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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART II—A NEW APPROACH TO INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT TETRAPOD VERTEBRATES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I am happier with the further justification and caveats the authors have added, although I still have a few minor comments:

- "For one species, this took an estimated 300–350 hours to perform". Could the authors please include this information in the text then? Both as a justification for their small sample size, and to allow readers to judge if technique is suitable for their future needs.

- Admittedly, I have gotten caught up on the extent to which the authors’ protocol can predict a particular (mid-stance) posture. I accept that the authors are instead trying to link trabecular fabric to a ‘characteristic’ posture, which is mentioned in the Intro and Results (ln 860). Thank you for the clarification in the Discussion Ln 977. Please could the authors just add something in the Discussion clarifying that, in the future, we need to figure out what the ‘characteristic posture’ is actually telling us about locomotor biomechanics? It’s nice to calculate this time- and load-averaged characteristic posture, but it is inevitable that people are going to want to apply this technique to say something quite specific about the biomechanical performance of an extinct taxa. What might ‘characteristic posture’ be a useful predictor of?

- Re Ln 764-767: This is fine. But please also reiterate for clarity in the first paragraph of the Results section that the ‘best’ posture represents both the quantitative minimizing of angular deviation AND qualitative visual inspection of the stress trajectories.

- Re Ln 153: I’m still not sure the authors have clarified when convergence was reached. “Until no further improvement was gained” is not repeatable. How do you define ‘further improvement’? Also, I don’t understand how the authors can produce 8 models and decide that convergence had been reached on the final 8th model. Surely you need to overshoot, produce 9-10 models and check that no further improvements can be made.

- Re: authors response "The fabric orientation in the bones of the chickens studied in Part I were quantified via fabric analysis and plotted on steroplots. Moreover, these plots fell well within the region of space occupied by modern birds. We have now reminded the reader of this fact (and more broadly, why a chicken was chosen as our model species) with a new paragraph in the revised Methods section (pages 6-7, lines 197-205)"

This still seems a little odd to me. So we do have some (albeit limited) quantitative data about the chicken fabric orientation from Part 1 to compare the simulation to. But instead of drawing a species-specific comparison (checking the simulated chicken matches a real chicken), the authors are comparing to an all-bird average. But Figure 22 of Part 1 clearly shows the chickens sit off to one side of the all-bird mean for the femoral head.

At least for this region, please can the authors comment on how well stress direction predicted for the chicken corresponds to fabric orientation as quantified in the femoral head of chickens in Part 1? What is the angular deviation in this region?


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART II—A NEW APPROACH TO INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT TETRAPOD VERTEBRATES
Review round: 2
Reviewer: 2

Output:
Basic reporting: All four criteria are met, especially number 2.
Experimental design: All four criteria are met.
Validity of the findings: All four criteria are met.
Additional comments: I found this paper to be an improvement on the earlier version. It is a bit long-winded, but this may be a result of having to keep 6 authors happy. I only saw two wording mistakes:

Line 218: "none-to-node"? Do you not mean "node-to-node"?
Line 855: "facies"?  Do you not mean "faces" or "facets".


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART II—A NEW APPROACH TO INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT TETRAPOD VERTEBRATES
Review round: 2
Reviewer: 3

Output:
Basic reporting: Already-good basic reporting has improved concomitantly with the minor review suggestions.

The methods figures are instructive and vivid. Some figures (especially in the results) can be improved with labelling, legends, and boxes around related images (see suggestions on commented manuscript).

Perhaps I missed something, but why is the pelvis mass so much greater than those of the limb segments? Does it represent the mass of the whole body, minus the hind legs?
Experimental design: Although I agree with other reviewers' vision of an ideal study with vast comparative scope, the authors now better explain their focus on the chicken model and localized parts of bones. The finite element approach is great, with clever touches involving joint forces and soft tissues.
Validity of the findings: Given the paper's stated focus, the findings are valid. Matches of principal stress and fabric fields aren't perfect, but the authors are clear about the exploratory implications of the work.
Additional comments: Detailed suggestions are on the commented manuscript. The authors can consider that some principal stresses may be constraint artifacts reflecting motion in life, the converse of not finding torsion at the tibia mid-shaft seen in-vivo. Bell et al. (2009) found stresses in hadrosaur jaws that suggesting torsion when rigidly constrained, indicating that in life the dentaries actually rotated about their long axis (likely given their articulation the the predentaries).


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART III—INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT THEROPODS, AND ITS EVOLUTION ON THE LINE TO BIRDS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The basic grammar and structure are fine. It is not clear whether the authors are going to made their raw scan data and models available.

More clarity is needed in the methods section with regards to how trabecular fabric orientation and stress orientation were compared in the two species. In Part II, the chicken stress trajectories were compared to the mean for all birds. Yet here it seems that the Troodon FEA results were compared to the Troodon fabric orientation from Part I, and the Daspletosaurus FEA results were compared to Allosaurus and tyrannosaurids? If so, this needs to be made clear in text.

Additionally, Troodon was microCT’d and subject to protocol 4 in Part I. Whereas Daspletosaurus was vet CT’d and subject to protocol 5. Which means we have quantitative data for trabecular fabric in Troodon, but qualitative data for Daspletosaurus. Given the very different sources of data, do the authors think it is then fair to incorporate these different measures of trabecular fabric into a comparative analysis and treat them as if they were equal? Furthermore, how do you make the comparisons? In Troodon, do we compare FEA stress trajectories from the “sphere of radius one-half of that fit to the entire femoral head” (Part II) for example, to trabecular orientation calculated from the same sphere, in order to find region-to-region correspondence? Could this get around the issue highlighted in Ln 830-832, that by only considering mean direction in the medial femoral condyles, you fail to account for the ‘fan’ of individual vectors?
Experimental design: Ln 123 – “appear to be linked”. The premise for this Part III would be far more convincing if a robust statistical correlation between cancellous bone architecture and locomotor biomechanics had been attempted in Part I.

Ln 146 – “a single characteristic posture”, and Ln 189 “best guess”. I question the degree to which any ‘evolutionary shifts’ in locomotor repertoire can be robustly identified, when based upon 3 models’ ‘characteristic posture’ but with no idea of intraspecific variation or modelling error.

If we refer to Figure 22B in Part I, we can see the considerable intraspecific variation present in the femoral head trabecular architecture of the chicken (in red). Indeed, the spacing between the two chicken samples appears roughly equivalent to the distance between the Troodon (Figure 22A green) and the Allosaurus + tyrannosaurids (Figure 22A purple), between which we are trying to identify these big evolutionary shifts. How confident can the authors be that these evolutionary patterns in posture would still hold given larger sample sizes and incorporating modelling error?

According to Table 1 in Part I, the authors microCT’d a second troodontid. How variable was the trabecular architecture between these two specimens? Why not repeat this modelling process with the second specimen and get a handle on how much intraspecific variation is present in the resulting ‘characteristic posture’?

Ln 328 – “modified appropriately”. Modified how? Scaled to match segment length?

Ln 423 – “solution posture”. How was this decided on? When did the authors decide that convergence had been achieved? Looking at Fig 4 A-B, it appears that angular deviation converged much more in Daspletosaurus than Troodon. Do the authors believe that further convergence genuinely could not be achieved in Troodon, even if the modelling approach was more automated to facilitate an optimisation loop between MBDA output and FEA input? It seems unjust to compare the characteristic postures of the two fossils in an evolutionary context, when the modelling protocol has converged on a solution to a greater extent in one taxa than another.

Ln 474 – How was this cylinder fitted? By eye? Least squares alignment?

Ln 515 – What postures where these? A table or a figure would be nice to visualise the suite of different postures attempted.

Ln 526 – How bad is ‘minimal correspondence’?

Ln 550 – What were the actual angular deviations in the tibia and fibula?
Validity of the findings: In this paper, much is made of testing evolutionary hypotheses regarding posture and locomotor behaviour along the theropod line. The authors' conclusions hang on interpreting potential postural and muscle activation ‘shifts’ between the 3 models, from ‘basal’ Daspletosaurus to ‘derived’ Troodon, and then the modern chicken. The authors find that Daspletosaurus had a largely upright posture, whilst Troodon “is inferred to have been more crouched, although not to be degree observed in modern birds” (ln637).

However, if we look at Figure 22 of Part I, the green dot representing Troodon’s femoral trabeculae fabric falls easily within the cluster of points representing modern birds, as does the purple area representing Allosaurus and tyrannosaurids. The same is true for Figure 29 and the medial femoral condyle. Stereoplots of the tibia are not included so I can’t comment on them. So when the authors say in Part II (ln 738) “it has been shown that birds as a whole appear to demonstrate a largely consistent pattern of cancellous bone architecture in the femur”, surely this also has to include the two fossil taxa studied in Part III?

Given that the two fossil species appear to overlap in trabecular fabric with modern birds, how is this a justification for trying to reconstruct postural evolution on the basis on trabeculae? And given that the modelling approach taken did indeed produce models of different posture, is it possible that the ‘trends’ the authors are interpreting  (Ln 721-724) is actually just within the range that would characterise modern birds? I would be far more convinced of the authors findings if they also made a model of a large ratite or such in Part II. Given the findings of Bishop et al. (PLoS paper, Fig 1), the ‘postural space’ occupied by modern birds could be defined by including 2 taxa with short and long leg lengths. If the fossil taxa then fell outside that range, you could begin to interpret the fossils as being significantly different to the extant sample. This just highlights the issues with taking such a complex modelling approach, the sample size is too small to really be confident in the patterns we’re trying to interpret.
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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART III—INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT THEROPODS, AND ITS EVOLUTION ON THE LINE TO BIRDS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: nothing to add
Additional comments: This was a much easier read compared to previous two installments. Maybe my brain had absorbed enough of the large number of details of the materials and methods by this point.

I was pleased to see the general agreement between earlier anatomically inferred aspects of theropod hindlimb posture and the new quantitatively derived results. I realize that the present method is very new and that a perfect match between computed forces and bone anatomy is not likely at this early stage. The final results presented in Part III represent the outcome of a HUGE amount of work that was summarized in Parts I and II.

Some general comments about the text and figures follow, but not nearly as many as with the other two reviews.

Line 168/9: I found it a nuisance to have to dig out figure 8 from Part I. This was especially so once I saw it was just a reference to a cladogram with named nodes that I was already familiar with. It would be better to have the images immediately available.

Paragraph beginning at Line 502: large tyrannosaurids are very derived coelurosaurs and 2 orders of magnitude more massive than most maniraptorans. I think it is stretching the data too far to claim that the massive limb bones of a Daspletosaurus are representative of the primitive.ancestral state for animals like Troodon. However, the Troodon to Gallus comparisons and linking are tolerable.

Line 565: the technical term "decent" as a statement of the degree of correspondence between stresses and trabecular vectors is not sufficient. A more quantitative/statistical measure of the agreement/alignment is really needed here.

Line 660: I am puzzled how a surface can be simultaneously "smooth" and "wrinkled". Please explain.

Figure 4: I would really like to see the full, 3Dskeletal views of the intermediate postures showing the trajectory towards the solution pose. The obscured, gray stick views don't really illustrate the story.

Figures 5 - 10: I would really like to see images of the original cancellous bone immediately adjacent to the computed stress fields computed for the bone. To make room for these cancellous views I think many of the multiple views of the stress fields could be dropped.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART III—INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT THEROPODS, AND ITS EVOLUTION ON THE LINE TO BIRDS
Review round: 1
Reviewer: 3

Output:
Basic reporting: "Validity of the findings" and the commented manuscript have suggestions for additional references.
For Figure 3, a large anterior view of the optimal posture would better show the degree of ab/adduction of the femur. The dorsal oblique views obscure the angles. Figure 4 shows the posture for the entire hindlimb, but a close-up of the hip and femur is warranted.
Experimental design: As with the companion manuscripts, the study design is well-conceived and executed. The modeling of the distal crus and metatarsal region of Daspletosaurus is rather cartoony, but not an issue for the study's results.

Also as in the previous manuscripts, be a little careful about "basal". Traits can more or less resemble the ancestral condition, but taxa have their own specializations outside the dazzling attractor of interest (crouched limbs in extant birds). A minor issue worth just one or two slight modifications in the text.
Validity of the findings: The conclusions are certainly valid and intriguing, especially the likely sagittal orientation of Daspletosaurus's femur. I suggest adding a note and references about the arctometatarsus in "Correspondence of the distal tibiotarsus".
Additional comments: Mind-expanding results on limb posture in large theropods. The big deal here for me is how one can be a three-tonne biped, which speaks to the broad interest and applicability of the work. The series of manuscripts is a landmark of consilient methods.


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

Input:
Title: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART III—INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT THEROPODS, AND ITS EVOLUTION ON THE LINE TO BIRDS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I'd like to thank the authors for their considered and detailed response to my concerns. I do understand that the work presented comprised part of the lead author's PhD, and I am sympathetic to their limited ability to re-run analyses. I do think this research is a novel development and has a lot of promise for palaeo biomechanics.

My concerns have always stemmed from the complexity and time-consuming nature of the method, and linked to that, the relatively limited validation carried out on modern taxa. Palaeo biomechanics are often very quick to adopt exciting new methods, and sometimes I think that comes at the expense of truly understanding the processes at play in modern taxa. I have sympathy, applying the method to a T. rex is more exciting than an ostrich. However I also believe that, in terms of validation studies, if the originating authors aren't going to do it, who will? I worry that others take this method and apply it to other fossil taxa without taking the time to understand how well it works in modern species.

Ultimately, the authors have added several caveats and areas of discussion to cover these points, and the manuscript is at the point where it is acceptable for publication. It's just unfortunate that the methodological complexity and the authors' circumstances do not permit further testing on modern taxa.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART III—INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT THEROPODS, AND ITS EVOLUTION ON THE LINE TO BIRDS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Refined presentation throughout. The anterior full-leg posture figures for the theropods are instructive. Consider more legends, labeling, and delineated clustering for some figures.

Replace neutral axis with neutral surface, the more exacting term from structural mechanics.

Clarify that M* is dimensionless, rather than an effort to divide torque by gravitational potential energy. It's an elegant way of comparing necessary musculoskeletal torques across body sizes!
Experimental design: The authors' musculoskeletal reconstructions involve a tremendous amount of well-judged effort.
Validity of the findings: The authors explain their three-taxon sample as proxies for evolutionary change, and a proof-of-concept for larger samples and more resolving or complex methods. As in the original manuscript, Daspletosaurus's small ad- and abduction of segments are revelatory for posture of large theropods.
Additional comments: The authors pay thoughtful attention to edits, suggestions, and comments on the original manuscript.

The explanation of the pelvic segment is quite clear here, in the original manuscript, and in iterations of Part II (which I missed when reviewing the Part II revision). Perhaps in relevant captions for both manuscripts, say that pelvic segment represents the mass of the body and one leg.


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 RESPIRATION OF A MOSO BAMBOO FOREST SIGNIFICANTLY AFFECTED BY GROSS ECOSYSTEM PRODUCTIVITY AND LEAF AREA INDEX IN AN EXTREME DROUGHT EVENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: Please see the "General comments for the author" section and the attachment.
Experimental design: This is a primary research article and it is within the Aim and Scope of the journal. The question addressed in this piece is relevant, which is based on knowledge gap on soil respiration and its drivers in Moso bamboo forest. Overall, the experimental design undertaken for this study is standard and sufficient details have been provided to ensure replication.
Validity of the findings: A better understanding of the biotic and abiotic drivers of soil respiration is prerequisite for estimating ecosystem carbon budget. To that end, the findings in this article are valid and one of its first kind as the study was conducted in one of the important forest ecosystems of China.
Additional comments: Liu et al., evaluated the dynamics of soil respiration within a tower footprint in a Moso bamboo forest of SE China. Overall, the results are straight forward. However, some work is still needed to facilitate a better flow of the story. Additionally, authors need to pay attention to grammatical errors (and terminology) before final submission. See the attached pdf for more details.
Also appreciate sharing the raw data. However, adding a README file will be useful for a short description of the columns (and units) related to each variable.


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 RESPIRATION OF A MOSO BAMBOO FOREST SIGNIFICANTLY AFFECTED BY GROSS ECOSYSTEM PRODUCTIVITY AND LEAF AREA INDEX IN AN EXTREME DROUGHT EVENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language quality starts very promising, but unfortunately drops at several points, most noteworthy the Materials and Methods section - almost looks as if someone else has written (or strongly edited) different parts. As a non-native speaker, I can only give a few examples (see general comments). The paper should be thoroughly checked, e.g. by whoever checked the introduction.

I am not familar with the (interesting) concept of asking submitters to provide raw data and asking referees explicitly to judge from them, and from the presented figures and tables, if there was any inappropriate manipulation. Of course I would report signs of manipulation if stumbling accross them, but I don't think that most (especially "well-done") types of manipulation can be excluded this way. I am unsure how strict the request to submit raw data should be interpreted, but maybe I should mention that the data submitted by the authors are not "raw data" in the strict sense. The closest match to "raw data" for this study would be the so-called "*.81x" files produced by the software of the chamber manufacturer (Li-Cor). They require a special (but free) software to conveniently look at, but can also be read with a simple text editor and would make undetected manipulation harder.
Experimental design: The design has all ingredients for a comprehensive successful study focused on but not limited to soil respiration, especially given the fact that LAI and eddy-covariance measurements of NEE are at hand. However, the potential of these extra data seems only partly exploited.

One point that requires a clearer description in the methods section and more presentation of different raw/aggregated states of the results is that despite using an automated chamber system, measurements were apparently performed only on selected days. Please get clearer about the reasons, the strategy resulting from it (see also general comments) and the resulting number of available raw data points.
Validity of the findings: The presented results look sound (apart from the fact that it would be good to also show some not-yet-aggregated diurnal cycyles), but the discussion is sometimes speculative and sometimes superficial.
Additional comments: L 58: Maybe consider replacing the "kingdom" by a more objective description, e.g. if China has the largest bamboo area or production, mention this.

L 62-64: It would be interesting to briefly report which former ecosystems or land use types are replaced by this growth.

L84-87: Sentence unclear (why "As.."/where is the verb?). Also it is unclear which data are from measurements and where the classification comes in. Give reference for the classification if possible.

L88: This number makes no sense without telling how the accumulation was done, e.g. adding mean temperatures of each day above 10°C? Then technically the unit is °C*day, not °C. If this is a common technique give the reference.

L89: Language example: are (here), not were, because the showing happens now. Similarly at L 93, "was" suggests that the area of the forest is not 1687 ha anymore now that the manuscript is submitted. Past tense is important in scientific papers, but only appropriate where events / methods / results really ARE past.

L100: (which are the even YEARS at our site) (clearer). Maybe it would be good to introduce this sentence with a more general one (I could only guess what you mean), e.g. something like "(This species of?) bamboo has alternating "off" and "on" years, in which the ... differs."

L113: Was this treatment repeated during the year, especially the growing season? If not, wasn't it necessary?

L117: How was the theta probe inserted? Permanently or for each of the measurements indicatd at Line 118? Horizontally or vertically?

L118: I do not understand. Typically the automated multiplexed system is used for continuous measurements, while "on selected days (about every two weeks)" sounds more like a manual survey measurement. How was the multiplexer exactly used - for all 4 plots or moving from plot to plot? What is meant by "mid-month"?

L133: then?

L134: grammar: reported as ... were chosen. Alspo try to avoid repeating "reported" between this and the next sentence, especiyll since they are about the same variable. Next sentence: For THE EC technique...

L138: How high was the bamboo canopy?

L140: Give more details on the processing - which corrections and quality checks? Which software?

L140 & 149: Not sure "whilst" is used appropriately.

L151: analysis was or analyses were

L160: "whilst" probably inappropriate

L162: mostLY

L164: shows

L166: exhibit instead of presented

Fig. 1: Replace "in long-term average" by "(long-term average)", drop sentence " legend shown as in figure"

Fig. 3: b also capital or all subfigure letters small

L186: Language example: "It (...)" - change construction.

L192: The word soil "surface" temperature seems to be newly introduced here. In the methods section the symbol Ts was used for a temperature measurement at 5 cm depth directly attached to the respiration chamber and I could not find TS5. I guess the Ts symbols with numbers refer to the Campbell array, but this does not seem to be explicitly mentioned and Ts and Ts5 is a bit strange to distinguish two temperature measurements that were both done at 5 cm.

L195-230: Do the R and R2 values refer to same regression analysis used to determine Q10 values (i.e. Rs was log-transformed) or are they strictly linear typical R values? Make clear.

L237: commonly what?

L236-263: The discussion of Ts-Rs relations at different depths, hystereses and phase shifts ignores the effect of heat transport in the soil, which has been abundantly discussed in the literature; one of the outcome of such studies was that the temperature measurement depth of highest R² does not necessarily indicate the prominent depth of respiration (as suggested at L249) or the "correct" Q10 value (e.g. Graf et al. 2008, Biogeosciences 5:1175).

L264-277: As far as I know the general expectation about SWC-Rs relations is that it is an optimum curve: At low to medium SWC, Rs depends positively on it because water is limiting, then there might be a plateau and at high SWC oxygen transport to the soil depth and transport of CO2 back might be blocked. Besides confounding effects with temperature which are briefly discussed but not throroughly checked, the reason for a nonexistent or negative linear correlation between SWC and Rs can therefore also be that the natural variation of SWC covers only a part of this curve.

L278: Unclear why the discussion now goes back to temperature relations, shouldn't this better be addressed directly with L236-263?

L281: No evidence is presented to support the hypothesis that soil moisture causes the different Q10 values in different seasons.

L329: Language example: "No obvious related..."?

L333-334: language example: "exhibited" twice close to each other.


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 RESPIRATION OF A MOSO BAMBOO FOREST SIGNIFICANTLY AFFECTED BY GROSS ECOSYSTEM PRODUCTIVITY AND LEAF AREA INDEX IN AN EXTREME DROUGHT EVENT
Review round: 1
Reviewer: 3

Output:
Basic reporting: a) English language should be deeply revised. Some parts of the manuscript are not easy to understand because of that. Just some examples in the abstract where the language could be improved: L21, L22, L24 or L27
b) References is one of the most important parts of a manuscript since establishes the foundation of the research. References should be carefully revised, since some of them are not related with the referred section (e.g. McDowell 2015 in L55)
c) The abstract should be improved and better organized. It directly starts with what the authors did, without introducing the state of the art or why was important measuring soil respiration in that forest. The goal of the study is not reflected in the abstract.
d) Introduction is well structured, but detailed goals of the manuscript are required. They sounds too general compared with results and discussion section.
e) Results and discussion section are confusing and topics order is not always logical. At some points, the reader could be lost.
Experimental design: Research presented in this study perfectly fits with the scope of the journal. Temporal variability of soil respiration and their relation with drivers has been largely studied for decades, and it does not seem that the way data is analyzed and presented is useful for filling a knowledge gap in the topic. Experimental design looks robust, but some important information on that section is missing (e.g. how different blocs are analyzed, how often Rs was measured (see specific comments below))
Validity of the findings: In my opinion, statistical approach was not the most appropriate for studying the aims of this study. I guess that the authors have good data for testing them, but the approach was not optimum. For instance, one of the aims of the study (distinguish the effect of different Rs drivers temporally autocorrelated) could not be tested just with direct correlations or multiple correlations. Interactions between drivers, such as SWC and temperature, should be tested. Additionally, relations between Rs and ecosystem productivity are poorly explored in the manuscript. I would suggest to the authors explore mixed effects models for analyzing the data. In addition, some of the conclusions are not well supported by the analysis.
Additional comments: In my opinion, the goals of the manuscript are interesting for the community and they have the enough data for addressing those goals. However, the used statistical approach and the way results are presented is not appropriate. The structure of the manuscript should be improved as well.

At certain points, results section looks like exploratory results. The authors showed a lot of figures (up to 24 panels), but many of them are not really related with the main goals of the manuscript (e.g. 2A, 2B, 2C, 3E). Accordingly, Discussion section is a little confusing and disconnected with the aims of the study.

Some specific comments for improving the manuscript:

L40 and L44-46. Why factors determining Rs are described in separated places? I guess they should be described together.
L49-51. Relation between productivity and Rs well demonstrated in many papers since decades, so this relationship is not a suggestion but a proved fact.
L55-58. This sentence is confusing.
L74-75. Redundant with the previous statement.
L87-89. I have never seen Effective accumulated temperature or Sunshine accumulated hours in soil respiration papers. Are these information relevant for the study?
L93. Flux tower? I guess you are talking about Eddy covariance flux tower. The way this is explained looks like the readers already know there was a tower, which is not the case.
L93-95. This sentence is confusing.
L106-107. LI-8150 is just a multiplexer. The authors should include information on the used analyzer (probably LI-8100?) and the chambers model.
L108. Which is the distance between plots? It seems that they are completely adjacent due to tubing limitations from the multiplexer. If so, why consider four plots with four replicates each one instead of 16 chambers randomly distributed nearby the tower?
L112. 24h after insertion is not enough for avoiding disturbance influence, considering that many fine roots may be cut in the first 5 cm of soil.
L114. The authors should explain this section in more detail. They did not say that they were performing automatic measurements.
L118-119. This should be better explained. It is still not clear when measurements were performed.
L132. When was LAI measured?
L144-145. Why the authors calculated Rs with temperature if they already measured Rs? This should be clarified.
L155. Results section is too long compared to other sections. Additionally, the way this section is explained is not fluent (e.g. As can be seen in figure 1…, Figure 2 shows…, Table 2 showed…, We plotted…). It might not be just a plain description of each figure and table.
L180-181. The statement exhibiting the typical growth characteristic of Moso bamboo in an “on year” needs a citation.
L183-186. How significance in diurnal patterns was tested. Figure 3A shows that Rs did not presented diurnal cycles.
L187-189. This statement describes seasonal variability rather than  diurnal variations.
L190. Table 1 should be that one appearing earlier in the manuscript.
L193 and 221. The same thing explained at two different sites.
L194. See my comment on L144-145.
L211-219. This analysis should be explained in M&M section. Additionally, it is usually the interaction between SWC and temperature and not only their independently effect which controls RS.
L224. This should be explained in M&M section.
L246-251. This is not well supported by data.
L253-254. This could be just an artifact of measuring soil temperature at different depth from CO2 production.
L264-277. As mentioned before, the authors should test the interaction between SWC and temperature, and not the solely effect of each variable independently.
L278-279. This was not tested in the manuscript.
L316-322. This section is repetitive from the introduction.
Figure 5 is not explained. I don’t know what Rs residual means in Fig 5A or why they discard some points on Fig 5D.


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 RESPIRATION OF A MOSO BAMBOO FOREST SIGNIFICANTLY AFFECTED BY GROSS ECOSYSTEM PRODUCTIVITY AND LEAF AREA INDEX IN AN EXTREME DROUGHT EVENT
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am happy with the response and the modifications in the revised manuscript.
Experimental design: It is now appropriate.
Validity of the findings: findings are valid for carbon cycle research in terrestrial ecosystems
Additional comments: See my response to the basic reporting section


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 RESPIRATION OF A MOSO BAMBOO FOREST SIGNIFICANTLY AFFECTED BY GROSS ECOSYSTEM PRODUCTIVITY AND LEAF AREA INDEX IN AN EXTREME DROUGHT EVENT
Review round: 2
Reviewer: 2

Output:
Basic reporting: I am glad to see how the manuscript has been improved since the last version and I hope my comments and suggestions could be used to improve the current version. Used English is much more better (this was not a limitation for understanding the manuscript) but I guess it still needs another revision to be published in a scientific journal (just talking about English). However, I am not a native speaker and perhaps I am not the best one for checking the writing. Literature and references seems appropriate.
In my opinion, there is too much information in the figures not relevant for the goals of the manuscript. There are 23 different panels and some of them are not relevant for the paper (even not described or discussed) and could be easily removed (see detailed comments at the end of the General Comments section). Additionally, a figure showing the seasonal course of soil respiration was not included, which might be relevant since is the main goal of the manuscript. The study includes all results relevant to the hypothesis.
Experimental design: The hypothesis is somewhat general (i.e. “explore the temporal dynamics of soil respiration, and to identify the relative importance of the measured environmental factors”); and because the hypothesis is too general, the results section and discussion are somehow vague and not always well oriented with different results not completely connected in the discussion.
Validity of the findings: I have two main comments for this section. First, the main conclusions of the study are that soil temperature and moisture are important drivers of Rs and that productivity and phenology could also play an important role. Despite there are a lot of studies reporting similar results for Rs, the authors mentioned that this had not been previously studied for Mozo bamboo forests. Secondly, most of the conclusions in the paper are based on causality inferred from direct correlations between pairs of variables. However, a lot of drivers tested in the manuscript showed strong autocorrelation (such as soil temperature, LAI, GEP), and thus causality cannot be directly extrapolated from correlations by pairs.
Additional comments: Soil and air temperature are strongly autocorrelated variables, and that is why Rs relationship with both of them are so similar. However, we already know that Rs is driven by soil temperature (and not air temperature), so including for all the analysis relationships between Rs and air temperature is redundant.
L37. Replace Bondlamberty for Bond-Lamberty
L51. Latitude is not actually a driver of Rs, but there are several variables influencing Rs that change with latitude.
L56-58. This is confusing. Which role they play in the context of sustainable development? Are they storing more carbon that woody forests, do they have higher growing rates and lower turnover? I would suggest removing this sentence since it is already explained further in the manuscript (e.g. L68).
 L75. I would suggest scale back the tone of this sentence. An alternative would be “Thus, given the ecological importance of Moso bamboo forests at regional scale, there is a need for understanding the relationships between biotic and abiotic factors and Rs in this kind of ecosystem”.
L84. “… an eddy covariance flux tower…”
L88. “There are on average 2021 h of sunshine annually”. This information is somewhat strange. I suggest remove it.
L93. “The study area (1km around the eddy covariance flux tower) was covered by…”
L95. “the average canopy height was 11 m with a mean diameter at breast height of 9.3 cm”
L109. Replace “by the software of the manufacturer” by “(SoilFlux Pro, version…”
L120. I’m sorry, but I still found this a bit confusing. Were Rs only measured during daytime? In L108 you mentioned Rs was measured during 1 year, but here you said it was only during sunny days. Why did you remove the cloudy and rainy days? How do you think removing cloudy or rainy days would affect the calculation of annual Rs and your overall results, especially since you are studying the effect of moisture?
L125-131. Remove all information is not going to be used in the study. It is distracting. This also applies for the results section.
L127. “… close to the eddy covariance tower”
L146. Replace rejected by discarded
L150. See my comment on L 120.
L150-151. I do not understand point number 4.
L146-152. Are these QA/QC procedures commonly used for the eddy covariance community? If yes, provide a citation.
L154-155. Detailed information would be required here.
L156-158. This sentence could be removed since it is already explained previously.
L184-185. Do you mean warmest? It looks that several months were drier than July.
L193. Delete “value”
L202. It looks that for the most of seasons, there is no a diurnal cycle. How the authors tested for the significance of the diurnal cycles?
L209. I did comment on that at the last version of the manuscript. As far as I understood, you were using these equations for estimating the temperature sensitivity of Rs, not for estimating Rs. In fact, you don’t have to estimate Rs because you already measured it.
L210-211. Be careful with this kind of statements. Ts5 and Ta do not explain 69.7 and 63.9% of Rs variation. This are just correlations (or R2, to be more precise). Additionally, where did these numbers come from? They are mentioned even in the abstract and in the conclusions, but no figure or table seems to show them. Which statistical analysis has been made?
L216. I was wondering why the authors do not show a seasonal course of Rs. Instead of averaging the seasons as in Fig 3B you can show a kind of graph similar to those in Fig2A. At this point of the manuscript is still no clear how many days Rs was measured, so this figure could help on that.
L219-221. I would remove this sentence. It is a bit confusing and some of the information is already posted in the following sentence.
L222. Be aware that you are discarding all rainy and cloudy days, so your annual Rs might be overestimated.
L226. I have a couple of comments on this sentence.
a) In my opinion, it is still no clear the meaning of Fig5A. Which is the purpose of plotting LAI against residuals from Temp and SWC model? Do you want to test the effect of LAI on Rs without the effect of Temp and SWC? Doing that is challenging with variables that are strongly autocorrelated (such as Temp and LAI in your case), because you are overestimating the effect of temperature and thus, underestimating the effect of LAI. Additionally, which is the justification for using a parabolic fit in this figure? Which is the mechanistic explanation of a decrease in Rs when LAI goes higher than 4.5?
b) Temp, LAI and GEP are strongly auocorrelated (especially if GEP data from July and August are removed; Fig5D), so it’s logical that all of them showed a significant relation with Rs. Just be aware that direct causality cannot be inferred because of this autocorrelation.
L230-232. Which is the relevance of analyzing the relation between Rs and SWC if the effect of Temp*SWC interaction is already tested (Table 3)?
L238. Relation between Ts50 and Rs was not plotted.
L238. I guess that Fig3D is not relevant for the paper.
L239. Which is the difference between Ts and Ts5? (see L118 in the manuscript). Is Ts temperature measured close to each chamber and Ts5 temperature measured close to the tower? If yes, I think you should use the temperature measured close to the chambers regardless of the R2 they have with Rs.
L248-249. I am sorry, but I guess this statement is not fully supported by the results. As I mentioned before the autocorrelation between Temp, LAI and GEP is so high (as demonstrated in Table 2) that no direct conclusions can be taken from pairs of correlations.
L256-259. The lowest temperature sensitivity during summer was likely cause by low SWC values. During summer SWC became the limiting factor.
L261. I do not understand why hysteresis was mentioned here. Which is the relation between hysteresis and a decrease of temperature sensitivity during summer?
L280-283. I do not know if these potential explanations applies in your study case. Differences in photosynthetic supplies does not seem to be the reason because you have the larger hysteresis at winter, when LAI and GEP are the lowest. Similarly, SWC during winter was not a limiting factor, so the critical value explanation does not seem plausible.
L288-294. As you mentioned, this was probably an artifact. Rs has a positive relation with temperature and SWC During summer time, SWC was lower when temperature was higher, which has sense since soils get drier at higher temperatures. Thus, increments in temperature still produce an increase of Rs, despite SWC decreased. So the apparent negative effect of SWC was more related to the relation between SWC and Temp than a direct effect of SWC on Rs.
L294-298. I guess this is much more simple. SWC does not have effect because there were enough water in soil during all the year (just a little limitation in summer), so the limiting factor in your system was mainly temperature. Water shows usually significant effect at semiarid and arid ecosystems where there is enough temperature but water is limiting.
L333-334. In fig5 you are reporting month averages, which is not short-term relationships (comparing with results showing in Hogberg et al 2008). However, the authors have continuous Rs and GEP data, so this could be tested.
L336-337. Again, there is a strong correlation between LAI and temp which precludes the direct extrapolation of causality from correlations as you mention in the following sentence. Accordingly, “LAI reflected the productivity of vegetation” is not an accurate statement.
L349. The daily cycle of Rs has not been statistically tested and based on visual estimation from Fig3A is does not seem likely to be significant.
L351. In some parts of the manuscript, the authors said that temperature can explain 91.5% of Rs variability (Fig3C) and in other side it is said that temperature can explain 69.7%. Please, explain the difference and be consistent.
L352. Rs correlated negatively with SWC in summer (L231)
L353. Where did you test the diurnal effect of SWC on Rs?
L354-356. I do not understand this statement and I am lost finding the connection with the first part of the sentence. Additionally, I think this is too speculative to be in the conclusions of the manuscript.
Figures:
In my opinion, there is too much information in the figures not relevant for the goals of the manuscript
Fig2. SWC at different depths (B), NEE and RE (C) are not discussed in the paper. Consider remove them.
Fig3. Information placed in Fig3B is redundant with Fig3A, and Fig3D is not relevant for the study.
Fig4. As far as I understood, Ts5 was soil temperature measured at 5cm depth close to the EC tower and Ts was soil temperature measured close to each chamber during Rs measurement. I don’t know which extra information provides plotting hysteresis with the two soil temperatures. Since Ts was measured simultaneously with Rs close to the chamber, I would assume that Ts is more accurate and thus, I’d keep it. Accordingly, I would remove panels B, D, F and H.
Fig5. I still don’t understand panel A (see my comment above), and panel E has not been discussed in the entire paper. Additionally, revise the writing in the figure caption.
Table 3. It is the first time I’ve seen some of the equations you presented here for testing the relation between Rs and SCW and temperature [e.g. Rs=exp(a+b*Ts+c*SWC+d*Ts*SWC)]. Could you provide an explanation or a citation justifying why these equations have been selected?


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: TESTING THE HEAT DISSIPATION LIMITATION HYPOTHESIS: BASAL METABOLIC RATES OF ENDOTHERMS DECREASE WITH INCREASING UPPER AND LOWER CRITICAL TEMPERATURES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Its good. But some minor errors and inappropriate citations - see comments to authors.
Experimental design: Statistical analysis of prior data so no design issues
Validity of the findings: It is good validated data well analysed.
Additional comments: The heat dissipation limit theory was published about 8 years ago and emerged from work in lactating mice which indicated that a major factor limiting their performance is the ability to get rid of body heat generated as a by-product of metabolic activity. It has resonances in earlier work from the 1960s. The theory makes several testable predictions one of which is that for animals that routinely experience high temperatures there should be selection to simultaneously increase the upper-critical temperature and decrease the basal metabolic rate. However because thermal conductance influences both upper and lower critical levels this will also lead to links between body mass and lower critical temperature, and between the two critical temperatures.  This would then enable a greater metabolic scope at these high temperatures.  In the current paper the authors test this idea by looking for an inverse correlation between estimates of BMR and the two critical temperatures in 146 endotherms. The results confirm the basic prediction of the HDL theory.  The analysis is well performed and uses R to evaluate the phylogenetic signal in the data (which turns out to be unimportant).   Have a few minor comments and suggestions.

Minor comments:

lines 41-42: This is not correct because of the possibility of heat substitution. That is energy derived as a by-product of exercise might be employed for thermoregulation purposes (see for example the review on this process by Humphries and Careau). The result is that costs of thermoregulation and exercise are not always additive.
Line 43: Reproduction does not enhance long-term survival. Indeed it may have the opposite impact. From an evolutionary perspective therefore animals should apply the level of EE that maximizes fitness.
Line 74: actually this work under cold conditions was presented in Johnston and Speakman 2001 (JEB) not Krol and Speakman 2003, which concerned exposure to hot conditions. Note that perhaps the strongest support comes from the shaving experiments by Krol et al (2007) also in JEB.
Lines 84: The paper by Speakman 1997 is not the best reference here as it contains rather limited data. Perhaps a better reference is the review by Speakman 2000 in Advances in ecological research 30: 177-197. There is a more direct independent evaluation of the HDL predictions with respect to DEE  in Hudson et al 2013 (J animal ecology 82: 1009-1020)
Line 116: you should probably add the Hudson et al 2013 paper referred to above to this list of supporting evidence. Plus there is also lots of additional support, in studies of other lactating small mammals – see e.g. Sadowska et al 2016, timing of behavior (eg in wild dogs) and many other studies. If you scroll through the 200 or so papers that have cited the original presentation of the heat dissipation theory (Speakman and Krol 2010 in JAE) you will find many such examples of supportive literature. Indeed these outweigh the failures to support the idea many fold. Yet your presentation here seems to imply almost an equal balance of support and refutation.
Results: can you also show the relation between Tuc and Tlc (mass and phylogeny corrected) since this is also an important consideration and part of a heat trade-off as you point out later in the discussion. Since you have the data it would be nice to show it.
Line 175: ‘your expectations’ or in line with predictions of the HDL theory?
Line 176-178: there seems to be some mix up in the scales of description and analysis here. The analysis concerns interspecific trends in evolutionary time but this discussion seems to refer to individual animals expose to high temperature and their short term metabolic responses.
Line 190: there is of course a very large debate surrounding these numbers and I think for a more balanced approach you should cite a range with a few more pertinent citations.

Very minor points

Line 71: date missing from Drent and Daan 1980
Line 165: change tense to past
Line 168: change tense to past
Line 360: the initials for Speakman are incorrect


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: TESTING THE HEAT DISSIPATION LIMITATION HYPOTHESIS: BASAL METABOLIC RATES OF ENDOTHERMS DECREASE WITH INCREASING UPPER AND LOWER CRITICAL TEMPERATURES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please see my General comments for the Authors
Experimental design: Please see my General comments for the Authors
Validity of the findings: Please see my General comments for the Authors
Additional comments: The manuscript submitted by Imran Khaliq and Christian Hof is timely because it explores the correlation between basal metabolic rate (BMR) and thermoneutral zone (TNZ) defined by lower and upper critical temperatures (LCT and UCT, respectively) in mammals and birds, in the context of their thermal adaptations to different climate conditions and the factors limiting their energy expenditure and performance. The mechanisms responsible for thermal adaptations are central to understand how endotherms respond to climate change.

Despite being potentially interesting, there many aspects of the paper that are confusing and somehow under-explored or not properly explained. The Authors aim to test the heat dissipation limit (HDL) hypothesis, by exploring its prediction that ‘BMR should be lower under higher metabolic critical temperatures’ (lines 26-27). This is a simplification as the exact position of LCT and UCT depends on the interplay between heat production (represented by BMR) and heat loss (represented by thermal conductance). The Authors completely ignore thermal conductance and focus on the correlation between BMR and LCT/UCT, thus testing the prediction that has never been generated by the HDL hypothesis. The Authors claim that both central and peripheral limitation hypotheses are inferior to the HDL hypothesis because ‘under cold conditions animals can elevate energy levels’ (lines 73 and 78). Please elaborate which aspects of energy expenditure are elevated, otherwise it is rather difficult to understand the difference between central vs peripheral limits and the reasoning behind the HDL idea, which is supposed to be tested in the ms. There is no such thing as ‘energy creation’ (line 72) – please correct accordingly (‘Energy cannot be created or destroyed, it can only be changed from one form to another’, see the work of Albert Einstein).

It is great to have the raw data (Supplementary Table 1), but these data have no units, so are of limited use. Both BMR and thermoregulatory curve are prone to seasonal changes and shifts (e.g., Stawski et al. 2017 on bank voles, S. Eryn McFarlane et al. 2018 on flycatchers, Levesque et al. 2018 on Tupaia). Do the Authors filter their data accordingly and use only one-season data to reduce the variability observed in Fig. 1?

I was rather surprised to read the assumption made by the Authors that ‘species with lower metabolic critical temperatures should be able to dissipate heat more efficiently than species with higher critical temperatures’ (lines 151-153). First of all, with low UCT, there will be more cases that Ta > UCT, which makes the animal prone to overheating. Secondly, the animals with low critical temperatures tend to have higher BMR (Fig. 1), so they are expected to have more problems with overheating, because the costs of maintenance are higher (?). What happens to the significance in Fig. 1d, after removing 3 data points from the top left corner? Please check Table 1 for typing errors.

Taking into account all these points, I do not think that the current version of the manuscript is suitable for publication in PeerJ.


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: TESTING THE HEAT DISSIPATION LIMITATION HYPOTHESIS: BASAL METABOLIC RATES OF ENDOTHERMS DECREASE WITH INCREASING UPPER AND LOWER CRITICAL TEMPERATURES
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am happy with the response of the authors to my review and the changes they have made
Experimental design: no comments to add
Validity of the findings: no comments to add
Additional comments: I think this is now acceptable


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: EFFECT OF OPERATIONAL PARAMETERS, CHARACTERIZATION AND ANTIBACTERIAL STUDIES OF GREEN SYNTHESIS OF SILVER NANOPARTICLES USING TITHONIA DIVERSIFOLIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: - The authors should carefully proofread the manuscript for English mistakes. I have not listed them all here but will point out a few.
- Some expressions such as “early in vogue” are ambiguous (line 27). I understand the appeal of creative writing, but it may confuse some readers.
- Line 27. “facing out” should be “phasing out”.
- Line 52, 221, 285, 298, Fig 4 (image and caption) says only “Bacillus” but this should be “Bacillus subtilis”
- The authors say 430 nm on lines 156 173, 182, 184, 242 but say 435 nm on lines 45, 45, 314. I think this should be consistent.
- Lines 79-81. These pharmacological properties of the flower should be cited.
- Lines 69, 283. In vitro and in vivo should be in italics.
- Throughout the manuscript these bacteria are called multi-drug resistant. I am not a specialist about bacteria, but I am wondering if these are multi-drug resistant species (e.g. MRSA). If I am wrong here, please disregard.
- Line 310. This should say “electron microscopic techniques”.
- Lines 319-320. The authors could note which bacteria are Gram Positive and which are Gram Negative. A small explanation (in the Discussion or maybe Introduction) about the difference could also be added elsewhere. This information may be helpful for readers whose focus is nanomaterials but not bacteria.
- Figure 2B. The IR peaks are hard to read, at least in the main text (the supplementary material one is fine). Perhaps the authors could make better labels for the important peaks that they mention in the text.
Experimental design: - Line 105. The cleaning process should be explained.
- Line 108. The phytochemical screening processes should be briefly explained here or elsewhere (Line 133, or lines 234-235) in the paper for the reader to understand. Many people interested in nanoparticle synthesis will have never heard of these tests.
- Line 114. Was the solution stirred or shaken? The supplementary material mentions “Agitating” but it is unclear what this means.
- For the antibacterial studies, it is not clear if the same amount of pure extract was used as is approximately present in the TD-AgNPs. I realise that this may be difficult to know exactly. If this authors have taken this into consideration, it should be mentioned somewhere.
Validity of the findings: - Lines 139-143. This is just a re-summary of the method. The results should be stated here.
- Line 158. The authors claim that 90 min is the optimum synthesis time. It certainly is better than the shorter time periods. Why did they not try a longer synthesis time? 90 min may not be the true optimum. If possible, the authors could examine longer synthesis time. If not, it could at least be discussed.
- Line 159. The authors could explain how these other studies support their findings.
- Line 161. “From the literature”… but there is no citation. Please cite whatever you have in mind.
- Lines 173-174. How does varying the concentration affect size and shape? This could be added here or in the Discussion.
- Line 180. The effect of UV-vis peak shape to nanoparticles with a broader size distribution is known among the nanoparticle community but may not be known to all readers. Accordingly, the authors should add a citation here.
- Line 193. The results should be described here. Again, it just seems like a repetition of the methods rather than a proper Results section.
- Lines 236-244. The authors could note that the room temperature synthesis is greener than the heated syntheses, which is a further advantage.
- Lines 247-248. This needs a reference.
- Lines 251-253. The authors should elaborate on the relation between the nanoparticle shape, SPR and TEM. They provide references, but do not actually explain how their data relate to these findings. This will improve their paper since it will be informative, rather than forcing the reader to look elsewhere.
- Lines 255-256. The rest of the FTIR seems fine, but is the 2240 cm-1 peak from C-H stretching? I am not an IR expert, but I am not aware of the C-H vibration here. The authors could improve the paper by providing a citation if this is truly the assignment.
- Lines 261-262. The authors could further explain their points here to make the paper better (similarly to the concern above about the nanoparticle shape, SPR and TEM). Again, what they have written is not wrong, but it is vague and makes the paper less useful (i.e. citable) for readers. I encourage the authors to go into greater detail to improve their paper.
- Line 266. The AgNPs look more round like a ball-shape than a rod-shape to me, especially in the TEM.
- Line 296. The authors note that the results were “analyzed statistically” and mention the standard deviation in one case (line 299). Error bars for should be added to Figure 4 to improve the graph.
- The authors note the TD-AgNPs work best against Bacillus. This is a useful finding. I also noticed however that in relative terms vs the positive control, the best case seems to be S. enterica. While not mandatory, this is something I would add to the manuscript.
Additional comments: Overall I have a good impression of this paper. I have noted many issues here, but my intention is simply for it to be improved. The issues are more with the manuscript and interpretation of the data, rather than problems with the experiments. My opinion is that this article is scientifically valid, and it could be accepted for publication in PeerJ after consideration of the various points I have noted above. These improvements as a major revision will provide further insight for the reader, and perhaps make the paper more citable.


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: EFFECT OF OPERATIONAL PARAMETERS, CHARACTERIZATION AND ANTIBACTERIAL STUDIES OF GREEN SYNTHESIS OF SILVER NANOPARTICLES USING TITHONIA DIVERSIFOLIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are too many grammer errors and odd sentences. The Figures are also not professional.
Experimental design: no comment.
Validity of the findings: Since 2008, there have been too many reports to synthesize the AgNPs using different plant extracts and microorganisms, including optimization conditions, characterization, and antibacterial test. Actually, researchers gradually concluded that most of the plants extracts can mediate the production of AgNPs at special conditions. The novelty and impact are not obvious for this manuscript, at least far from the standard of this journal.
Additional comments: The language should be revised completely, and the data such as UV-vis figures should be more professional. The main problem is lacking the obvious novelty and advanced impact.  The experiment design is complete, while it can't reach the standard of PeerJ.


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: EFFECT OF OPERATIONAL PARAMETERS, CHARACTERIZATION AND ANTIBACTERIAL STUDIES OF GREEN SYNTHESIS OF SILVER NANOPARTICLES USING TITHONIA DIVERSIFOLIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: There are numerous grammatical errors throughout the manuscript - examples are but not limited to….

1. vis-à-vis is not a scientific word and should not be used.
2. Line 126 - ‘used’ is wrong tense
3. Line 141 - ‘The colour intensified with increase in time’ no article before increase IE ‘with an increase’
4. line 106 - mL or ml
5. Formatting 1 or 2 spaces after a a period - be consistent.
6. SPR is defined multiple times after first use.
7. line 279-81 ‘It was observed that more inhibitory activity of the synthesized nanoparticles occurred more on Bacillus with inhibition zone of 15 34 mm than the rest of the microorganisms.’
8. line 224 - nitty-gritty is not a scientific word normally used.

A great deal of the references are greater than 5 years old, I find it difficult to believe there are not some relevant update references in this area.
Experimental design: This research fits into the aims and scope of the journal.

The gap in the research literature is identified and defined, the meaningfulness and relevance in the gap is not fully explained however.

For the experimental design the methods are described in sufficient detail to be reproduced and seem of a high technical and ethical standard.
Validity of the findings: The data is robust, and apart from fig 4 which has no error bars.

Figure 3 - (b) FTIR spectra is not analyzed for specific peaks relevant to the text or work

Conclusions seem to fit with original research question.
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: HAHAP: A READ-BASED HAPLOTYPING METHOD USING HIERARCHICAL ASSEMBLY
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I have several questions and suggestions of this paper
1.	Like WhatsHap and HapCut2, the authors should implement their algorithm as a software tool for public use.
2.	Can HAHap be used in organisms which do not have reference genomes?
3.	Why do authors use old hg19 genome in the simulate datasets? The authors should use the latest hg38 genome if possible.
4.	Why do the authors use the phasing error rate and perfect ratio as the only performance indices? Are there any other performance indices used in the existing algorithms? If yes, why not use them?
5.	The authors compared their algorithm with WhatsHap and HapCut2 only using one real data. I would like to see the comparison in the simulated data as well. In that case, I would be convinced that HAAap really outperforms WhatsHap and HapCut2.


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: HAHAP: A READ-BASED HAPLOTYPING METHOD USING HIERARCHICAL ASSEMBLY
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: The overall experimental design is clear and intuitive. The author applied the multinomial distribution to assess the confidence score between two variants, which is the fundamental of the HAHap. Since the confidence score is calculated from a likelihood-based method, I am wondering if the confidence score is affected by the sample size, (here, the sample size could be N). For example, the variant pair with larger N comes with higher confidence score. If it is so, the authors might need to discuss it.
Validity of the findings: The authors have provided the comprehensive comparisons between HAHap and the other two algorithms. All the bioinformatics algorithms/software are designed to investigate or help to investigate the biological science. I suggested that the authors might apply the HAHap to some real data and demonstrate that the HAHap is capable of identifying the well-known disease-associated haplotypes. Through this way, I believe that the applicability of the HAHap could be emphasized more to the readers.
Additional comments: 1. I noticed that, in the Fig. 4 and 5, the trends were changed at the block size of 300-400. I am wondering why this happened. The authors might discuss it in the main text.
2. I suggested the authors to add boxplots in Fig. 6 and 7 to show the difference of error rates between the evaluated algorithms. In addition, the paired Wilcoxon ranksum test could be helpful to assess the significance of the differences.


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: HAHAP: A READ-BASED HAPLOTYPING METHOD USING HIERARCHICAL ASSEMBLY
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors propose an approach for the (hierarchical) haplotype assembly of short reads whose objective function is the minimum error correction (MEC).

While this method may show promise, it is not quite clear from the exposition, what exactly is hierarchical assembly, and Figure 1 does not seem to make this any more clear.

Moreover, the discussion is not very deep, i.e., the MEC is not the only objective function to consider, and the authors miss out on much of the related literature.  Aside from this, different methods optimize the MEC in different ways, e.g., Whatshap is optimized for low-coverage long-reads (such as PacBio and ONT), and has since been augmented to consider pedigrees as an extra source of information for phasing.
Experimental design: For reasons that likely result from the problems indicated in the previous section, the experimental study seems inconsistent.  Indeed, the authors do consider a trio (a pedigree of size 3) of long PacBio reads — which is the ideal input for WhatsHap, for example — however there is nothing about whether HAHap also phases trios (or just single individual, like HapCUT2 considers, for example), let alone whether it works best for long reads (one would suppose not, since in the abstract it is stated that it is for “.. constructing haplotypes using short reads ..”.  Why not compare to HapCol, for example?  It was shown to outperform Whatshap in certain contexts such as this.  Moreover, using GATK as a ground truths seems out of date, since its ReadbackedPhasing project has been discontinued for at least a few years — one could rather use GIAB gold-standard phasings instead (available for Ashkenazim trio, as well as NA12878)

Also, the simulated study seems incomplete.  Why not compare HAHap to the other methods on the simulated data, where the ground truth is known?
Validity of the findings: no comment
Additional comments: For the above reasons, I believe the paper cannot be accepted as-is.  The exposition needs to be clearer, and a more consistent and comprehensive experimental setup needs to be carried out


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: HAHAP: A READ-BASED HAPLOTYPING METHOD USING HIERARCHICAL ASSEMBLY
Review round: 1
Reviewer: 4

Output:
Basic reporting: The paper “A read-based haplotyping methods using hierarchical assembly” introduces a novel phasing algorithm (HAHap). It uses hierarchical assembly to construct haplotypes from short read sequencing data. The authors aim to reduce the influence of sequencing or alignment errors on the phasing procedure. The idea is to assemble short haplotype fragments based on confidence scores computed for each pair of variants connected by sequencing reads.  In regions of low confidence, haplotype segments are combined based on locally applying minimum error correction (MEC).
HAHap was evaluated on real and simulated Illumina data. It was compared to WhatsHap and HapCut2, which both solve the minimum error correction problem (MEC) in order to derive haplotypes.

In general, the paper is well structured. In the introduction, the authors give a good overview of different approaches to phasing as well as strengths and weaknesses of existing methods.
Furthermore, the outline of their new algorithm is described clearly. The authors provide figures demonstrating how their algorithm works. They are generally useful and make it easier for the reader to understand the proposed method. However, it is not described how the local MEC-based search works which is applied in low confidence regions. Since this seems to be an important aspect, more details should be given.
In some parts of the paper (especially the evaluation section), the writing needs to be improved since language and notation are sometimes ambiguous, making it difficult for the reader to understand some parts of the paper (see Validity of the Findings and General Comments for examples).

The authors provide the data which was used for their evaluation experiments and their tool is publicly available.
Experimental design: As a motivation for their novel algorithm, the authors claim that the fact that MEC based approaches compute solutions in a global manner can lead to wrong haplotypes in noisy regions. This should be explained in more detail since intuitively, considering all positions together should be useful in detecting sequencing errors in the reads. At least a small example should be added to demonstrate this.

Furthermore, it is not clear which objective function the authors attempt to optimize with their method. In section 2.5, the authors claim that their algorithm is similar to solving a minimum spanning tree problem and that the solution can be interpreted as a minimum likelihood solution. This requires more explanation, since it is not clear why one is interested in the minimum and not the maximum likelihood solution.

The authors claim that HAHap successfully removes noise in the data and therefore leads to better phasing results than other approaches. However, they only evaluate their method on short reads with low sequencing error rates. In order to demonstrate that HAHap indeed better handles noise, experiments should be performed on long sequencing reads which are affected by much higher sequencing error rates and for which removing noise is essential in order to achieve good phasing results.
Validity of the findings: The authors describe how they evaluated their algorithm in detail. Besides performing experiments on simulated data, they also ran their algorithm on real data, showing that it is applicable to real world sequencing data. However, when describing their experiments, some definitions and terms are unclear, for example “phasing cases” is not properly defined. Similarly, it is not clear what the authors mean by “bins” and “bin sizes” (e.g. in line 282). This makes it difficult for the reader to understand the results presented in the paper.
Additionally, since data of a trio was used for evaluation, results should be given for each individual separately.

In general, the authors give a detailed discussion of the results and use several tables and plots to visualize the most important aspects.
Additional comments: Line 147: what is meant by  “each pair of the two connected variants”?

Line 161: the notation is not clear. What is c?

In Figure 2 (b), CS1 and CS2 is used to refer to the confidence scores of the two haplotype solutions. The notation should be introduced in the text.

Line 241: formulation is confusing. “The term 'phased variant' is how many variants are phased in the group 'variant needing to be phased'” suggests that these terms refer to groups of variants, but the names indicate that single variants are considered.

Line 254: when defining the perfect ratio, it is unclear what is meant by “error free phasing cases” or “total number of cases”. What is a case?

Line 273: Why was GATK run additionally when variant positions and genotypes where provided by GIAB already as mentioned earlier? And also, it should be mentioned how many variants are in the intersection.

When trying to run HAHap on a small example region, it gave this error:
ValueError: invalid literal for int() with base 10: 'chr3'


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: HAHAP: A READ-BASED HAPLOTYPING METHOD USING HIERARCHICAL ASSEMBLY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The basic reporting seems fine now.  The authors state clearly that they perform phasing on single individual, short-read datasets, and explain more thoroughly the methodology -- with an added figure -- clearing up any previous confusion.  The method seems novel, offering some value to haplotype phasing.

I can only offer some minor comments here, such as cleaning up the grammar/language, for example (sec. 2.4.1), "mergences" is so rarely used that I had to look it up -- it is a synonym of "merging", so I think it would be better to simply say "merging", i.e., "Embedded Merging"
Experimental design: It is now clear that HAHap is focused only on single-individual short-read data.  Based on the improved explanation of the methodology, it is clear that HAHap can do much better in this setting of high-coverage noisy short-read data than, e.g., Whatshap, since Whatshap has been designed for low-coverage (also with noise, but from indels) long-read data, with the goal of phasing the largest haplotype blocks as possible.  It seems, then, that this comparison -- to Whatshap, maybe HapCut2 as well -- is a bit out of scope.

A possible way to reconcile this, is in addition to computing accuracy (phasing error rate, etc.), is to compute also the _recall_, e.g., quality-adjusted N50 (QAN50) score, see:

Duitama J, et al. Fosmid-based whole genome haplotyping of a HapMap trio child: evaluation of single individual haplotyping techniques. Nucleic Acids Research. 2012; 40:2041–2053.

However, it is certain that short-read data has limited capabilities to obtain good recall (as reflected in good QAN50 scores, for example) -- one of the reasons haplotyping has largely moved to long-reads, since the goal is to assemble long haplotype blocks.

And it is because haplotyping has largely moved to long-reads, that methods optimized for short reads reached its peak some years ago -- this is why methods like Whatshap and HapCut2 are considered state-of-the-art.

So, maybe it is more appropriate to compare against such short-read methods which were very good for their time, for example:

He, D., Choi, A., Pipatsrisawat, K. et al. 2010. Optimal algorithms for haplotype assembly from whole-genome sequence data. Bioinformatics 26, i183–i190.

which is a dynamic programming algorithm (much like Whatshap), but is fixed parameter tractable (FPT) in the read length (Whatshap is FPT in the coverage, hence it dealing with limited coverages) -- allowing it to scale to the 100s-X coverage that Illumina reads have.  Another example is:

Chen, Z.-Z., Deng, F., and Wang, L. 2013. Exact algorithms for haplotype assembly from whole-genome sequence data. Bioinformatics 29, 1938–1945.

which is an integer linear programming (ILP) approach that performs _very_ well on short-read datasets.
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: HAHAP: A READ-BASED HAPLOTYPING METHOD USING HIERARCHICAL ASSEMBLY
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors addressed the concerns mentioned in the reviews and improved their manuscript.

Parts of the Evaluation Section were rewritten and are clearer now.
Experimental design: The local MEC-based search implemented in HAHap is now described in more detail.
Furthermore, the authors added an example to demonstrate how HAHap differs from MEC-based approaches in noisy regions.

Unfortunately, it is still unclear which objective function the authors attempt to optimize.
They mention that their method solves a minimum spanning tree problem. Likelihoods are used as edge weights. How is a minimum spanning tree helpful if the aim is to maximize the likelihood?
This section is still confusing and requires explanation.
Validity of the findings: Definitions and formulations are clearer now.

The authors used their algorithm for blood group detection based on short reads.
Unfortunately it is not clear what exactly was done in this experiment. The authors should explain in more detail how haplotyping helped to determine subtypes.
Additional comments: Still there is an error when running HAHap on a small Illumina dataset.
"KeyError: 'PG'"


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: USING STIFFNESS TO ASSESS INJURY RISK: COMPARISON OF METHODS FOR QUANTIFYING STIFFNESS AND THEIR RELIABILITY IN TRIATHLETES
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment
Additional comments: Only some minor points:

Line 138-139: Please provide a references for this sentence.
Line 248-250: Please provide a references for this sentence.
Line 250-251: Please provide a references for this sentence.
Line 345: Please reconsider the wording "...reliability to moderate to good.
Line 382: Please reconsider the wording "...other athlete adjust...".


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: USING STIFFNESS TO ASSESS INJURY RISK: COMPARISON OF METHODS FOR QUANTIFYING STIFFNESS AND THEIR RELIABILITY IN TRIATHLETES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript was very well written with clear logic.  Authors used unambiguous, and professional English throughout. It is easy to read and understand the manuscript.

Introduction
The introduction is sufficient to illustrate the background in the work and relevant prior literature is appropriately referenced. It clearly explained the measurement of the vertical stiffness, leg stiffness and joint stiffness, and clarified the applicability of the three measurements of stiffness in research. The writing is going on smoothly and without obstacles for understanding.
Line 84-87: Would you please explain briefly what are the five risk factors associated with risk of Achilles injuries in running athletes and linked to changes in lower limb stiffness?

Methods
Line 188: What did TrainingPeaksTM monitor in athletes? How do you decide the effects of variations was minimized by utilizing TrainingPeaksTM?

Results
The results were presented well even there were plenty of data.

Discussion
The discussion compared the average stiffness value calculated with different equations with those in previous studies, and explained clearly why the values were different among studies. It also highlighted the good inter-day reliability of vertical and leg stiffness during running, and hopping and running stiffness did not correlate with each other well. The results have been fully discussed and well explained.

One problem is that in the introduction part, the first paragraph mentioned the overuse injuries especially the Achilles tendon injuries in triathletes, but no related contents to echo the content of this part later in the manuscript. It may be good to add some discussions about the utilization of the stiffness measurement in triathletes with overuse injuries here.

Table 2, 3, 4, 5 should be modified to three-line tables.
Experimental design: The research question was well defined, relevant and meaningful. There was a very good review about the effects of the three stiffness measurements on performance and injury and implications for training (Brazier et al., 2014, Strength and Conditioning Journal, 36(5),103-112), but research about the comparison of different stiffness measurements as well as their reliability when used in determination of injury risk was few. The rationale of the manuscript is very strong and the research finding should be very meaningful in the future investigation.

The study design is sophisticated and comprehensive. The authors selected top-level triathletes and conducted the study based on the ethical approval from the university ethics committee. The rationale of non-randomisation was clearly presented. Setting of the testing procedure as well as data analysis method were reasonable and were stated precisely.

The details of the methods were described very clear and organized.
Validity of the findings: Data is robust, statistically sound, and controlled.

Conclusion are well stated, linked to original research question and limited to supporting results.
Additional comments: In general, the study was well designed and conducted very carefully. The different methods of stiffness measurement were usually confusing in different studies. Therefore, it is imperative to clarify each of the methods as well as compare the utilization of them so that researchers could choose the proper method to investigate related research questions. This study has done a good job in distinguishing the methods of the stiffness measurement, reporting the reliability and correlations of the methods, and making the recommendation about the utilization of the methods under different situations. This will greatly contribute to the future research in assessing injury risk with stiffness measurement.


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: USING STIFFNESS TO ASSESS INJURY RISK: COMPARISON OF METHODS FOR QUANTIFYING STIFFNESS AND THEIR RELIABILITY IN TRIATHLETES
Review round: 1
Reviewer: 3

Output:
Basic reporting: While the literature review has been well written, there has been several prominent pieces of work within stiffness literature which investigate this topic and have been overlooked in the literature review such as Diggin et al. 2016; Joseph e al; Pruyn et al. One article in particular has been cited for it's stiffness measures but the author does not discuss their reliability results. Tables are well presented. Some concepts also require a citation to support this e.g. line 111-112 which has been established in research. Once again 154-155 this concept has been explored particularly in hopping and comparisons between hopping stiffness and running stiffness have been made/investigated.
Experimental design: Overall there a several issues with the experimental design of this project, while there is a good research questions and has the ability to add to the body of research. There are a few flaws with the methods used, particularly the calculations which appear to be done without any justification or scientific back up e.g. the summing of joints. Summing of joint stiffness values appears to have been done to improve reliability, rather than with evidence to support the sum of the values e.g. line 171-173. The joints involved have varying degrees of freedom and the point of peak moment will vary as the joints time different e.g. as suggested in the paper the hip pre-activates first. Additionally transforming stiffness numbers to unitless values appears unnecessary and with little scientific support, suggest revisiting this concept. Would also suggest redefine this aim or presenting data on speeds that are reflective of elite triathletes as suggested by the study (which appears to be captured). Elite triathletes threshold pace is 3 min/km, 5 min/km pace would significantly influence your stiffness values and its comparison to hopping. This is noted in the conclusion of the article but is a contradiction to the what the paper suggests initially line 499 - 502. I suspect the population is a recreational group which would have an effect on the joint stiffness reliability as they potentially will utilize individual strategies and joint dominance or contributions may change. Would also suggest technique may vary significantly between Olympic  level distance and long distance triathletes.
Validity of the findings: Further statistical analysis needs to be undertaken, it is stated that data was assumed to be normal, were normality tests undertaken? If not this will affect the statistical results. Additionally, PCA analysis could of been undertaken to assess which joints where the main contributors to movement. Methodology of the paper needs to be revisited or more clarity provided. This will effect the findings of results as it will provide between comparisons e.g. comparing stiffness levels in the discussion to previous papers, it is difficult to compare different population groups due to different training levels. Recreational athletes are very different to elite athletes, based on the running speeds, age and weight presented in this study it suggest they a recreational which will change how the data is discussed and what speeds should the data would be presented. Would rather see data presented on speeds reflective of their true competition pace.
Additional comments: The paper provides some good insights and has potential. It is well written and covers the main articles in this topic. Major revisions are required on the methodology of this paper, justification of methods around summation of joint stiffness values and the unitless values is required. This will change the interpretation of findings and conclusions drawn. Consideration needs to be given to the population recruited and taken into consideration into the interpretation of findings and further investigation into existing literature is required and will provide guidance and assistance is developing this paper.


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: USING STIFFNESS TO ASSESS INJURY RISK: COMPARISON OF METHODS FOR QUANTIFYING STIFFNESS AND THEIR RELIABILITY IN TRIATHLETES
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no commen
Validity of the findings: no comment
Additional comments: After the revision, the rationale of this study has been more clearly and fully explained. Relevant prior literature has been appropriately referenced. Article structure is more complete.

Only one suggestion:
Line 551-552, line 632: please keep the format of the two references consistent with the rest of 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: MICROBIOME ANALYSIS OF PACIFIC WHITE SHRIMP GUT AND REARING WATER FROM MALAYSIA AND VIETNAM: IMPLICATIONS FOR AQUACULTURE RESEARCH AND MANAGEMENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript entitled “Microbiome analysis of Pacific white shrimp gut and rearing water from Malaysia and Vietnam: Implications for aquaculture research and management”  aims at characterizing the microbiota from shrimp gut and pond water of farms located in Malasya and Vietnam using the amplicon sequence variants (ASV) method. The manuscript provides an interesting analysis of the whiteleg shrimp gut microbiota, and it has adequate experimental design and data analysis of sequences from V3-V4 16S rRNA region. Authors found a limited diversity of the adult shrimp gut microbiota as compared to the water from the same pond, which is presumably due to host selection for microbial strains. The details of the sequencing and annotation seemed appropriate. Importantly, the sequencing data are freely available for the scientific community. The statistical test applied to microbiota data is acceptable. Literature references are sufficient field background/context. The results are relevant results to hypotheses.

However, several major and minor points need to be addressed to improve the manuscript.
Experimental design: However, several major and minor points need to be addressed to improve the manuscript.

Major changes:

Lines 277-286:
It is probably due that Planctomycetes was not found in other studies due to the bioinformatics methodology (OTUs Vs ASVs). Please discuss in this regard.

Lines 350-355 and 385-387.
How many reads is the difference in the assignation to Vibrio species among using OTUs Vs ASVs?

The alpha diversity analysis showed a statistical difference between studied groups. However, the authors should specify how many replicates for the rarefactions curves were made to obtain the alpha diversity metrics.

Please clarify the cut-off of the filters used for quality filtering: which was the selected Phred quality score? The ambiguous bases were removed? A minimum length of the read was selected? Etc.

How many of the total sequenced reads (after quality filtering) matched against RDP database? How many reads were unclassified? Please discuss that. How many reads per sample were obtained?

Lines 236-241.
Please describe how many reads were assigned to Vibrio using OTUs and ASVs.

Authors claim that using ASV to detect Vibrio parahaemolyticus is an option for early detection of diseases such as EMS. However, the authors should demonstrate that utility using samples of microbiomes with really EMS diseased shrimps such as doi: 10.1038/s41598-017-09923-6 and 10.1038/s41598-017-11805-w.

Please include the age and weight (g) of shrimps collected in methods, and discusses the potential effects of the shrimp age in defining the difference of the microbiota among Malaysian and Vietnamese shrimps (Figure 3).

For a better comprehension of the shared and unique microbiomes between intestines and water from the same pond and between farms, the construction of Venn diagrams of shared ASVs at family and/or genus level will be very useful.
Validity of the findings: No comment.
Additional comments: Minor changes.

Lines 54-67:
There are several articles missed in the introduction about the microbiota from pond water and sediments of shrimp farms, i.e. doi: 10.1186/s12866-016-0770-z and others. I think that these works can be added to the cited background of the introduction section.

Lines 70-73:
There are at least two references of microbiota from wild-type shrimps, such as doi: 10.1371/journal.pone.0091853 and 10.1038/s41598-017-11805-w. These two references should be cited as wild-type shrimp microbiomes in these lines.

Line 103:
How was pelleted the sample, using centrifugation or gravity?

Lines 115-120:
How much was DNA concentration for PCR amplification used?

Line 266:
Please include the following two cites about the impact of diseases in L. vannamei microbiota in the sentence, doi:  10.1038/s41598-017-09923-6 and 10.1038/s41598-017-11805-w.

Lines 265-268:
There is at least one reference of L. vannamei microbiota from a wild-type environment (doi: 10.1038/s41598-017-11805-w). This reference should be cited as wild-type L. vannamei microbiome in these lines.

Lines 372-377.
I think that microbiota from pond sediments is also important with the species contribution to the gut shrimp bacterial diversity. Thus the authors could discuss that.

Figures 2-6.
A short description of what is shown in each panel and the symbols used are missing. For example, A, B, C and D symbols, and legends are missed in figure 2.

Figure 5.
The value of the X-axis is not clear. What is meaning 1000 or 10?

Figure 6.
In the left section, what the light and dark colors of the bars mean? What is the difference between these two colors?