and mentioning of poorly studied coastal zones would be good.

Also, I would be more cautious with painting MPAs as the panacea for conservation of marine biodiversity. There are certainly some success stories, but there are many other examples where MPAs actually cannot provide sufficient protection against external threats. The authors later acknowledge this when they talk about coral reefs, but some warning statement should also be included in the section where they emphasize the usefulness of MPAs.

Finally, I would encourage the authors to include at least a brief statement about the power of citizen science (see also comment in annotated manuscript). There are many examples how citizen scientists are contributing to a better knowledge of local marine biodiversity. Also, the power of this approach in engaging many members of the general public in the conservation of marine biodiversity could be mentioned.

In summary, the manuscript may be very timely, but it has ample room for improvements. Furthermore, it probably should be categorized from the outset as a forum or comments piece (in the title), to immediately distinguish it from a hard-core research paper. Incorporating my suggestions will require some time and effort, but it will make the paper much more powerful thereby ensuring that it will have a much stronger impact.

Finally, I hope that my comments will be helpful in improving the manuscript. In case of any questions concerning my comments, I invite the authors to contact me directly.

Sincerely, Martin Thiel, Facultad de Ciencias del Mar, Universidad Católica del Norte, Larrondo 1281, Coquimbo, Chile; email: thiel@ucn.cl

ps: i just notice that i can only upload the PDF of the annotated manuscript to the PEERJ website - i would be happy to provide the annotated word document any time - just send me an email.


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: GLOBAL MARINE BIODIVERSITY IN THE CONTEXT OF ACHIEVING THE AICHI TARGETS: WAYS FORWARD AND ADDRESSING DATA GAPS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the abstract reflects the text of the paper well, but needs some careful editing.  There is one issue with the framing of the problem, which implies a fundamental misunderstanding of the objectives behind the Strategic Plan for Biodiversity and the Aichi targets.  These are global targets for action rather than simply analytical targets for studies.  Some reframing of the abstract will correct this.

The paper has been written by multiple authors and could do with some careful editing for language and consistency.
Experimental design: Line 65 - This makes no sense as drafted.  They are global targets, so need to be met by the global community.  Reporting to the targets is carried by countries who each contribute through their national biodiversity strategies and plans.  Scientists certainly play an important role and feed into that process by undertaking studies that contribute to reporting and developing indicators to inform the targets.  But scientists can't 'meet' the targets per se.

Line 72 - The focal areas identified in the paper are indeed key areas that need further focus, but these underpin many more of the Aichi targets than set out in Table 1.

Also it is important to view the targets alongside the indicators used to measure them if the aim is to understand the status of achievement through a scientific lens.  Some aspects may be achieved, but we simply don't have the data to show that, or as in the case of target 11 we are basing achievement on only a subset of the target!
Validity of the findings: Throughout the paper there is some confusion over the correct terminology for the 'Strategic Plan for Biodiversity 2011-2020', and also the purpose and ambition of this global plan.  Suggest the addition of a co-author with expertise in this area.

The summary of the discussion topics is very interesting and a useful contribution to the scientific literature.  However, I think the framing as a response to Aichi targets is unconvincing.

While stated as a paper that discusses the achievement of the Aichi targets, the link between the targets and measurable indicators is absent from the paper.  Indeed to link form the focal areas to the targets feels like an afterthought rather than an integral part of the study design.
Additional comments: Overall there is useful content in this paper that should be published.  However, it has been framed poorly as a response to delivery of the Aichi targets and in this is fails.

The paper is based on a discussion group at the 4th World Conference on Marine Biology.  The group identified 8 focal areas for further discussion.  The focal areas seem to have been arrived at as focal areas for future research and development areas.  It is not clear how they linked to the Aichi targets during this discussion.

In the paper they review each of the focal areas, but the connection to the Aichi targets feel much like an afterthought and not part of the core study design.  Indeed there is no mention of the indicators that are used to measure the Aichi targets, which would seem a critical area for the authors to review if they are looking at how best to measure and achieve the targets for the focal areas.

I would like to see the authors rethink the framing of the paper.  Instead focus on how the reviewed priority areas could be better reflected in the Aichi targets.  It would be very useful to use the results to propose new indicators and ways of measuring progress.  This can then make a clear link to the drivers of positive change.  This would be a very worthwhile contribution to the literature, and timely given that the targets will likely be revised in 2020 and there is a strong drive to make the post2020 targets more measurable.


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: SOIL AGGREGATES INDIRECTLY INFLUENCE LITTER CARBON STORAGE AND RELEASE THROUGH SOIL PH IN THE HIGHLY ALKALINE SOILS OF NORTH CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is written quite well, easy to read and follow and with little errors. References are extensive. Figures and Tables are well presented in general, although I think that Figure 1 is very busy and the repetition of the legend is not needed and distracting. I don't think that relationships Figure 6, except maybe SOC and pH although I have issues with the small pH range, and the interpretations that can be made form this. The links to hypotheses in the discussion are somewhat speculative, and not directly linked with data (exudate quality, microbial community and range of pH is averaged across aggregate size which is confounding).
Experimental design: The experiment itself is quite detailed and well executed I think. The level of measurements and amount of data and synthesis of this is quite good and detailed. My main concerns are related to the initial aim of the study, the litter treatments (the fundamental reason for looking at the different combinations or types), their little difference in C:N (only 23.95-29.66, which would all require external N for mineralisation/decomposition) and the little range in pH (0.5 pH units), and the fact that the effects of pH are assessed by pooling aggregate size classes.
Validity of the findings: Residue type is largely ignored in the discussion but is one of the treatments.

I question the size of the litter fragments (1 cm long), the length of the incubation (56 days) and whether these are conducive to allow these to decompose sufficiently and interact with smaller aggregate size classes, which essentially biases the moderate size class (1-2 mm).

Much of the discussion is speculation and individual examples are outlined below in general comments.
Additional comments: microbial activities - this needs to be considered a single parameter, the contribution of components of the microbial community cannot be analysed separately, and as such it is one, microbial activity.

It is not clear whether leaf and stem were also dead? all are essentially standing biomass? the terms and description are confusing. is all (treatment 3) a mixture of the other 2?

Maybe it would be better to show the bar charts as values of each treatment relative to the corresponding CK? it is often difficult to see whether there has been relative effects of the treatments or these differences are all proportional to the original CK.

False wheatgrass/chinese ryegrass? the common name and relevance of the plant should be added.

The term quickly is subjective.

Add the rate (1.5% w/w or similar). First paragraph pf the M&M could be condensed.

How did you measure and maintain 90% RH?

After the stabilization period? this implies something different occurred in the second phase but essentially you did nothing different?

The start of the second paragraph repeats reps and treatments etc and is not needed.

Cleaning litter with water? didnt you lose C and N?

Soaking with HCl using auto analyser? this needs more detail on thew size, concentration and amounts of acid and materials.

Headings of M&M and results are too interpretive and should just be descriptive. The are more fitting for a discussion.

Why did you do the one-way ANOVA? you need to have some justification here? because of the large effect of litter ? but you don't mention this is the discussion?

Spaces between numbers and units (mm) are not consistent.

The first sections of the results just state significant effects and do not have good comparisons of the relative effects. The section on pH is done much better (% differences, X times more than Y etc)

CO2 accumulation, may be better as cumulative CO2?

Higher mass loss, more CO2 emissions BUT higher CO2 storage. The concentrations not easily digested and understood. Essentially this means that other treatments had less mineralisation and greater amounts of the added materials remaining as undecomposed plant fragments?

Line 52, you are speculating but you have the data?

Line 160 et al. I don't understand the acidification that has occurred in the litter-amended soils? this process is usually an alkalinising process? This needs some explanation? at this pH nitrification should not have been inhibited so the reason for a net increase in pH is unclear?

Mass loss rate is an odd term since only two time points and presented.

L184, I find it interesting that you only consider two aggregate size classes here and ignore the finer size classes. 184-186 is all speculation and not based on your data.

L199 implied. speculation.

L205. what does heterogeneous distribution of the microbial biomass mean here? this section is on soil pH? you didn't test the soil pH value difference in aggregates? (i.e. you don't have a range of pH values within each aggregate class and you didn't set up an experiments to test this). therefore your pH range is confounded by pooling the different aggregate size classes. I don't see the value in the next section (L208-210) where a correlation is derived from such a little delta in soil pH (only 0.5 pH units). All are mildly alkaline. The figure is very messy. Kemmitt had a much greater range of pH values and it is therefore not surprising they got as different relationship (L216).

What is the relevance of reducing conditions to the current study (L219).

L224, which is the most favorable for litter decomposition and soils C storage? for your data and I think that this is confounded by the fact that not a sufficient amount of time has occurred for 1-cm leaf fragments to get into these smaller size fractions.

Much of the conclusions make some bold statements from an experiment of the narrow pH range etc Similarly, suggesting that microbial community and its composition are drastically changed by the pH shifts are not valid I don't think.

If you consider the relative differences between pH are smaller than the CK's. Actually the 0.25-1mm aggregate size has had the greatest relative change in soil pH, then maybe the <0.25 and these effects are overlooked.


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: SOIL AGGREGATES INDIRECTLY INFLUENCE LITTER CARBON STORAGE AND RELEASE THROUGH SOIL PH IN THE HIGHLY ALKALINE SOILS OF NORTH CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Improve the English language carefully, where needed (see some comments below)
Experimental design: The experimental design is okay and research questions are well defined.
Validity of the findings: Novelty is also okay; the conclusion part needs some improvement such as linking the messages to the key research questions.
Additional comments: Reviewing Manuscript 38613v1

This is an interesting study where the authors examined the role of soil aggregate size classes and their interactions with different types of litter on carbon storage capacity in soil. The manuscript is generally well written and the listed questions in ‘Introduction’ are well explained (as per the findings of this study), but there is a need for further improvements of the whole manuscript. The authors need to make the right use of articles, plus to also fix a few grammar issues. There are a few issues with some figures, which should be clarified/improved in a better way. All (sub)-sections and many figures of this manuscript are mostly okay but the authors need to address some of the issues before the publication of this manuscript in PeerJ (see some specific comments below).

Specific comments:

Improve the title of this manuscript: for example, clarify the meaning of “through soil pH”.

Abstract

Line 11: The authors mentioned microbial activities but these were not examined.
Line 13: Change ‘is’ to ‘are?
Line 17: Clarify that this is the “Litter mass loss rate”.
Line 17: The authors should present the data and statistical outcomes of Cr and Cs in relevant figures; see below.
Lines 24-25: What would be the broader implications of these results (CO2 release and litter C storage) from the aggregate size classes (macro- vs. micro-aggregates), while considering these results are from one soil type only; clarify.

Introduction

Lines 44-46 and then Line 48: Yes, this is important with growing evidence, but why the authors are talking about “decomposer community composition”; their research results did not present any data on microbial activities/community composition, etc.

Lines 56-57: What do the authors mean by “higher conversion capacity”? Clarify.

Material and Methods

Line 77: Change ‘dry sieve’ to ‘dry sieving’.

Line 82: As the authors may know, there would be some reasonable quantities of silt (<0.053 mm) and clay (< 0.002 mm) particles in less than <0.25 mm micro-aggregates, which would still not be aggregated as micro-aggregates (<0.25 mm) and micro-structures (<0.053mm). These data need to be evaluated and reported, or at least to say that “micro-aggregates (<0.25 mm)” will also have silt-plus-clay particles and micro-structures. Then after clarifying this, they can classify all these size classes as “micro-aggregates” for reporting in this study. Look at some relevant published studies and cite those.

Lines 97: Hope the authors would have added the plant litter in each soil aggregate after the pre-incubation period for three days. This is a usual approach and is important. Clarify.

Lines 103-104: Improve the message here.

Line 119: Is there any reference where previous incubation studies may have used this carbon storage capacity approach (i.e. Cs/Cr) over only two months? Cite a couple of those studies.

Lines 125-126: Why this statistical approach (one-way ANOVA) was also done? Clarify or remove this sentence. This best approach is the two-way ANOVA, which is already mentioned above (Line 124).

Results

Lines 142-144: Clarify/explain the significant differences for the other aggregates size classes also.

Lines 148-150: There are a few issues. Fix citations of the right Figures for different statements; remove the irrelevant ones. The data presented in Figure 3 are just the SOC concentrations but not the storage; hope the authors can also present the SOC storage data, which is Cs (SOC in litter treatment minus SOC in the control treatment). Was the SOC storage really high in 1-2 mm aggregates? If the authors can also present the Cs data in relevant subfigures, then it will be clearer for the readers. There is also a minor grammar issue here (and also a few other places; carefully improve the manuscript while fixing similar English grammar issues).

Line 152: Is the impact of soil aggregate size and litter type interaction really significant on the Cs / Cr ratio? This is not right as per the statistical results presented in Table 2 for the Cs / Cr.

Lines 160-161: This information does not seem to be provided “significantly lower mean soil pH”?

Lines 168-170: Fix any minor English grammar/language issue.

Discussion

Line 174: Change to “Soil aggregates regulate”

Lines 185-187: Improve the flow of this message here (Seems the sentence is not complete and not clear) so the readers can understand.

Line 188: Why saying “affected”

Line 193: Did the authors examine and report sand, silt, and clay contents in each aggregate size class; this information will be useful.

Lines 199-200: Clarify this information here, and in Figures 2 and 3; the results presented here are just the litter treatments and controls but the data and statistics are not presented for Cr and Cs values (for example, after subtracting the control SOC from litter SOC and then litter C storage (Cs) and their statistical results will be clearer for the readers.

Lines 204-205: Clarify and improve this statement/message. Then fix some minor English issue (e.g. at Line 205).

Lines 214-216: Improve the message and the English language flow here. What do you mean by “both soils”; this study only looked at one soil but then different aggregate size classes.

Lines 225-226: This study is about aggregate size classes and the information on microbial structure and diversity in soil aggregate size classes needs further studies, although some work has been done; carefully look at the literature and improve the flow of the message here and cite those new studies.

Conclusions

I feel the conclusion section would only briefly mention the key results but the messages need to be linked well the questions/hypotheses developed in this manuscript, for example, in the Introduction section.

Line 229: clarify that the mass loss was related to “litter mass loss”.

Line 231: Change CO2 accumulation to CO2 release.

Lines 236-237: Mention implications of these future work for SOC storage; of course the microbial diversity will change with changing pH, but it is important to link soil microbial abundance/diversity with SOC storage/release at different aggregate size classes, and more of this work is needed in future research activities. Clarify this information for future work.

Table 1: Did the authors also analyze inorganic C content in all aggregates?

Figure 2: Cumulative CO2 data for both litter treatment and the control are also presented in Figure 1 (g, h, i), including for days 28 and 56. It would be better to also present Cr (CO2 from litter minus CO2-C from control) and their statistical comparisons. Ditto for Figure 3 (Cs = SOC-L minus SOC-CK); present these data also (i.e. Cs).


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: SOIL AGGREGATES INDIRECTLY INFLUENCE LITTER CARBON STORAGE AND RELEASE THROUGH SOIL PH IN THE HIGHLY ALKALINE SOILS OF NORTH CHINA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article has some issues with clarity and language. Please see my points below:

Please see general comments for all Review points.
Experimental design: I think the experimental design is ok, however, I have some concerns about drying soil aggregates as this may effect microbial composition, abundance and activity. This may be a standard method, however, can you please provide a suitable reference or further explanation.

One major component of the experiment is to measure how much plant litter is incorporated into each aggregate fraction microcosm. This goal needs to be made clearer. To do this please replace 'mass loss' with 'litter mass loss' or 'litter mass incorporated'.
Validity of the findings: The main findings are that macroaggregates (1-2mm) incorporated that greatest amount of leaf litter (i.e. litter mass loss was greatest) and the macroaggregates had the highest CO2 accumulation and release. These findings need to be made clearer in the conclusions. Specifically, the author needs to correct the error where they say '. . . 2mm aggregates had the highest CO2 accumulation (Cr)'. This is an error and contradictory as Cr is C released. Instead the author needs to write something like, 'Moreover, the 1-2mm aggregates had the higher CO2 accumulation (Cs) and loss (Cr) for all treatments, while the 0.25-1mm had the lowest'. That is if this is true also for the 0.25-1mm.

The author also needs to state in the conclusion that C storage in response to leaf litter is greater than C released within the soil macroaggregates and point the reader to the graph (Fig. 4) which shows the ratio of Cs/Cr.

An understanding that macroaggregates can increase SOC content has validity when trying to understand how to manage soils for increased C sequestration. A similar conclusion needs to be made in the paper.
Additional comments: Review of paper: Soil aggregates influence litter carbon storage and release through soil pH

1.	Line 13. The Background section of the Abstract does not provide enough context to allow the reader to understand what the paper is going to be about. My suggestion is to add a sentence after that says something like, ‘Here we ask how four different aggregate sizes influence rates of C release (Cr) and SOC storage (Cs) in response to three types of plant litter added to an ungrazed natural grassland. The remainder of the abstract needs to be amended as appropriate to avoid duplication.

2.	Lines 19 – 25. The Results section should be written more simply to focus on the main messages in relation to the hypotheses set. This should say something like: (i) A significant negative relationship was found between Carbon stored (Cs) / Carbon released (Cr) and soil pH, and (ii) Macro Aggregates (1-2mm) had the highest CO2 release and accumulation rates of all treatments.

3.	Line 39. After low lignin content, consider adding, (i.e. low C-to-Nut ratio).

4.	Line 46. Remove the word ‘controls’. I think the sentence can end at litter quality.

5.	Line 46. I don’t understand the sentence, ‘Soil microbial processes are regulated by constraints in soil pH . . . ‘. Please explain further. It is true that soil pH is a main factor regulating soil processes, including plant and microbial activity and composition with effects on soil aggregate stability and development.

6.	Line 50. I don’t like the sentence, ‘Soil aggregates are structural units of physical barriers . . . . . ‘. I think it should be worded something like, ‘Soil aggregates provide physical protection of contained SOC and nutrients which can change the rate of C and nutrient cycling’.

7.	Line 53. I think an explanation needs to be added at the end of the following sentence, ‘SOC mineralization in macro-aggregates is considered to be higher than micro-aggregates (Fernandez et al. 2010; Rabbi et al. 2014), because . . . . ‘. Please see Six et al. (2004) (already in your reference list or Stamati et al. (20013) for an explanation. Stamati’s paper is titled, ‘A coupled carbon, aggregation, and structure turnover (CAST) model for top soils’.

8.	Line 64. Change to something like: ‘(i) soil aggregate size and pH are correlated and effect rates of litter decomposition’. Delete consequently. For hypothesis (ii) change to something like, ‘macro aggregates will have higher litter C concentrations than micro aggregates, despite greater losses of carbon.

9.	Line 74.	Change to the soils were spread.

10.	Line 76. Change the sentence to something like, ‘Soil aggregates were separated into different size fractions by dry sieving in accordance with the method in Elliott (1986).

11.	Line 86. Change Ca. to Ca. (Italics). Acceptable without so up to you.

12.	Line 93. Change to ‘. . . was used as a control (CK).

13.	Line 141. The sentence is written for an introduction and not for the results section. Please change to something like, ‘Soil aggregate size, litter type and their interaction has significantly influenced mass loss, CO2 release and SOC concentration.

14.	Line 144. Change to ‘In all three litter addition treatments, . . . .’

15.	Line 146. Change to, ‘. . . . . remaining decomposition for all the four aggregate sizes. The ‘s’ needs to be added.

16.	Line 150. Add the words, ‘the’ and ‘fraction’ to the sentence so it reads, ‘. . . . was highest in the 1-2mm aggregate fraction.

17.	Line 178. Change the sentence to read, ‘. . . significantly higher rates of loss occurred in soil . . . . ‘.
18.	Line 179. Change the sentence to rear, ‘This may be because of greater contact with air filled pores and microorganisms . . . . ‘.

19.	Line 180. Consider changing the sentence that begins on line 180 to read as follows, ‘The study by Jha found that the CO2 released from soil aggregates increased with increasing size class (i.e. 2-4mm > 1-2mm > 0.5-1mm > less than 0.25 mm; Jha et al. 2012). The results of this study generally concur with these findings, however, macro-aggregates (1 – 2mm) released more CO2 than large macro aggregates (2-4mm).

20.	Line 192. Add the word, ‘the’ to the following sentence, ‘ . . . . . aggregates has the lowest SOC concentrations.

21.	Line 194. Add the word, ‘the’ to the following sentence, ‘Hence, the low content of SOC in the smaller aggregate size class . . . ‘.

22.	Line 195. Remove the end of the same sentence. Remove, ‘than <0.25 mm aggregates’. I don’t think this is required.

23.	Line 232. Add the word, ‘negative’ to the following sentence, ‘In addition, significantly negative relationships were . . . . ‘.

24.	If possible, carry out a mass balance to understand if rates of CO2 release in macro aggregates are > or < then rates of C storage.

25.	The results of this paper show a negative relationship between pH and SOC etc. This is contrary to many papers that show a positive liming effect on C and N pools e.g. Egan et al. (2018), ‘Effects of long-term grassland management on the carbon and nitrogen pools of different soil aggregate fractions’. Could the difference be mineralogy and interaction of lime (CaCO3) with clays?? This needs to be included in the discussion.

Tables and Figures

T. 1.	Add the word initial or similar so the reader knows what data this table relates to, ‘i.e. Initial mean . . . ‘
T.2.	I do not understand this table. The description says it is aggregate size and litter type v. the other variables (Mass loss, CO2 release rates, SOC, Cs/Cr). If so, why is there only one size and one type?

Shouldn’t the graph look like the attached PDF

Overall I think it is a good paper. However, the authors need to decide what are there key messages and structure the paper accordingly.


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: SOIL AGGREGATES INDIRECTLY INFLUENCE LITTER CARBON STORAGE AND RELEASE THROUGH SOIL PH IN THE HIGHLY ALKALINE SOILS OF NORTH CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: All fine. Thorough revision. Think that the manuscript is acceptable for publication with some minor revision.
Experimental design: All fine. Thorough revision. Think that the manuscript is acceptable for publication with some minor revision.
Validity of the findings: All fine. Thorough revision. Think that the manuscript is acceptable for publication with some minor revision.
Additional comments: Thorough revision. Think that the manuscript is acceptable for publication with some minor revision.

Comments/suggestions.

L40. decomposer activity? Composition and activity of the soil decomposer community?

L53. The word contained is not needed I don’t think.

L57 maybe higher should be greater? (mineralization)

L58 a reduced microbial activity? ‘a’ is not needed.

L63. Litter decomposition capacity of carbon ... needs rewording.

L101 chemical properties?

L111 before adding litter?

L113 pre incubation period?

L122 shaking soil with water (1 :2.5 w/v) for 30 min.

L129 Burette?

L136 please insert a space between 1 and indicates.

L138 zone? Not clear what you refer to here.

L148 chemistries? Better to say that the initial chemical composition of all three litters differed substantially. Place a space between 1 and Table.

L156 C/N ratios were higher?

L166 then a decrease is misleading, since the rate slowed from the initial rapid rate but didn’t in-fact decrease

L171 can’t have concentrations (plural), with the and was (singular)

L174 too many spaces between pH         and carbon

L175 can is not the right word here as it is speculative, but you are using actual data.

L176 has ‘the’ highest

L183 decreased the pH in the soils than the same soils? This suggests that the drop in soil pH was the same with and without litter? Then this is not an effect of the litter? But the data show that the drop in pH is the same for all aggregate class sizes?

L201 chemical composition of the litters?

L203 decay not decays.

L206 compared with.

L209 the use of the refence here suggests that the statement is based on their data (Jha) and not yours also, it needs a conjunction I think as the statement is for your data but also shown by Jha? Have I interpreted this correctly?

L216 The explanation is that there is a greater size (microbial biomass) and diversity of the microbial communities in macro-aggregates?

L218 significantly affected SOC concentrations

L233 The different values of soil pH

L237-247 this whole section about soil pH and SOC mineralization only refers to one reference but there are others that have explored this phenomenon. E.g.  Grover, S.P., Butterly, C.R., Wang, X. et al. Biol Fertil Soils (2017) 53: 431. https://doi.org/10.1007/s00374-017-1196-y

L254 significant negative quadratic relationships? Also change in other places.

L265 greater instead of higher?

L268 were correlated? Significant negative relationships?

L271 greater litter C storage capacity

L275 in different aggregate size classes? And further research in this area is needed?

I still feel that the repetition of the legend on Fig 1. Makes it too busy and they are not needed on every single panel. The Editor should advise on this.


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: T1000: A REDUCED GENE SET PRIORITIZED FOR TOXICOGENOMIC STUDIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, Soufan et al. used a systematic approach to identify 1000 genes (T1000) highly responsive to chemical exposure using microarray data from the Open TG-GATEs program. The authors then compared the performance of T1000 to that of previously published gene sets (L1000, S1500, gene list from Limma, and a random set).
The manuscript is generally well written, and provides adequate background/literature review supporting the need of further studies aiming at building models to predict toxicity. Yet some major concerns remain.

1. When referring to the datasets used in the study, GEO Accession numbers should be provided in the main text (i.e. lines 134-137) as well as included in table 1.

2. The figure legends should be more exhaustive, to allow the reader to understand the main content of all the figures/tables without coming back to the main text.

3. Table 2 has not been discussed in the manuscript.

4. In the legend for figure 4, the abbreviations used in the graphs should be explained (i.e. HZBZ).

5. Raw and processed data, as well as source codes should be made available in accordance with the journal’s Data Sharing policy.
Experimental design: The method section is quite fragmented and sometimes repetitive. The workflow should be described in the “overview” and not repeated afterwards. Nonetheless, the authors provide a clear and detailed description of the analyses performed.
Validity of the findings: 1. As the authors do not discuss how (or even in which contexts) their findings are going to guide decision making, the title of the manuscript “T1000: A reduced toxicogenomics gene set for improved decision making” should be rephrased. Indeed the authors fail to identify a clear use of their gene set for the scientific community (lines 444-447), thus bringing into question the value/scientific impact of the work.

2. The authors claim that T1000 has more toxicological relevance than other available gene sets (L1000, S1500) as their data-driven approach relies upon data derived from in vitro and in vivo human and rat toxicological studies. Yet table 4 shows that the sensitivity, specificity and precision of all of these gene sets are (a) very similar to a randomly selected gene set and (b) not impressive as classifiers (~25% sensitivity, ~70% specificity). This would lead to a lot of false negatives and a moderate number of false positives, bringing into question the value of T1000 and other gene sets for the identification of chemical hazards. Of further concern is the fact that these classifier values relate to the prediction of apical outcomes in a rat in vivo data set, in which histopathology data would also be available. The more useful scenario in which gene sets could be employed is to predict the clinical translation of a chemical hazard identified in preclinical studies. It would be expected that the classifier performance values would be even worse in this setting, hence the value of such an approach is questionable. Evidence supporting the translatability of T1000 from non-clinical species to human should therefore be provided. How well does T1000 perform as a classifier of drugs with e.g. hepatotoxic concern in humans?

3. The authors do not discuss their findings in a biological context. For instance, are there differences in genes/network responsible for the better performance of T1000 compared to the other available gene sets? This should be discussed in more detail in the result section (lines 365-386) and in the discussion.

4. Other authors have used the TG-GATEs databases to apply a weighted gene co-expression network analysis to safety assessment, identifying marker genes of liver toxicity but also using co-expression modules to understand stress-response pathways in drug-induced liver toxicity and to reveal mechanisms of pathogenesis concurrent with or preceding toxicity phenotypes (Sutherland JJ, et al. Toxicogenomic module associations with pathogenesis: a network-based approach to understanding drug toxicity. Pharmacogenomics J. 2018 May 22;18(3):377-390). Without any attempt to demonstrate the utility of T1000 for clinical applications, the paper lacks novelty in the biological/clinical sciences, and the authors may want to consider submitting to a journal in a different field (e.g. bioinformatic/mathematical modelling).
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: T1000: A REDUCED GENE SET PRIORITIZED FOR TOXICOGENOMIC STUDIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Dear Author

I have only two comments.

1) Reactome is not mentioned in Material and Methods.

2)The Authors addressed that the gene set was derived from analyzing data from human cell lines and in vivo and in vitro Rat liver. However, the testing and comparison with other known gene sets were done in rat tissues. Regarding the nature of how the authors calculated the gene set (involving both species and several tissues), the authors should mention in the Abstract that the testing was done in rat kidney data (or the dataset if they will)


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: T1000: A REDUCED GENE SET PRIORITIZED FOR TOXICOGENOMIC STUDIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: 1-    Method seems to be fragmented, not well describe and hard to reproduce the results using the provided description. For instance:
a.    Authors mentioned that they combined rat and human networks, however, they did not provide details on how the genes were mapped between the two species.
b.    Some parameters are just provided without any justification, for example, authors set k for K-means clustering for 3 and MCL inflation parameter to 3.3. To obtain systematic results, authors should apply the proper hyperparameter selection for algorithms used in this study and share their selection criteria.
c.    Authors refer to outliers in their Kmeans clustering method as most contributing, however, it is not clear to what these points contribute.
2-    In the prior knowledge part authors, authors used distance from cluster centroids to rank the gene. This may work only if the cluster sizes are comparable, however, if the cluster sizes are different then the authors may need to normalize such distance.
3-    Authors used the average of prior knowledge scores, this does not reflect the joint distribution of prior information of both nodes. Authors may need to explore further methods or discuss the limitations of their current method.
4-    Authors used MCL to cluster their graph, MCL is known to produce too many small clusters. From the number provided in the text, it seems there is one big cluster that covers 75% of genes while all other clusters are very small. It is interesting to see the distribution of the clusters size authors have. Also, I would suggest using the weighted gene coexpression network analysis (WGCNA) tool as it provides a utility to analyze co-expression networks.
Validity of the findings: 5-From the results side, it is interesting to see how the T1000 gene set compare to other gene sets reported in the literature in term of the number of common and different genes.
6-    From Figure 5, classification results seem very comparable. It is also very comparable to random gene set. Authors may consider performing some permutation test to make sure that the accuracy they are obtaining is significant from random genes.
Additional comments: 7-    References to some of the figures are missing, lines 375, 384-386.
8-    Figures 2 and 3 are hard to follow and see. I would suggest moving them to supplementary.


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: T1000: A REDUCED GENE SET PRIORITIZED FOR TOXICOGENOMIC STUDIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors addressed all of the comments in my first review.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors addressed all of the comments in my first review.


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: T1000: A REDUCED GENE SET PRIORITIZED FOR TOXICOGENOMIC STUDIES
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: T1000: A REDUCED GENE SET PRIORITIZED FOR TOXICOGENOMIC STUDIES
Review round: 2
Reviewer: 3

Output:
Basic reporting: Authors have substantially improved their manuscript, however there are still key issue related with randomness of T1000 genes.
Experimental design: 1- Authors did not explain how did they measure the statistical significance of their model performance given the random-500 null hypothesis.
Validity of the findings: 2- Author report significant level of 0.1 however on the other hand they say that models from random genes outperformed their model 30% of the times. Both results do not add up. In significance analysis 30% is considered a high number and indicate that the generated models are more likely random than true.
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: LIVING COCKROACH GENUS ANAPLECTA DISCOVERED IN CHIAPAS AMBER (BLATTARIA: ECTOBIIDAE: ANAPLECTA VEGA SP.N.)
Review round: 1
Reviewer: 1

Output:
Basic reporting: I recommend to fuse figures 1+2 (1) and all others except illustrations (2, 3) in total 3 figures, only first of which needs color. But this is not obligatory.
Some references are differently formatted.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Great job, congratulations


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: LIVING COCKROACH GENUS ANAPLECTA DISCOVERED IN CHIAPAS AMBER (BLATTARIA: ECTOBIIDAE: ANAPLECTA VEGA SP.N.)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is properly organized, clearly and the English language well (with some very minor exceptions, see the review)
Experimental design: no comment
Validity of the findings: Authors gave the differences of the new species with all other species, and described the structure of the species in detail. It is validity to erected a new species.
Additional comments: This is an interesting paper described a new species and species based on one specimen which come from Miocene Simojovel amber. We can know more informations about  Miocene through amber. Whereas I found some minor errors in your paper, please correct them.


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: LIVING COCKROACH GENUS ANAPLECTA DISCOVERED IN CHIAPAS AMBER (BLATTARIA: ECTOBIIDAE: ANAPLECTA VEGA SP.N.)
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: See comments in the PDF


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: LIVING COCKROACH GENUS ANAPLECTA DISCOVERED IN CHIAPAS AMBER (BLATTARIA: ECTOBIIDAE: ANAPLECTA VEGA SP.N.)
Review round: 1
Reviewer: 4

Output:
Basic reporting: engish clear
references ok
structure ok
results coherent
Experimental design: aim and scope attained
question well defined
investigation rather rigorous, some points need better justification
methods well described
Validity of the findings: new
data robust
conclusions should be better supported
Additional comments: Cenozoic cockroaches were modern and with two indigenous exceptions they represent living genera

This sentence is curious, as it is what s currently known, not all the taxa !!, also, the fossils have been attributed to extant genera but on the basis of generally incomplete fossils, especially the genitalia are nearly always missing
So be more prudent

cockroach does not show any significantly primitive characters
on the basis of which phylogenetic analysis, please precise

Order Blattodea (cockroaches) originated in Late Carboniferous
No, no proof at all,
Stem dictyoptera are known in carboniferous, which is very different
replace by stem group of Dictyoptera

line 41: reorder the references from oldest to most recent
Föster

Line 76: strange sentence, extraction of what ? rephrase please

it is unclear whether the mentioned specimens does not represent

line 141: in having derived simplified form of pronotum
precise why derived, and simplified in what ?

line 328: please give at least one reference to justify the genus attribution, and precise which are synapomorphies, and why (reference of a phylogeny), important point !!

of Chiapas amber were cosmopolitan, while younger Dominican amber contain modern
please, give reference on the dating of the these ambers, because age of Dominican amber is controversial ….
Line 359: why Eocene, you have fossils from this period ?


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: LIVING COCKROACH GENUS ANAPLECTA DISCOVERED IN CHIAPAS AMBER (BLATTARIA: ECTOBIIDAE: ANAPLECTA VEGA SP.N.)
Review round: 1
Reviewer: 5

Output:
Basic reporting: In this manuscript, the authors describe a new extinct species of cockroach, Anaplecta vega, from one specimen preserved in Chiapas amber. This study is quite straightforward but it lacks some context and references, and some figures are irrelevant or not clear enough (see general comments for more details)
Experimental design: The methods is not described with sufficient details (see general comments for more details)
Validity of the findings: The figures does not allow to observe the characters discussed in the manuscript.
A list of characters justifying the taxonomic position of the new species within the genus Anaplecta is missing.
Additional comments: In this manuscript, the authors describe a new extinct species of cockroach, Anaplecta vega, from one specimen preserved in Chiapas amber. They provide a lengthy description of the head, tegmina, legs… and a differential diagnosis with extant Mexican Anaplecta species. This work is interesting and quite straightforward but I have a few concerns preventing the publication of this manuscript.

1. The authors must provide a list of clearly identified characters to justify the taxonomic position within the genus Anaplecta. In addition, the description relies only on a single specimen, which is always problematic although acceptable. Still, this specimen has asymmetrical hindlegs and palps. The author should explain why they believe this asymmetry is characteristic of the species and not specimen-specific (e.g. due to taphonomic processes or due molting issues, etc.)

2. The introduction should be revised because its structure is not clear and its content inaccurate.
The first paragraph, composed of a single confusing sentence (Mantodea does not belong to Blattodea, they are sister-groups), misses several references (and Brongniart 1885 is inadequate given the progresses made in our understanding of roachoid fossils and their relationship to modern Dictyoptera).
The second paragraph is supposed to be a list of works concerning cockroaches. Yet, some studies concern Alienoptera, Raphidiomimidae, which are not cockroaches sensu stricto, or Aethiocarenodea, which are not cockroach at all. This list, supposed to be exhaustive(?) and in alphabetical order(?) must be revised.
The third paragraph is also a list of studies, but about Cenozoic cockroaches. Among this list, the authors could distinguish the ones relying on amber as their introduction seems to emphasize fossils from ambers.
The fourth paragraph is again a list: list of species from the studies listed in the previous paragraph. This list is not easy to read and could be presented in a Table instead.

3. Some figures are irrelevant or do not allow observing the characters discussed in the paper. Specifically, several characters (in the tegmina, the legs) cannot be seen in Figures 2 and 3. I understand that good pictures might be challenging to obtain but the authors should provide better figures (close-ups) so that the reader can observe the characters and not only rely on the authors’ description. In Figure 5, computing average measurements for living Mexican Anaplecta species does not bring much useful information. Why is it useful to know that Anaplecta vega is smaller than the average of Mexican Anaplecta species? In Figures 7 and 8, it is unclear what the authors want to show. In addition, some measurements are doubtful as noticed in the text but not in the figure; which is quite misleading (e.g. femur of right front leg).

4. In the methods, the authors mention two species of Anaplecta that have been used for comparisons. However, it is unclear whether the authors borrowed and looked at the type specimens or if they relied on the photographs. If so, the authors might explain why looking at the photographs from only two species was enough for their work. Also, what about the other Mexican species compared to A. vega (did the author rely only on the literature?)

In the Discussion, the authors emphasize the asymmetry of the specimen in the palps and legs but do not discuss this issue much further. Given that the authors chose this angle of highlight, it should be more discussed.

6. A large part of the description is composed of measurements (antennomeres, tarsomeres, which could be summarized in Tables rather than mentioned in the text as it is because it is not easy to read.

Minor point:
Blattaria is used in the title but Blattodea is used in the Introduction. Please homogenize.


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: LIVING COCKROACH GENUS ANAPLECTA DISCOVERED IN CHIAPAS AMBER (BLATTARIA: ECTOBIIDAE: ANAPLECTA VEGA SP.N.)
Review round: 1
Reviewer: 6

Output:
Basic reporting: The manuscript is based on the description of a fossil cockroach found in amber. The finding is interesting because the genus Anaplecta is poorly known while representing a worldwide distributed group in cockroaches.

The introduction should be improved to better present the study. Making a long list though incomplete of fossil cockroaches studied until today is not useful. The authors should better focus on more recent phylogenetic studies (Legendre et al., 2015; Evangelista et al., 2019) to replace their finding into a wider scope.

The qualifier cosmopolitan for the genus Anaplecta is misleading. The word 'Cosmopolitan' lets the reader thinking that this is a tramp genus present everywhere without local diversification. They should rather suppress it from the title and explains that the genus has a worldwide distribution.

The English could be slightly improved in order to make the manuscript more attractive
Experimental design: The placement of the fossil specimen in the genus is not made according to the relevant literature. Grandcolas (1996) has been providing several apomorphies for the family Anaplectidae that could be esasily used here in this respect. This author also described wing folding that the present authors are citing as an informative character.

The authors should abandon gradistic characterizations such as primitive or evolved for taxa. Whatever the position more or less deeply nested of Anaplecta within published trees, this does not allow arguing that Anaplecta would be especially primitive or not. This is basic phylogenetic reasoning for which explanations can be found in recent papers (Crisp, M. D., Cook, L. G. 2005. Do early branching lineages signify ancestral traits? Trends in Ecology & Evolution 20, 122-128)

They should refer once again to more recent phylogenetic studies (e.g., Legendre et al., 2015) that also document the position of Anaplectidae in cockroaches with a much more relevant sampling that the older study they referred to.
Validity of the findings: The finding seems correct but the characters used should be attributed to previous publishing authorities.
Additional comments: The paper is trying to make it worth publishing of a new species of fossil cockroach belonging to a poorly known genus. Though useful as showing an original finding, the paper should be freed for the problems evoked above. The authors should cite all relevant literature. Within the discussion, they could usefully make a review of the knowledge - recent and less recent - existing on the genus Anaplecta.


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: LIVING COCKROACH GENUS ANAPLECTA DISCOVERED IN CHIAPAS AMBER (BLATTARIA: ECTOBIIDAE: ANAPLECTA VEGA SP.N.)
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I provide a pdf where I tried to address and/or correct some errors 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: LIVING COCKROACH GENUS ANAPLECTA DISCOVERED IN CHIAPAS AMBER (BLATTARIA: ECTOBIIDAE: ANAPLECTA VEGA SP.N.)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript has been improved since the first reviewing session. However, it still remain some aspects that should be corrected to make it acceptable for publication.
The introduction is still a very biased catalogue of the works of some authors while some others, largely influential (e.g., Legendre et al., 2015), are still not cited.

The authors have corrected many details but they still failed to give the manuscript a very general value, further than the description of one peculiar fossil species of Anaplectidae. At this stage, this is up to the editor to decide whether PeerJ should publish it or defer it to a journal of taxonomy accepting pieces of one-species taxonomy.
Experimental design: This is OK
Validity of the findings: Ok again
Additional comments: The authors have corrected many details but I feel that they still failed to give the manuscript a very general value, further than the description of one peculiar fossil species of Anaplectidae.


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: THE EFFECT OF EXTERNAL LATERAL STABILIZATION ON THE USE OF FOOT PLACEMENT TO CONTROL MEDIOLATERAL STABILITY IN WALKING AND RUNNING
Review round: 1
Reviewer: 1

Output:
Basic reporting: •	I have not previously reviewed for PeerJ, so I don’t have a frame of reference for how raw data is typically shared. The authors clearly provide extensive raw data and code, which is admirable. I wonder if it would be possible to provide documentation that makes interpreting these data (or performing future analyses) easier for readers.
Experimental design: •	The authors list 5 hypotheses to be tested (lines 91-100). It was unclear to me exactly which statistical tests were used to address each of these individual hypotheses. Would it be possible for the authors to draw a more explicit link between the hypotheses and the statistical methods?
•	Could the authors more clearly define “ML foot placement position”? The Methods section reads to me as if this was defined as the mediolateral displacement between the heel of the trailing leg and the heel of the leading leg upon heel strike. I think this is fine, but could cause confusion. While inconsistent across the field, some prior work has defined this measure as “step width”, while “mediolateral foot placement” was defined as the displacement between the CoM/pelvis midline and the heel of the leading leg upon heel strike. Again, I think either definition is fine – as long as it’s clearly defined.
•	For clarity, please explicitly state what gait events were used to define the start and end of gait cycles. I think this is defined as heel-strike to heel-strike, but making this explicit would be helpful.
•	I think it would be worth stating in the Methods if the ANOVAs included interaction terms (see line 187).
Validity of the findings: •	Did the authors check whether metabolic rate reached a plateau within the 5-minute trials (even if just through visual inspection)? While this is a typical trial duration for quantifying metabolic rate, I wonder if the unusual nature of walking/running in lateral stabilization could potentially lengthen the time until a plateau is reached.
•	In my opinion, the presented results are interesting, but also quite complex. I think that readers could be helped by a more detailed Results section – including a description of some of the potentially counter-intuitive results. For example, the authors state that their second hypothesis is supported by a significantly stronger CoM-FP relationship in walking than running. However, I think that the significant difference between ~30-40% of the gait cycle (visible in Fig. 3) is actually due to a stronger relationship in running than walking (based on Fig. 2). Is this correct? If so, I don’t think this contradicts the authors’ big-picture explanation, but probably deserves to be mentioned. Additionally, I think the results presented in Figure 5 would benefit from more explanation. What exactly is indicated by a significant main effect of Condition (Fig. 5A)? By a significant main effect of Mode of Locomotion (Fig. 5B)? By a significant interaction (Fig. 5C)? Presently, only the interaction effects are mentioned – and only focus on one aspect of the apparent significant differences.
•	I think including slightly more information in the figures or figure legends would be helpful. In Figures 3 and 5, it may be useful to just state what the shaded areas indicate. In Figure 4, it would be helpful to state what the error bars represent, as well as what the horizontal lines indicate. Are these the results of specific post-hoc comparisons? For example, is the energy cost of Normal walking significantly different from the cost of Stabilized walking, as appears to be indicated in Figure 4C?
•	The authors state in the Discussion that trunk mechanics explain over 60% of the variance in ML foot placement (lines 219-220). I think it would be worthwhile to be a little more specific with this statement – this is only the case for trunk mechanics near the end of the gait cycle.
•	While not necessary, I would find it valuable if the authors would briefly speculate why they observed an increased energy cost during stabilized locomotion. They are absolutely correct that the results from other groups have been equivocal, but I’m not aware of a previously reported increase.
Additional comments: •	In line 120, “trial” instead of “trail”
•	Add the intended reference to lines 142-143
•	The “first” in line 186 seems out of place. Maybe I’m reading this sentence incorrectly.
•	In line 284, I think this would be clarified by “…and others reported no effects…”


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: THE EFFECT OF EXTERNAL LATERAL STABILIZATION ON THE USE OF FOOT PLACEMENT TO CONTROL MEDIOLATERAL STABILITY IN WALKING AND RUNNING
Review round: 1
Reviewer: 2

Output:
Basic reporting: There is an over-emphasis on "hypothesis" testing throughout the manuscript that is unwarranted and diminishes the credibility of the manuscript.  This work is primarily exploratory in nature.  This is perfectly fine, but the manuscript presents all of this work as being "hypothsesis" driven, which it mostly was not.  For example, Lines 91-100: For "hypothesis" (2), the proposed "higher aforementioned correlations in walking" cannot be predicted a priori.  Likewise, "hypotheses" (4) and (5) are purely conjecture.  This comes across as "HARK-ing" (the unscientific process of contriving hypotheses after the results are known).  This unwarranted over-emphasis on "hypotheses" continues throughout the Results and Discussion sections in particular.  As the dependent measures addressed here have not yet been assessed in running, an exploratory study to determine how running is similar/different from walking is perfectly legitimate, but the manuscript must be written to present the work as such.
Experimental design: The research question being addressed (lateral balance control during running) is original and is of modest relevance to the scientific field.

There are a number of technical and study design issues that need to be addressed, however, outlined below:

Sample Size -- Line 103:  No a priori power analysis presented for sample size of N=10.  Here, this is an issue as it was raised by the authors (Line 69-70) pointing to a paper of theirs (Ref. #[20]) that is currently under review titled "Small sample size impedes reproducibility..." and yet the sample tested here (N=10) is as small or smaller than prior similar studies cited previously.  Thus, the sample size needs to be fully justified and increased as needed to ensure rigorous and reproducible findings.

Experiment -- Line 127:  No justification given for using stiffness of 1260 N/m.  In Ijmker et al 2013, with same experimental setup, that study tested stiffnesses up to 1820 N/m.  It seems entirely likely the present negative results could easily have been due to not providing enough lateral stabilization.

Incorrect Calculation -- Lines 149-161:  Calculations are either not correct, or not properly described (see also Fig. 2 etc.).  The goal of the regression is to estimate subsequent foot placement based on prior COM state within each *step*.  Thus, (Lines 149-150) time normalizing data to 0-100% of the full gait cycle (i.e., one full stride = 2 complete steps) is not correct here, and makes no sense!  This subsequently makes the Results largely indecipherable, as representing these calculations across "0-100% of the gait cycle" is inconsistent with the nature of these analyses.

Statistical Analyses -- Section 2.6:  Two assumptions appear not justified.  First, Supplement Fig, 1 does show significant differences between left & right legs, especially near 50% gait cycle.  While Fig. 1B pools across both running and walking, the significant difference appears clearly driven by the walking data as shown in Fig. 1A.  The SPM analysis should therefore be run separately for the walking and running data sets to identify what specific differences occurred within walking itself.  However, pooling across limbs may still be justifiable if these differences do not represent a primary aim of this study.  Otherwise, the authors should choose one limb or the other to analyze.

Second (and more importantly), whether pooling across limbs or not, the lack of speed differences across running speeds does not justify pooling or averaging these data across all running speeds because you cannot also average across multiple speeds for the walking trials.  This creates "apples to oranges" comparisons of 1 walking speed to the average of multiple running speeds.  The legitimate approach would be to choose one running speed (maybe 9 km/h?) as "representative" and then compare to the one walking speed.
Validity of the findings: The major concern over the validity of the findings is the issue of increased metabolic cost while being laterally stabilized.

The Introduction (Lines 67-70) makes misleading statements.  Refs. [3], [9], [10], and [18] all found consistent and significant reductions in energetic cost.  Ref. [19] found small reductions that were not statistically significant, but also was comparing healthy subjects to trans-tibial and trans-femoral amputees and stated that "one outlier in the energy cost data considerably influenced the significance of these results"...  Ref. [20] is still "under review" so cannot be assessed.  Thus, the balance of evidence (while not "unanimous") does strongly support the idea that lateral stabilization does reduce energetic cost.  The only inconsistent findings are those that have been produced by the authors' own lab.  The subsequent Discussion (Lines 280-291) just repeats the same misleading statements.  The only studies to report equivocal findings are those (like this one) from the authors' own lab.  This suggests the possible alternative real reason for such equivocal findings may well be within that specific experimental setup and/or with how the processes and procedures were conducted within those experiments that may have led to the discrepancies.

Secondly, the Discussion is largely speculative, but not presented as such.  In multiple places, statements are made as if they were "conclusions" but the statements themselves are not supported by the results presented in the study.  For example:

Lines 238-244:  Likewise, emphasis on "active control" over "passive dynamics" here is no supported by the data.  This is conjecture / speculation.  The authors' intuition may well be correct, but the analyses presented do not and cannot address the question of which (active or passive) is the underlying *cause* of these correlations.  Both possibilities should be discussed and addressed from an unbiased point of view.

Discussion, In General:  Likewise, multiple statements throughout the Discussion refer to what these results imply about maintaining (mediolateral) "stability".  All of these statements are conjecture and none are supported by the results because no measures of "stability" were computed or presented.  All discussion and conclusions should remain within the scope of the actual results themselves.  Any speculation for what implications these results may or may not have for other issues should be very clearly labeled as speculation.  Indeed, statements made in the Introduction (Lines 71-83) also seem to strongly argue for quantifying ML Margins of Stability, as this measure directly relates to the changes described.  It is not clear why this was not done in this study.
Additional comments: Additional Comments:

Lines 53-54:  Yes, both passive dynamics and active control will occur...  But the correlation analyses presented here cannot disentangle which is which...

Lines 86-87 (and throughout the manuscript):  All measures should be reported in standard SI units - Thus, speeds in m/s, not km/h.

Lines 85-88:  The sentence, as phrased, is again misleading - It implies different results from the two different studies, when in fact, both studies report consistent results for the same speeds: i.e., no difference b/t 1.0, 1.2, & 1.4 m/s in Wang 2014 & no differences at 1.0 & 1.2 m/s in Stimpson 2018.

Line 127:  No justification given for using stiffness of 1260 N/m.  In Ijmker et al 2013, with same experimental setup, that study tested stiffnesses up to 1820 N/m.  It seems entirely likely the present negative results could easily have been due to not providing enough lateral stabilization.

Lines 155-157:  Referring to the regression equation as a "model" is, while technically "correct", still somewhat misleading.  This is simply a statistical regression, to compute a correlation.  There are no "cause-effect" relationships defined here.  Many readers will assume the authors are referring to some mechanistic model (e.g., a dynamic model of actual walking), which is not the case here.

Line 177:  More description and definition of "the SPM method" is required.

Lines 193-194:  "Highly correlated" is not defined in this context.  R^2 = 0.6 is far from R^2 = 1.0.  Additionally, R^2 ranges from very low (< 0.1) to higher values approaching 0.8, depending where in the gait cycle you look.  So there is both (1) no a priori definition or expectation of 'how high' (R^2 magnitude) and (2) no apriori expectation of where in the gait cycle such correlations should exist.  These results are thus exploratory (which is fine), but are not specifically hypothesis-driven as implied.

Lines 220-223 & Line 228:  These statements are not supported by the results.  Yes, results show correlations of COM state with subsequent foot placement.  But correlations do not constitute causation.  No conclusions can be drawn about the extent to which these correlations may or may not reflect "active control" or simply passive dynamics.

Lines 238-244:  Likewise, emphasis on "active control" over "passive dynamics" here is not supported by the data.  This is conjecture / speculation.  The authors' intuition may well be correct, but the analyses presented do not and cannot address the question of which (active or passive) is the underlying *cause* of these correlations.  Both possibilities should be discussed and addressed from an unbiased point of view.

Supplement:  Descriptions given need to be improved.  The statements in the Supplement all refer to differences (or lack thereof) for "running".  But the figures (Supplement, Figs. 3, 4, & 4) also show data for walking (4.5 km/h).  So the statements made do not match the figures shown.


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: THE EFFECT OF EXTERNAL LATERAL STABILIZATION ON THE USE OF FOOT PLACEMENT TO CONTROL MEDIOLATERAL STABILITY IN WALKING AND RUNNING
Review round: 1
Reviewer: 3

Output:
Basic reporting: (1) The term "tight" is used in a few places:
- Line 45: "tight" coordination
- Line 87: "tight" coupling
- Line 245: "tight" ML foot placement
and I was not sure what this term meant.  Can more specific term(s) be used instead, e.g. does "tight coordination" really just mean a significant correlation between the variables or a stronger correlation compared to some reference case?

(2) Line 28: It would help for clarity and for framing the scope of the paper if the authors could define in the text "stability" or what it means to be "stable" in the context of this research area and their research question.  It seemed to me like it would be something like "reject small (internal, step-to-step) perturbations without falling/slowing", something along those lines.

(3) Line 91: It was not clear to me how correlation between these variables reflects "stabilization by active control".  The paper would benefit from spending more time in the Introduction developing this relationship.  The distinction between "active" and "passive" control does not seem strictly necessary or helpful in this particular paper (unclear how anything concrete on this distinction could be be inferred from these data).

(4) Line 142: Appeared to be a missing reference here

(5) Line 162: Suggest referring to this variable as the "metabolic rate" (or something similar) instead of the metabolic energy expenditure.
Experimental design: Line 99: I didn't understand the basis for hypothesis #5.  There is not much about speed in the Introduction.  The authors might consider removing this hypothesis to improve the focus of the study on the other more strongly emphasized hypotheses.  I didn't think the speed element added much here.

Line 103: Given the relatively small sample size and multiple comparisons, please consider reporting some related statistics e.g. what was the minimum detectable difference or what was the power level for the minimum effect of interest?

Line 158: Why does the model need to include both position and velocity, or if this is not needed, why were both chosen for inclusion?  The basis for the model should be briefly explained here beyond just stating what the terms are.

Line 174: I was confused on what was done here with the statistics.  How were the R^2 values averaged?  They are usually not normally distributed in which case an arithmetic average is probably not appropriate.  I had the same concern over using the F-test to test for differences in R^2 values (Line 178); these are typically compared using Fisher's z-transform or something similar, was this done?  On Line 176, what is meant by the "R^2 time series"?  R^2 is typically just a single number.  At a minimum some more detail here is needed.  A graphic demonstrating the "flow" of the data analysis might be helpful.

Related to the previous comment, overall I could not tell how the outcome variables were produced.  It seems there are a time series of R^2 values, one at each 1% of the gait cycle, but from the description on Line 155 I did not understand how this model produces such data.  Earlier text stated (Line 92) stated that the Trunk CoM during swing was being related to the subsequent foot position in stance.  How exactly does model do that?  It is not clear.  This made it very hard to evaluate the paper.

Given the large number of comparisons made in a non-exploratory study, the threshold p-value of 0.05 is not appropriate.

Concerning the estimation of trunk ML CoM, why not just use the force data to calculate the (change in) whole-body CoM?  An estimate seemed unnecessary.  Or does the framework here require trunk CoM specifically and would not apply to whole-body CoM?  It would help to explain this somewhere in the text concerning the choice of outcome variables.  I realize trunk is a large fraction of the whole body mass but the notion of whole-body stability seems more relevant to whole-body CoM than trunk CoM.
Validity of the findings: The interpretation of the results seemed rather subjective and I struggled to understand what results most of the inferences in the Discussion were based on and why.  What is it that makes these correlation results "high", "strong", etc.?  What are the statistical outcomes supporting these statements?  Why are these particular periods of the gait cycle emphasized?  What is the basis for the statement on Line 245 that ML placement control is "less tight" in running?

The result of greater energy cost with lateral stabilization needs more Discussion.  Previous studies to my knowledge have all either shown a reduction in cost or no change in cost.  Are there differences in the equipment that could explain this?
Additional comments: There is good data here, but (with respect to the effort of the authors) I was not able to understand how the main outcome was calculated and the basis on which inferences were made from it on the hypotheses.  Overall I thought there was too much here for a single paper.  Suggest focusing on a smaller number of outcome variables (e.g. are the step width outcomes needed?) and explaining more clearly how changes in these variables with external stabilization reflects the importance of ML control of foot placement on stability.


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: THE EFFECT OF EXTERNAL LATERAL STABILIZATION ON THE USE OF FOOT PLACEMENT TO CONTROL MEDIOLATERAL STABILITY IN WALKING AND RUNNING
Review round: 2
Reviewer: 1

Output:
Basic reporting: •	The authors provide the raw data from this study, and code used to analyze these data. In the resubmission, the authors have improved clarity with the addition of new documentation.
Experimental design: •	The authors have clearly addressed the majority of my previous concerns regarding experimental design.
•	The fifth hypothesis seems out of place. I understand the authors’ desire to include this question, as it was pre-planned. However, I did not think this hypothesis was justified based on the background information provided in the Introduction. The stated hypothesis does not appear to include a direction (e.g. faster speeds increase the correlation between pelvis state and foot placement), so I found it unclear what the expected/hypothesized effect actually was. Further making this hypothesis seem out of place, the statistical test used to test it is not described in the Statistical Analysis section. The manuscript may be clearer if this question is described as a pre-planned analysis (with results included in the Supplementary Material), but is not listed as one of the primary hypotheses in the Introduction.
•	It was not clear to me how mid-stance was defined (see p. 7, line 10).
•	I’m not sure that I understand the new analysis presented in Figure 3. I think it would be beneficial to describe in more detail (in the Methods) exactly what was done to arrive at these percentages. For example, was “significance” of each beta value determined for leg of each individual participant?
Validity of the findings: •	The authors addressed the majority of my previous comments regarding their findings.
•	I suggest not including the paragraph on page 13, lines 10-13. The referenced data are not included in the main text, so I think this conclusion/discussion would better belong in the Supplementary Material.
Additional comments: •	I found the sentence starting with “The first hypothesis…” on page 8 line 21 difficult to follow. This may just be an issue of grammar.
•	In the legend for figure 7, the (A) panel label is missing.


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: THE EFFECT OF EXTERNAL LATERAL STABILIZATION ON THE USE OF FOOT PLACEMENT TO CONTROL MEDIOLATERAL STABILITY IN WALKING AND RUNNING
Review round: 2
Reviewer: 2

Output:
Basic reporting: Previous Comment #1:  My primary comment had been that there was an over-emphasis on “hypothesis” testing throughout the manuscript.  The authors’ response addresses (mostly) the HARKING question.  However, the authors did not address the initial and more fundamental concern that this work is "exploratory" in nature and not fundamentally “hypothesis driven”.  The present work focuses on testing "predictions": i.e., of what the authors expected to observe.  As I stated previously, this itself is fine for exploratory research.  Conversely, a "hypothesis" poses a possible *explanation* for the expected observation.  While the results presented in this work are interesting, no true hypothesis regarding the underlying explanations for the results observed is tested.  Several possible explanations are speculated in the Discussion and elsewhere, but new experiments would be needed to directly test any of those.  Thus, the notion that this work is fundamentally "hypothesis" driven remains over-emphasized throughout the manuscript.
Experimental design: Previous Comment #6 (Previously under “Experimental Design”):  I had said that the lack of speed differences across running speed did not justify pooling or averaging data across speeds, when this could not also be done for the walking trials (where only 1 speed was assessed).  I suggested the very reasonable alternative of picking one of the 3 running speeds as “representative” and run statistical comparisons between that condition and the walking.  The authors responded, stating that “averaging only decreases the variability for the running condition” – But this was exactly my point!  Because you averaged across 3 speeds for the running condition, you reduced the variability for *that* condition - but you do not have 3 speeds for walking, so you cannot treat the walking data in the same way.  Thus, the walking data will have more variability not because it is inherently different from running, but because the walking and running data were processed differently.  Even if “ANOVA is… reasonably robust against violation of the assumption equality of variances”, there is simply no reason rely on this assertion.  The alternative I had suggested before would avoid this, removes any doubt of differences found being due to differences in data processing, and is very simple to implement.
Validity of the findings: Previous Comment #3 (Previously under “Experimental Design”):  I had requested justification for using the stiffness of 1260 N/m.  The authors’ explanation (in their response and in the paper) is that 1260 N/m was selected (Lines 123-125) “since in a previous study no significant reductions of energy cost, step width, and step with variability were found beyond this stiffness” [cites Ijmker et al., 2013].  The problem is that study was done by the same group in the same lab with the same (or nearly the same?) experimental set-up.  And that study reported significant *reductions* in metabolic cost with added lateral stabilization (which is now cited as the rationale for the current study design).  However, the present study reports significant *increases* in metabolic cost with the same lateral stabilization.  This appears to be a rather glaring contradiction – e.g., it seems very possible the lateral stabilization was simply imposed incorrectly… Or perhaps the metabolic data were recorded / analyzed incorrectly…  Or perhaps the Ijmker study was conducted incorrectly.  However, rather than addressing this contradiction, the authors merely pushed their energy cost results into their Supplement and then only speculate that (Supplement, p. 7, Lines 7-8) that “These conflicting findings in literature, may be explained by differences in experimental conditions or designs” – but that is not an explanation at all.

Previous Comment #7:  The issue of the energy cost results still remains significantly problematic.  Pushing these findings to the Supplement does not resolve the discrepancies.  Likewise, the revised text (Supplement, pp. 6-7) makes clear that all of the prior studies cited found either significant decreases in energy cost, or no significant changes…  Thus, the fact that the present study reports significant *increases* in energy cost with lateral stabilization remains contrary to all of those prior published findings and the current manuscript lacks any explanation for this.  Indeed, the main manuscript still claims (Lines 168-169):  “Reduced energy costs in stabilized conditions would support that the control of ML stabilization requires energy consumption…” and there is no mention in the main manuscript that the findings themselves were the exact opposite of this assertion, and no explanation in either the paper or the Supplement as to why this occurred.

Previous Comment #8 (also comments #10, 17, & 18):  I had pointed out that conclusions about “active control” are simply not supported, either by the results or by the methods used here.  The present study computed correlations of CoM state to subsequent foot placement – period.  At the beginning of their Intro (Lines 48-49), the authors admit at the outset that “motions of the CoM relative to the BoS are thought to be controlled by passive dynamics as well as active processes [1-3].”  The calculations of the correlations themselves alone cannot distinguish what is driving those correlations: active control, passive dynamics, or something else.  Indeed, the authors state in their Discussion (Lines 237-242) that these correlations “could also be due to passive dynamic coupling of lower extremity movements to movements of the upper body” and that “the results of current study cannot answer the question whether active control or passive coupling is the underlying cause of this correlation”.  This is true!  The authors are also correct that aspects of “control” (muscles, reflexes, etc.) likely do influence these correlations also.  The fundamental problem is that calculating correlations themselves *cannot* distinguish these! There may well be differences in “control” between walking and running.  There may well be differences on “control” without and with external lateral stabilization.  And these differences in “control” may affect these correlation calculations.  BUT!  There absolutely *are* differences (significant ones!) in passive dynamics of walking vs. running.  And there absolutely *will be* (by construction) differences in the passive dynamics of stabilized vs/ not-stabilized gaits (precisely because you are adding a passive stabilizing mechanism).  And these will also affect these correlation calculations!  So the fact that the correlations differ between running and walking and/or between stabilized and not-stabilized cannot be used (by themselves) to infer any reasonable conclusions about the degree to which “control” contributes to these differences.

Previous Comment #9:  I had pointed out that references to notions of “stability” in this paper were misplaced, as no measures of "stability" were computed or presented here.  The authors largely concurred and re-phrased a number of statements in the paper, but 2 issues remain:

First, I had recommended perhaps computing XCoM-based measures such as “Margins of Stability” (MoS).  In their response, the authors indicated that “the XCoM indicates where to place the foot to come to a static equilibrium state. Clearly this is not appropriate for walking/running.”  This seems highly disconcerting (1) because of the large body of literature using XCoM & MoS to quantify “stability” of gait (both walking and running) and (2) perhaps more importantly, because both of the more senior authors here (Bruijn and van Dieen) have (together and separately) published multiple papers that used XCoM measures precisely to characterize gait “stability”.  So if the claim now is that "Clearly this is not appropriate for walking / running" then one could only conclude that that entire body of literature is now invalid?

Second, the title still refers to “control of mediolateral stability”.  In the Abstract, "stability" is mentioned twice in the first 3 sentences and again in the final "We conclude..." sentence.  The Introduction starts (Lines 45-46) by defining “gait stability”.  First sentence of the 2nd paragraph states that “The foot placement strategy is the main mechanism to control medio-lateral (ML) stability in walking and running.” And so on…  So the changes made to the Discussion and Conclusions to remove multiple references to “stability” are laudable, they fall short when the entire paper remains, from the beginning, framed in the context of “gait stability”.
Additional comments: Overall, I do like the findings of the study and I do find the results themselves interesting, thought-provoking, and potentially relevant.  However, I think this revised manuscript, while much improved, still goes way too far in trying to connect what was actually calculated to concepts of “control” and concepts of “stability” in ways that are simply not justified here, either by the experimental design or by the dependent measures themselves.  While I have no objections to the calculations themselves, I think the authors are getting well out “in front of their skiis” in how they are interpreting them.  The paper at this point just needs to be re-written from a neutral and un-biased perspective – reporting the correlations that were calculated at face value for what they are and nothing more than that.


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: THE EFFECT OF EXTERNAL LATERAL STABILIZATION ON THE USE OF FOOT PLACEMENT TO CONTROL MEDIOLATERAL STABILITY IN WALKING AND RUNNING
Review round: 3
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed my prior concerns.


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: THE EFFECT OF EXTERNAL LATERAL STABILIZATION ON THE USE OF FOOT PLACEMENT TO CONTROL MEDIOLATERAL STABILITY IN WALKING AND RUNNING
Review round: 3
Reviewer: 2

Output:
Basic reporting: In regards to stated Journal Criteria:
These issues are fine.
Experimental design: In regards to stated Journal Criteria:
The experimental design itself is fine.  The dependent measures calculated are appropriate and appear to have been calculated correctly.  Methods are described with sufficient detail.
Validity of the findings: In regards to stated Journal Criteria:

"Negative/inconclusive results accepted" by PeerJ - The current results are at best "inconclusive" but this is fine.  No concerns if reported as such.

All underlying data have been provided -- No concerns.

"Conclusions are well stated, linked to original research question & limited to supporting results":  The authors' conclusions are clearly stated, but just not supported by the results themselves as currently presented.

"Speculation is welcome, but should be identified as such":  Much of the interpretation of the findings is speculative, but is not presented as such.
Additional comments: While the authors have again made some important improvements to the paper, I must again point out that the underlying substance of several of my prior comments has not really been addressed.

On the issue of the energetic cost results (Previous Review #2, Comment #1 and Review #1, Comment #1):
If indeed, both the current experiments and prior experiments were conducted "correctly" (and let's assume they were - that's fine - no problem), the fact that the present experiment showed changes opposite to those in prior studies using a very similar protocol is then more interesting and more important than if one or more of the different experiments had somehow not been done "correctly".  If the results showing both increased and decreased energy cost are both correct, then this would seem a potentially very important finding, worthy of including in the main paper (not just the supplement) with some appropriate explanation.  (This issue is, however, of somewhat lesser concern).

On the issue of interpreting the R^2 results (Previous Review #2, Comment #5 and Review #1, Comment #8):
The issue here is not really that I as a reviewer have a different "opinion" as to how to interpret these R^2 measures.  To be honest, I really don't care.  The issue is that the manuscript itself includes statements that contradict the conclusions being drawn.  If indeed (Lines 244-246) "we cannot rule out that the passive dynamics play a role in the correlation..." and that (Line 246) "further studies are needed...", then one cannot then conclude that (Lines 283-284) "ML foot placement is adjusted to ML trunk CoM state to control ML stability..."  Yes, this is one possibility.  But the alternative possibility that the effects measured here could be attributable instead to passive dynamic effects, as the authors themselves directly state (Lines 244-246) still cannot be ruled out.  The authors offer (Lines 60-64) evidence from other studies regarding "sensory illusions", "visual perturbations", "muscle activity" and "neurological disorders".  These may be fine in the context of those experiments, but do not directly relate to THIS experiment conducted here.
I see 2 options here:  One is for the authors to provide a coherent explanation for how and why, in THIS experiment, which compared walking to running and did so with and without adding passive elastic springs at the waist...  why and how these specific manipulations did NOT alter the passive dynamics of locomotion.  The alternative option is for the authors to offer a balanced presentation (consistent with their own statement on Lines 244-246) across the manuscript that offers changes in passive dynamics as an EQUALLY plausible explanation for the findings.

On the issue of "stability" (Previous Review #2, Comment #6 and Review #1, Comment #9):
Again, the issue here is not a difference of "opinion" but that the authors make statements (in their responses and in the manuscript) that contradict each other.  They define "stability" (Line 45) as "maintaining a steady gait pattern without falling in the face of perturbations".  This is great!  But it remains not at all clear how (or even if) any of the measures reported here reflect this definition of "stability".  Indeed, the manuscript claims (Line 52) that "foot placement strategy is the main mechanism [used] to control medio-lateral (ML) stability"  But if this is true, then if R^2 is a measure of this "strategy" or "mechanism" itself (as claimed, see previous comment), then R^2 is not (itself) a direct measure of "stability" which is the result or outcome of that "mechanism".  So does R^2 quantify the mechanism or the outcome of the mechanism?  This is not clear, and the manuscript at various points implies both.  Thus, that R^2 may or may not tell us something about "stability" is just as unclear as what it may or may not be telling us about "control".  It remains true that there is still no independent or direct measure of "stability" reported here.
Again, I see 2 legitimate options here:  One is for the authors to provide such a measure (I had previously recommended MoS / XCoM, but there are others).  The alternative option is to remove references to "stability" and to describe the findings directly in terms of what the dependent measures themselves ACTUALLY calculate.  With regard to R^2 for example, Wang & Srinivasan (2014) state "Thus, most conservatively, our results are only about the pelvis state’s predictive ability of the next foot position."  This is factually correct.  To go beyond this (e.g., to "control" or to "stability", etc.) is speculation.


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: GENETIC CHANGES IN THE EPAS1 GENE BETWEEN TIBETAN AND HAN ETHNIC GROUPS AND ADAPTATION TO THE PLATEAU HYPOXIC ENVIRONMENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: It fails
Experimental design: It fails
Validity of the findings: Some novel findings but would need to be rewritten, see my detailed critiques.
Additional comments: see highlighted portions of the manuscript with specific comments and suggestions fair revision