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

Input:
Title: A SIMPLE METHOD OF EQUINE LIMB FORCE VECTOR ANALYSIS AND ITS POTENTIAL APPLICATIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Basic reporting: This manuscript aims to investigate the use of time force vector diagrams captured over the stance phases of horses for illustrating functional asymmetry and to compare traditional ground reaction force values (peak force, impulse etc) to continuous data in this context. The manuscript is generally very well written and presented. Figures/Tables are relevant and well described.
Experimental design: Experimental design: The research aims are defined. There are however no research hypothesis presented. Including specific objectives/hypotheses may help the reader in terms of for example easier understanding of which parts of the investigation have been performed to study left-right differences and which parts are investigating ‘force mechanisms’, i.e. the general relationship between peak force, impulse etc and the newly proposed continuous parameters (VecMag, VecAng).
No concerns about Ethics: non-invasive procedures during standard in-hand exercise which is normal routine for many horses. Technical standard high: combined multi-force plate and 3D motion capture data.
Methods: Generally appropriate level of detail. Could be more comprehensive in some places, particularly when describing the statistical method for comparing continuous data. Sample sizes should be presented more accessibly: it is not immediately clear what the relationship is between the number of ‘trials’ and the number of ‘stance phases’. Please report sample sizes (number of stance phases, not number of trials) when reporting results of statistical tests.
Validity of the findings: Validity: The main difficulties encountered when reading this manuscript are listed below (in order of perceived importance) followed by some more detailed comments referencing specific sections in the manuscript:
1.	In the context of functional asymmetry analysis (lameness, as listed as one of the motivators for this study by the authors), population level comparison of left-right asymmetry is of comparatively little use when the direction of asymmetry is not dealt with appropriately. Let me give a more detailed explanation: assume five of the ten horses show smaller force left fore than right fore and the other five show smaller force right fore and the magnitude of the measured force asymmetries (independent of what force parameters is chosen) are similar. A paired sample assessment of LEFT versus RIGHT GRF values will in all likelihood show no significant difference since negative and positive values (i.e. differences between left and right values) will cancel out in the analysis. It is hence questionable what a population level analysis applied to the traditional left right values and also applied to the suggested continuous time data contributes to a comparison between the two approaches. The authors may need to think about ways of dealing with this effect e.g. using some sort of ‘normalization’ of the effect of different ‘directions’ of asymmetries. I understand that here the authors are dealing with perceivedly sound horses (some more direct evidence about this assumption, e.g. direct reporting of peak force and impulse differences (in percent?) for each horse may be helpful in this context).
The above challenge with left-right differences does not affect the conducted correlation analysis, which (if I understand correctly) has been applied to the individual limb values rather than to left-right differences. If the authors however aim at correlating asymmetry values between the traditional and the continuous approach, then further thought needs to go into the normalization of the direction of asymmetry.
2.	The discussion puts (in comparison to the population level data) quite a lot of emphasis on the ‘pilot data’ of one particular horse for which eight trials (rather than 3 trials, how may stance phases?) has been collected and for which the proposed temporal analysis is identifying some significant left-right differences at specific times over the stance phase. This is being used to discuss in detail the advantages of using this analysis in the context of lameness despite the horse not having been identified as lame. This speculative part may benefit from some condensing and from a more balanced discussion of this topic.
It may also be interesting to analyse in a bit more detail the influence of the algorithm used to identify beginning and end of stance. In particular over the first and last approximately 10% of the stance phase, force values are changing rapidly so I slight difference in how the left and right limb contact the ground may cause a temporal shift that may lead to the detection of significant differences in this transient phase of the force signal. A sensitivity analysis investigating the influence on changes in foot on and foot off timings may provide information about the robustness of the statistical approach towards these temporal effects and then justify a slightly more detailed discussion of this part of the study. A recent study (by one of the co-authors of the current manuscript) indicates that a difference of 26ms captures 95% of the differences between kinetic and kinematic timings for foot on and foot off events. This would indicate a possible shift of about 3 samples (for the sub-sampled 120Hz data). It would appear very interesting to provide some information about the robustness of the statistical method applied to the continuous data against time shifts of this magnitude.
3.	The correlation analysis between the traditional and the continuous parameters is very nice (please add p-values to the provided correlation values in the main text). The authors may want to consider discussing the difficulty of comparing a novel method (providing complementary information) to a more limited but established method. A correlation analysis of course shows how well the two are agreeing (so in one way it is good if they do). However if there is perfect agreement and the aim is to create some sort of improvement over the established method: why is the new method needed when it agrees perfectly so does not provide new information? It may be worth discussing how is it possible to show that the new method provides something that the established one doesn’t? Just a thought.
Additional comments: Line 60-62 and following paragraph (line 63-67): thank you for providing relevant references indicating the use of peak vertical ground reaction force for lameness detection. There is also some evidence that peak vertical ground reaction force may be less useful than more intricate analysis based on principal component analysis of different force parameters, which may indeed help making an argument for additional ways of analysing force data. Williams, Silverman, Wilson, Goodship, 1999, AJVR 60, 549-555 and also the seminal work that shows that tendon injuries in Thoroughbreds may be detected with force plate analysis (Dow, Leendertz, Silver, Goodship, 1991, EVJ, 23, 266-272). One of the studies is indeed referenced in the discussion.

Line 81-84: I am wondering whether it may be worth introducing (or contrasting to) the method of using ‘functional limits of agreement’ which has been used for statistical comparison of IMU data over entire stride cycles here? While not applied to force data over a stance phase, this also appears to be a method that can be used for kinematic data over entire stride cycles. (Olsen, Pfau, Ritz, 2013, J Biomech, 46, 2320-2325). My understanding is, that the method proposed here can deal with multi-dimensional time continuous data while the previously published method cannot?

Line 85-89: Did you have any research hypotheses (and objectives) linked to the aims and objectives? I have struggled at that point in the manuscript to get my head round which analysis actually looks at asymmetries (compares left to right) and which parts is hunting a ‘mechanism’, ie correlation between established and new values (is that latter done on left-right comparisons?

Line 94-97: given that the authors mention the use of peak force asymmetry thresholds for lameness detection it would appear useful to learn more about the peak force asymmetry values for the horses. Testing for statistical differences between left and right may not be a useful undertaking (table 1) here, since some horse may show reduction in left and some horses reduction in right peak force and hence no statistically significant difference may be detectable with this approach. Please consider alternative methods for providing information about force asymmetries between limbs. This relates to main issue 1 outlined above.

Line 106-107: Please specify what you mean by valid trials in this context. How many foot strikes were available from each trial? One per force plate per limb? What were the conditions that had to be met for a ‘valid’ trial. Wherever possible, it would be nice to mention the sample size (in figures/tables and where results are presented). In the current version, it was not clear to me what the sample size was (N=3 trials? N=8 trials?). It would appear more intuitive to me to expess sample size as the number of foot strikes recorded.

Line 108-110: This may need some more ‘motivation’ here both in terms of why intra-horse gait asymmetry was further investigated and why in one horse only. I would consider this a worthwhile more speculative part of the investigation (in particular if robustness against time shifts in identifying stance phases from kinematic data is included). A little more background may help the reader.

Line 115-117: This may be my limited understanding but can you explain why you use the term centre of pressure and not the term point of zero moment which I am more familiar with in the realm of force plate analysis as opposed to pressure mat analysis where the term centre of pressure appears more logical (to me).

Line 118: express in ms (despite ‘s’ being the SI unit) to make more efficient use of decimal places?

Line 121-124/line 136-138: please clarify how many foot strikes (stance phases) were obtained per trial.

Line 139-141: this relates to the point raised earlier about the effect of ‘left-sided’ and ‘right-sided’ asymmetries in force cancelling out. It is also not quite clear to me what these t-tests are aiming for: which of the study aims is the addressing? Consider being more explicit about this.

Line 141-143: Please clarify what variables (e.g. for each limb? Left-right comparisons?) this part of the analysis was performed for.

Line 179-184 (and Figure 3): I am no entirely sure that I completely understand what has been tested for here: is this (in analogy to the t-tests testing for left-right differences) to establish whether there is a difference in the 2D continuous stance phase GRF? If this is the case, could the authors please add some more detail (to the introduction) explaining the rationale of testing for left-right differences on population level, taking into account that some horses may show left-sided bias and some show right-sided bias so the significance of the ability (or failure) to detect any left-right difference is not quite clear? One point in the introduction mentioned as an application of force plate analysis (with the traditionally used parameters) is for example to identify lameness. Comparing ‘population level’ left-right differences between the traditional (peak force, impulse etc) and the time continuous approach appears of limited information value in the context of lameness when not dealing with side/direction of asymmetry in some way or other.

Line 193-196: this is very exciting in the context of lameness analysis (following the topic above and chosen as one of the topics in the introduction) but some additional information may be useful here. Can you please clarify how many stance phases are included in this analysis (is the number of trials equal to the number of stance phases, presumably not since more than one force plate has been used?). This may also be useful to understand why the value of the ‘critical threshold’ is different for the forelimb and hind limb data. Please consider giving a little more information about this threshold in the materials and methods section.

Line 197-201: Please add significance values (p-values) for the reported correlations in the text.

Line 224-227: Please indicate clearly that these are the authors’ opinions and do not relate to findings that you have tested for in this study (study evaluated for example correlation between the two techniques but not whether the results were ‘easy to read’ or ‘intuitive’). Add ‘potential for’ to the last sentence mentioning lameness, rehabilitation.

Line 238-239: … and to investigate to what extent steady state locomotion was performed over the analysed stride cycle?

Line 264-277: This appears to be a somewhat speculative section based on one horse assessed as ‘clinically sound’. It seems plausible (to me) that this technique might indeed have some uses. However, it may be prudent to be a little more ‘balanced’ in these speculations and for example replace the phrase ‘it will be necessary to … explore asymmetry throughout the stride …’ by a phrase such as ‘it might prove useful to …’ and ‘the results presented here suggest … is well suited’ by ‘the results presented here present some indication that SPM may be suitable for this purpose’. Consider robustness/sensitivity analysis against time shifts.

Line 278-297: Even more so than the paragraph before, this section is based on the results of one horse categorized as ‘clinically sound’ be veterinary expert analysis as well as by a suggested force threshold. Please consider considerably shortening or removing this section. It appears a little ‘dangerous’ to discuss this (in the current length and depth) based on the data of one horse without clinical indication without debating the underlying issue of decision making in this context and the difficulty of improving decision making based on the limitations of current best practice. This topic appears immanently relevant in the context of this study which is motivated by saying ‘current force plate analysis is limited’ and we investigate a method that may have potential in this context. The current analysis shows that the new method shows some correlations with the established method hence in effect ‘shows the same’. It appears important (to me) to debate how progress can be made.

Line 319-320: Please restrict the conclusion section as much as possible to reporting the direct consequences of this study. For example: how does this study show that the method can be used to compare GRFs between ‘conditions’. What conditions are you referring to?

Line 322: I would suggest being more specific here and indicating that ‘VecMag correlates to vertical force (and impulse)’ and ‘VecAng to longitudinal forces and impulses’

Line 323: The study has not tested for ‘intuitiveness or simplicity’

Table 1+2 and materials and methods (Coefficient of variation): a coefficient of variation for an angle may be somewhat of an odd thing to do? If you choose a different ‘zero point’ or for example an opposite direction of your angle definition, an angle of +1 degrees varying by +/-0.1 degrees will have a 10% variation while choosing to express this angle as let’s say -359 degrees will in a value of 0.03% variation. Are there better ways of doing this? Is a CoV useful for angles or is an angle not already ‘normalized’.

Figure 1: what are the grey (non-straight) lines?

Figure 2: add shaded area indicating stride-to-stride variation to panels B and C? what is the sample size (N=? stance phases)

Figure 3: sample size (N=? stance phases, not trials if they are not the same). This may need reconsidering since this relates to main issue 1 outlined above with regards to directionality of left-right differences at population level.

Thank you very much for providing raw data in the form of Excel spreadsheets that are reasonably well labelled with respect to their content. It is still not easy to comprehend all of this but I guess it never is when dealing with a data set collected and processed by somebody else. Well done.


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

Input:
Title: A SIMPLE METHOD OF EQUINE LIMB FORCE VECTOR ANALYSIS AND ITS POTENTIAL APPLICATIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript compares different techniques to analyze ground reaction forces during stance phase of horses when trotting.
Although this matter has been addressed in human biomechanics, it is interesting in the context of animal biomechanics.
Experimental design: Experimental design is fine. Indeed, it is very good.
Validity of the findings: As I have mentioned above, although this matter has been addressed in human biomechanics, it is interesting in the context of animal biomechanics.
Additional comments: The manuscript compares different techniques to analyze ground reaction forces during stance phase of horses when trotting.
Although this matter has been addressed in human biomechanics, it is interesting in the context of animal biomechanics.
The manuscript is well written and explained.
I have only some minor comments and suggestions.

Abstract
Line 17 and Line 19
Please, indicate here what was compared (contralateral fore and hind limbs).

Line 31
“In addition SPM was performed to seek differences between combined vertical and longitudinal GRF throughout the stance phase.”
This sentence leads the reader to conclude that vertical GRF was compared to longitudinal GRF, although this is not the case.
I suggest rewriting this sentence according to Line 34: “differences between the left and right contralateral limb pairs”.

Line 48
“vertical, longitudinal and transverse components…”
As this paragraph has general comments about ground reaction forces, I think these terms are not appropriated since they apply only for quadrupeds (at least the term “longitudinal”. For humans, longitudinal is, indeed, the vertical component). Please, use more general terms, such as “Typically, the 3D force is resolved into components according to the adopted coordinate system…”, or indicate that you are referring to quadrupeds.

Lines 85-89
Please, justify why you have done the analysis only in sagittal plane.

Line 135
Please, explain how mean speed was calculated.
Line 143
Please, define “relative speed” and explain how it was calculated.

Lines 160-161
Please, define the acronyms LFRH and RFLH. I suppose they are left forelimb/right hindlimb and right forelimb/left hindlimb, respectively, but I think, for clarity, it is necessary to define them.

Line 176
Please, consider improving the quality of the coordinate axis in Figure 2. They are too light. It is difficult to see VecAng is negative in the forelimbs and positive in the hindlimbs, especially in Fig. 2-D. Some guys, like me, have to use awfull glasses.

Line 182
I think it is not exactly the “SPM value” that is shown in Fig. 2 and 3. It is the t2 value. Consider rewriting this sentence.

Line 193
Figure 4 – Consider to include post-hoc tests here, for vertical and longitudinal GRF components. I think they would help to understand what was discussed in Discussion section.

Line 204
The parentheses were not closed.

Lines 207 and 208
I suggest to rewrite this sentence with something as “which coincide with the first and third clusters of data points that reached significance in SPM plot (Figure 3).”

Lines 208-209
This sentence is somewhat ambiguous. Consider rewriting this sentence.

Discussion section
As I have previously mentioned, I think a plot showing post-hoc tests for longitudinal and vertical GRF components in Figure 4 would help to understand/visualize several points in the Discussion section.

Line 310
Please, define the acronym “COM”.

Line 322
“…VecMag represents the vertical force and VecAng represents the longitudinal force.”
I suggest rewriting this sentence as “…VecMag is more related to (or more influenced by) the vertical force and VecAng is more related (or more influenced by) the longitudinal force.”

Conclusion
I suggest including a comment that vector diagrams and SPM analysis can be extended to other planes, and SPM, indeed, can be performed in 3D considering simultaneously the three GRF components (and, indeed, vector diagrams can also be performed in 3D: see Fig. 1 in Pataky et al. Vector field statistical analysis of kinematic and force trajectories. Journal of Biomechanics, 46 (2013), 2394-2401).

Table 3 has several acronyms that were not defined. Besides, I suggest presenting the variables in the same order they were presented in Tables 1 and 2.

Figure Captions
Figure 1: include a description for the gray lines.

Figure 2: include a description for the acronyms RH, LF, LH, RF, LFRH, and RFLH

Figure 5: include a description for the acronyms RH, LH, LF, and RF.


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

Input:
Title: A SIMPLE METHOD OF EQUINE LIMB FORCE VECTOR ANALYSIS AND ITS POTENTIAL APPLICATIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have no further comments on this manuscript. The authors have dealt more than adequately with my initial comments.
The figures and tables have been improved considerably.
Experimental design: No further comments. Experimental design is appropriate.
Validity of the findings: No further comments. Inclusion of higher versus lower comparison has alleviated my initial concerns with regard to asymmetry and lameness.
Additional comments: Thanks for taking into consideration the original comments. Much appreciated.

One small point: I believe the reported relative speeds (results section) should be dimensionless and not given in m/s.


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

Input:
Title: A SIMPLE METHOD OF EQUINE LIMB FORCE VECTOR ANALYSIS AND ITS POTENTIAL APPLICATIONS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No additional comments.
Experimental design: No additional comments.
Validity of the findings: No additional comments.
Additional comments: The manuscript have improved substantially. All my suggestions were included and all my comments were properly reponded. I have no more comments. Congratulations!


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

Input:
Title: REPEATABILITY OF GLUCOCORTICOID HORMONES IN VERTEBRATES: A META-ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Summary - The purpose of this paper was to analyze the available literature regarding the repeatability of glucocorticoid measurements. The study included measurements of baseline (initial), acute stress-induced (response), and integrated glucocorticoids.  The analysis was conducted on different taxa with birds being the best represented by number of studies.  Findings were that initial glucocorticoid measurements were moderately repeatable with response and integrated measure being more repeatable than initial measures.  Factors contributing to the repeatability of glucocorticoid measures included whether the measurements were taken within a life history stage and what type of assay was used with a kit producing the least repeatable results.  Of the taxa analyzed, amphibian measures of initial and response glucocorticoids were the most repeatable.

The writing is clear and flows well.

The Introduction provides necessary background.
Minor comment – it would be nice to define allostasis for readers whose expertise fall outside of this field.

The literature was well used and cited.

Structure is within PeerJ standards.

Figures are well done.

Raw data was provided.
Minor comment – it would be nice to see the r2 values for the analyses of Supplemental Table 1. even if only for the best fit models (those within 2 ΔAICc).
Experimental design: The experimental design was a Meta-analysis of the available literature on repeatability of glucocorticoid measurements.  I think that the study was well designed. Explanation of statistical analyses was clear.
Validity of the findings: Sample sizes for some of the analyses were small. For example, amphibians showed substantially greater repeatability estimates compared to the other taxa, but their numbers were small (n=4).  In general, I think that small sample sizes limit this study.  Having said that, I think that the study is well done and provides interesting results with the data that they do have.  I am also very surprised that RIAs were less reliable than ELISAs in terms of repeatability in glucocorticoid measurements. However, the authors address this in the discussion.
Additional comments: As stated above, small sample sizes hindered this study for certain analyses.  However, the study was well done, and it is an important topic to the field.  Overall, I enjoyed reading this paper and I recommend it for publication.

It does, however, leave me with questions.  For example:

1)	For the integrated glucocorticoid analyses: Were there differences between the repeatability of glucocorticoids taken from feathers vs. feces (or saliva)?

2)	The authors explored the influence of pre-breeding, breeding, and nonbreeding on the repeatability of glucocorticoids, but it would be nice to see what is happening within these time periods (e.g. for birds, within breeding – egg laying, incubating, nestling provisioning).

It would be great to be able to address these questions if sample sizes permit.


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: REPEATABILITY OF GLUCOCORTICOID HORMONES IN VERTEBRATES: A META-ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: No Comment
Experimental design: No Comment
Validity of the findings: No Comment
Additional comments: This study is a meta-analysis investigating the repeatability of corticosterone across taxonomic groups. The authors find varying degrees of repeatability across taxonomic groups, assay type, sampling interval.
General comments.
Overall I think this is a well written manuscript and the authors acknowledge the limitations of this type of study. I only have very general comments which are more of me thinking about the limitations of this type of study.
I think this is a question that is worth addressing. My worry with these types of studies, or even the individual studies that were used, may often underestimate repeatability because differences in environmental conditions, stage of breeding, or assay variation. The authors of the current submission attempt to control for some of these factors but did the authors in the main studies? I think that some species lend themselves very nicely to these types of studies which I would venture to guess they show a smaller range in of glucocorticoid concentrations across the annual cycle. For instance,  white-crowned sparrows show high seasonal variation in glucocorticoid titers so unless you capture the bird at the exact same stage of its breeding cycle you likely will not find that corticosterone is repeatable. But this may be a classic example in which we fail to reject the null hypothesis when it is not true simple because our sampling date was not correct to capture the repeatability of an endocrine measure. Alternatively, it could be that is just not that repeatable because environmental conditions are so variable that not matter what we do we will find relatively low repeatability. This then makes me think that there are likely less studies on repeatability then we would like because the limitations of the data are known and cannot be properly addressed. The authors have acknowledged many of these caveats in the discussion so I must commend them for that.
I understand why Wingfield and McEwen have pushed the concept of allostasis from a point of understanding how corticosterone levels will fluctuate across life history stage, environmental condition, and etc. In terms of the repeatability measure one would assume that corticosterone levels both at baseline or initial sample and in response to a stressor would fluctuate greatly. There is very likely a range of reactions as nicely outlined by Taft and Vitousek 2016 or Angelier and Wingfield 2013 so if all conditions are similar enough across our sampling points then we would detect a high degree of repeatability (potentially).
It would be nice to see a meta analyses of repeatability in which individuals are challenged. This would get at what factors can decrease the repeatability of glucocortiod measures. Some of the studies that may really highlight these changes are food restriction/removal studies, environmental extremes such as storms, selection for stress physiology across a breeding range, light pollution, increases in brood size and etc. The combination of these factors may begin to shed light on factors in the environment that drive changes in stress physiology. These would all provide examples were metabolic demands have led to changes in corticosterone concentrations. To put it into the authors words, we could look at the phenotypic plasticity of hormonal signaling or reaction norms. This obviously is not something I would expect to be add to this paper but rather expanding on in a future paper. I think this would bring some valuable insight into  the concept of allostasis in terms of using a meta-analysis to find common reactions to environmental challenges.
I think the authors should have a look at and cite the following paper as it is important for thinking about corticosterone assays across labs. Although  this particular meta analyses really controls for laboratory biases. IT would be relevant for the paragraph starting on line 343. Fanson et al. 2016 Inter-laboratory variation in corticosterone measurement: Implications for comparative ecological and evolutionary studies


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: REPEATABILITY OF GLUCOCORTICOID HORMONES IN VERTEBRATES: A META-ANALYSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript reports results from a well designed study using data from the literature.  The manuscript is well written and the results are well presented.  The study will be a useful addition to the literature on repeatabilities of glucocorticoid measurements in animals.
Experimental design: The study used a wide range of statistical methods.  Whilst the reviewer is not able to comment on the validity of these methods, the appropriateness of calculating mean repeatabilities after 1000 bootstrap samples (line 196) is questioned.  The authors should include mean and SE values calculated directly from the repeatabilities.  These mean and SE values should be reported as well as or instead of the bootstrap values.  It is misleading to report in the abstract that the bootstrap values were mean values.
Validity of the findings: A comprehensive dataset has been collated from the literature.  The conclusions are supported by the evidence.
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: BACTERIAL IDENTIFICATION OF THE VAGINAL MICROBIOTA IN ECUADORIAN PREGNANT TEENAGERS: AN EXPLORATORY ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Summary: The authors reported the valuation of eight vaginal bacterial species, known to be risk or protective factors for bacterial vaginosis, and the pH value in a specific cohort: pregnant teenagers in Ecuador. Surely, considering the correlation between dysbiosis and some adverse pregnancy outcomes, this study could implement our knowledge on vaginal flora, also in low- and middle-income countries. A limit on the study, reported by the authors, was the absence of a control study and, another one, was the lack of information on pregnancy outcomes in this population.

Basic reporting
The English language was intelligible, but errors, repetition and long sentence were present in the text.
The literature available was summarized in the test. Considering this is an observational study, more information could be added about data reported in other studies to give a point on the topic of the study.
Figure are of high quality, but I think that the graphs do not add any additional information and the text could be enough.
Table are clear; I have only to underlined that table 2,3 and 4 are all named as table 1.
Experimental design: See “general comment”
Validity of the findings: This study could give a description on partial vaginal microbiota in pregnant teenagers in Ecuador. The novelty of the study correlated with the population take into consideration. The limit of results correlated with the little simple size (as reported by the authors) and the absence of a consistent clinical impact of the data found. In fact, no all bacterial species were searched, and no correlation on maternal and fetal outcomes were reported. Even if it is not possible to define an influence on adverse outcome, as explained by the authors, a description of incidence of major complications of pregnancy in the population may be of interest.
Additional comments: English language required some improvements. For example:
- frequent repetition of word is used. See rows 45-46; rows 127-140
- A long sentence was reported at row 61-66. Please summarized it or try to clearly explain the concept.
Specific comments
Title: The title is appropriate.
Summary/ Abstract: Some inaccuracies were reported. Please clarify the sequent points.
- The author reported that “five risk factors were collected”, but only four were listed [rows 31-32]
- They also reported that nine bacterial species were searched, but only 8 were defined [row 34]
Introduction: The literature available was summarized in the test. Considering this is an observational study, more information could be added about data reported in other studies to give a point on the topic of the study.

Materials and methods: 1) how risk factor analyzed in the test were choose?
2) Are there any information of previous use of hormonal contraceptive? In could be of interest to verify if this factor, associated with change in vaginal pH, could be correlated with BV
3) Considering the fact that the patients were pregnant, how the use of condom was defined? Use of it before pregnancy research? Use during pregnancy? Please clarify
4) Why placental and fetal disease were excluded?
5) Considering that vaginosis is a risk factor, but it is not always associated with adverse obstetric outcomes, could the authors reported the pregnancy course or their population? In fact, even they reported the association of VB and preterm delivery in other studies, could be of interest to value this condition in the particular population collected in the study (Ecuadorian pregnant teenagers).

Discussion: The discussion is too short and it should extended in a systematic manner. List the principal findings and then discuss them in comparison with other literature, reporting more detailed on novelty of the study, why some risk factor were analyzed while other were not take into consideration.
Tables: The material provided by the authors is clear. Table 2, 3 and 4 are called table 1


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

Input:
Title: BACTERIAL IDENTIFICATION OF THE VAGINAL MICROBIOTA IN ECUADORIAN PREGNANT TEENAGERS: AN EXPLORATORY ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Numbers of pages are not indicated

Introduction is clear and complete, the available literature is well illustrated in the text.

English language used is correct, but some errors are present in the text, an example: line 198: error: “All study participants were colonized with at least by two of the five Lactobacillus”.

Tables and figures are clear and well constructed. But table 2, 3 and 4 are all entitled as table 1
Experimental design: The study is just observational and the conclusions, in line with the aim declared: a characterization of bacterial and Lactobacillus species present in Ecuadorian pregnant teenagers, are merely descriptive.

In the study there is no mention of patients’ symptoms. Would have been interesting register how the presence or absence of certain species of bacteria or Lactobacillus correlated with symptoms declared by the patients.

Even if the authors themselves reported the known association between presence or absence in vaginal tract of pregnant women of certain microbiota species and the risk of preterm labor and colonization from pathogens, they did not investigate this point in their study.

Discussion should be improved. I suggest to list the findings progressively comparing them with available literature in order to illustrate the innovation bring from the study.
Validity of the findings: Relation between high pH and BV was already known and is in accordance with previous literature; however this is the first study that investigate the population (even if not all species were taken into account) of lactobacillus sp. and bacterial anaerobes in a given specific population of Ecuadorian pregnant teenagers.

The novelty provided by the authors is that the bacterial population found in this specific group is different from the ones reported in literature both in low and high income countries. The authors also found that L.Crispatus, L.iners and L. acidophilus are the species most present in their study population.

Results are consistent with declared aim of the study, but their clinical impact is scarce. Would have been more fruitful to investigate how these finding can help in management of BV in pregnancy,  preventing development of BV and risk associated with this condition (such as colonization from other pathogens and preterm birth). For example recording the outcomes of pregnancy, describing in particular age at delivery and pregnancy complications.
Additional comments: I would suggest to perform different kind of studies in this particular population:
A comparison of bacterial colonization of vaginal tract between pregnant and non pregnant Ecuadorian teenagers; if the aim is just to characterize the bacterial population of vaginal tract.

Analyze how the presence of determined species correlates to pregnancy outcomes, such as vaginal colonization from pathogens and the risk of preterm birth


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: BACTERIAL IDENTIFICATION OF THE VAGINAL MICROBIOTA IN ECUADORIAN PREGNANT TEENAGERS: AN EXPLORATORY ANALYSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript entitled “Bacterial identification of the vaginal microbiota in Ecuadorian pregnant teenagers: An exploratory analysis” by Salinas et al., seeks to identify the presence of 5 Lactobacilli species and 3 BV associated anaerobes in the vagina of pregnant teenagers. The study is interesting, although there are several outstanding issues.

1)	It is never clearly explained by the authors why this study targeted this population other than it hadn't been done before. Is there a high rate of BV in Ecuadorian teenagers? Is there a higher than expected rate of preterm delivery in Ecuadorian teenagers? Those would be valid reasons to pursue this research conditions, but there is no indication in the manuscript that is the case. Since the study involves the participation of a vulnerable population (pregnant minors), one would hope that there is an outstanding reason to pursue their involvement. The course and outcome of these pregnancies is also not provided, adding to the questions surrounding this study.
2)	The English needs to be revised. There are major passages that are incomprehensible such as Line 32-33, and multiple odd grammar constructions throughout the manuscript.
3)	There are multiple formatting issues, from inconsistent display of references (including/excluding year arbitrarily, display multiple authors at times, etc.).
4)	Figures lack proper display. Figure is missing a Y-axis and error bars. Figure 2 is incomprehensible to me. I have no idea what is being displayed.
5)	Table 1: One of headings is in Spanish.
6)	The abstract should mention at what time point the subjects were sampled.
7)	In the Methods it is mentioned that the samples were sequenced to confirm identity, yet no methodological details or results are provided.
8)	Line 213: “…weak statistical evidence (P-value for Fisher’s exact test = 0.08)…” A P-value of 0.08 is not significant. Statistical significance either exists or does not exist. There is no weak or strong statistical evidence.
9)	The ethnicity of the participants is not disclosed. This is an important parameter for the vaginal microbiome composition. The discussion should address this when comparing to other studies.
10)	Line 254: “…this study did not analyze every Lactobacillus species only the most significant.” The selected species in this study were chosen because they were presumed to be the most common. Significance has nothing to do with this.

In summary, this study has multiple serious flaws.
Experimental design: Research question ambiguous. Missing data.
Validity of the findings: Primers were not validated with pure cultures prior to the experiment.
Additional comments: See above.


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

Input:
Title: BACTERIAL IDENTIFICATION OF THE VAGINAL MICROBIOTA IN ECUADORIAN PREGNANT TEENAGERS: AN EXPLORATORY ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The English language and the structure of the text were implemented.
The literature available was summarized in the test and in the table.
Figure are of high quality; I already think that the graphs do not add any additional information and the text could be enough. My comment did not preclude the pubblications of this paper, but summarized the test could be suggested, if the authors would like to published also the graphs,
Table are clear
Experimental design: Original research
Aim and scope well clarify
Limits are present in the study, but the authors explain them satisfactorily
Investigation were conducted with good standards; ethical standard was respected and an informed consent was signed. Methods were clarely described
Validity of the findings: This study could give a description on partial vaginal microbiota in pregnant teenagers in Ecuador. The novelty of the study correlated with the population take into consideration. The limit of results are now well explained by the authors
Additional comments: I appreciate the improvements the authors have done to their manuscript
Even if limits persist in the study, they are well explained and the necessity of future evaluation is underlined
I think that the article meets the criteria of Peerj and it should be accepted now in the current form


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: BACTERIAL IDENTIFICATION OF THE VAGINAL MICROBIOTA IN ECUADORIAN PREGNANT TEENAGERS: AN EXPLORATORY ANALYSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The author’s answer satisfy all my request.
They clearly explained the errors in numbers of pages and in table titles and corrected the English errors .
They  improved the results session and the discussion.
Experimental design: The limit of this study remains (small size and experimental design), but, considering that this is a pilot study, the descriptive and observational nature of this work and the small sample size are acceptable.
Validity of the findings: As mentioned above this study has some limits and the results have scarce clinical impact, but this work is a pilot study. So, in view of setting up a bigger study with the aim of compare the bacterial flora in pregnant and non pregnant teenagers and of determine the correlation between BV and preterm birth, this could be a good start.
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: BACTERIAL IDENTIFICATION OF THE VAGINAL MICROBIOTA IN ECUADORIAN PREGNANT TEENAGERS: AN EXPLORATORY ANALYSIS
Review round: 2
Reviewer: 3

Output:
Basic reporting: This manuscript is an improved version of the previous iteration. However, a few concerns remain. The English is improved but still contains multiple grammar issues. This version still needs to be improved.
Experimental design: Ok.
Validity of the findings: Results are valid but conclusions made are beyond the results presented and the scope of the study.
Additional comments: I continue to find the study design, presentation of results and conclusion somewhat disconnected. The reasoning for the study is reflected better in the rebuttal letter than in the manuscript for example. And while the presence of BV associated microorganisms can be seen as a sign of disease, it is not necessarily so. Many women carry these microorganisms without symptoms or deleterious effects. Given that pregnancy complications were not reported in this study, the statement that some of these adolescents were at increases risk simply for carrying these microorganisms is not supported if not accompanied by symptomatic manifestation or adverse pregnancy outcome. Given the complexity of interactions, carrying 3 anaerobes versus 1 of them does not necessarily equal a worse prognosis either, especially given the different interactions with the different Lactobacilli species. So, given the limited scope of the experimental testing, the analysis to support the conclusions would have to be much more extensive and be grounded on clinical outcome. In summary, either the study has to adopt a descriptive nature, meaning that it limits itself to presenting the data in terms of what is the most common bacteria found in this study population; or a much more elaborate analysis will have to be performed to support the current conclusions.


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: PHYLOGENY, TIME DIVERGENCE, AND HISTORICAL BIOGEOGRAPHY OF THE SOUTH AMERICAN LIOLAEMUS ALTICOLOR-BIBRONII GROUP (IGUANIA: LIOLAEMIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written in general but I think it would be a good idea to be corrected by a native English speaker. The background included in the text  allows understanding how this work fits in the broader field of knowledge. The relevant prior literature is appropriate referenced. The general structure of the article is correct. The article is accompanied with supplementary material. However, the matrices (morphology and DNA) and obtained trees are not available in supplementary material. This should be corrected. The article include all the results required to answer the hypothesis (i.e. it is self-contained).
Experimental design: I have two major concerns about the analyses. One of them is related to the calibration point. The authors stated that:

 “We used the fossil assigned to Eulaemus described by Albino 135 (2008), representing the earliest record of this subgenus to place a mean prior of 20 Myr on the tree height.”.

This seems not to be very good decision. If all that is known about the fossil is that it belongs to the subgenus, it might perfectly be place within any of the clades within it. In my opinion it is imperative to include the fossil in the phylogeentic study in order to use its age to define the mean prioir of the node that subtends its position (instead of directly assuming a basal position). Given that this is the only calibration point, taking care in this step is crucial to support the conclusions derived in this manuscript.

The second concern is related to the topological uncertainty. Although the trees obtained by maximum parsimony and Bayesian inference are similar, they differ in several nodes. However, the biogeographic and divergence time analyses were performed considering only the BI topology. This is not a good methodological practice. If both analyses were performed it is because the authors consider that the methods are methodologically sound. As a consequence, deriving conclusions from only one of the topologies in not correct. In my opinion the biogeographic and divergence time analyses should be repeated considering both topologies, showing the common patterns and differences between both results.
Validity of the findings: The validity of the findings is tied to what was expressed in the previous point. The authors should  reanalyze the data and show that the methodological issues are not affecting the findings.
Additional comments: 1-. Please include a paragraph in the main text describing how many new observations (i.e. scorings) were included in the morphological matrix.

2-. Line 114. If you used the free version of TNT you should cite the paper describing the program and acknowledge Willi Hennig society for making it freely available (see TNT documentation)

3. Line 115. Replace “k” by “concavity value”. Add implied weighting cite (Goloboff 1993).

4-. Line 229.  Please include the details of this in M&M section not in discussion.

5-. Please rerun MP analysis without continuous characters in order to determine if the differences in the results obtained by MP an BI are related to the inclusion/exclusion of these characters.

6-. Figure 2. “The L. lemniscatus clade is recovered as a sister group of the L. walkeri clade under MP”
 This statement is not compatible with the tree shown in Figure 4. Species of L. Lemniscatus are either nested within L. walker group or form a grade at the base of the tree.

The legend in Fig 4 is also incompatible with Figure 4, since not all the species of L. lemniscatus group are nested within L. walkeri group.  (following the group definition of Figure 3):

7-. The probabilities calculated are only valid if the topology is correct. Given that you obtained a different topology with CC and Mp   Please make it explicit

8-.  L185. “There was high congruence between both phylogenetic analyses performed (Maximum  Parsimony and Bayesian Inference), especially in the main groups (Figure 2)”. Please support this statement quantitatively: calculate SPR or number of shared nodes between 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: PHYLOGENY, TIME DIVERGENCE, AND HISTORICAL BIOGEOGRAPHY OF THE SOUTH AMERICAN LIOLAEMUS ALTICOLOR-BIBRONII GROUP (IGUANIA: LIOLAEMIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is a thorough evaluation of the systematics and biogeographic history of the Liolaemus alticolor-group, one the most widely distributed groups within Liolaemus. The paper is thorough, it is generally well written and flows well. However, it does have some major methodological issues I think need to be addressed before publication, so my recommendation is that this article might be suitable for publication in PeerJ after major revisions.
My main concern is the methodologies used, particularly to infer the phylogenetic relationships, combining morphological and molecular characters when these two have been found to be very incongruent in Liolaemus. More details are found below.
Experimental design: Introduction:

Line 53: This sounds odd: “…studies were performed with the L. alticolor-bibronii group as the aim of study”. Maybe replace to something like “L. alticolor-bibronii as the focal group”.

Line 68: Please give a reference for Liolaemus inhabiting 6,000 masl.

Paragraph from lines 71-86 should focus more on the results rather than the methodologies of those studies. What have they concluded, is there a consensus, what do they disagree on.

Line 65: Says the alticolor-bibronii group has 30 species but in line94 it says you inclided 31 species in the paper.

Materials and methods:

Paragraph in lines 94-97 is oddly written, please restructure the use of punctuation to make it more clear.

Line 100: web address of Genbank not necessary.

Line 103: was there any visual inspection of the alignments?

Line 123: Partitioning data might not be the best option with little molecular data, for this the best partitioning scheme must be tested with programs such as PartitionFinder.

Line 127: How did you conclude GTR+G was the most appropriate model for these data? Did you do any model test? I suggest you use JModelTest or PartitionFinder for this.

Did you assess convergence and mixing of the MCMC chains? It is very important to make sure all of the chians and also independent runs converge on the same area of probability space. You can assess this with Tracer or the RWTY package in R.

I think you should run a Bayesian Inference Analysis with the molecular data only, since it is often found in Liolaemus that morphological characters and molecular characters lead to very conflicting results. Morphological characters can be extremely linked and very prone to homoplasy, so phylogenetic inference on them should be taken with caution. This is not to say DNA is a perfect solution, but has fewer problems and is more informative.

Line 138: If you used the fossilized birth death then you should have included the fossil Liolaemus as a taxon in the set and not a calibration point. Otherwise you should stick to a model like calibrated Yule.

Line 142: I find unexpected that you reached proper convergence and mixing in BEAST after 5 million generations, this usually happens at list after 50 million and usually after 100 million, especially if you are doing a dated analysis with complicated models that have lots of parameters. I suggest rerunning this for 100.000.000 generations, or at the very least 50.000.000.

Line 143: Before combining chains you need to confirm that they have converged to similar values (looking at the trace plots in Tracer is the most common option).

Line 167: Did you compare the likelihood of other models, is there any reason to believe DEC is the most appropriate one?

If you are going to use Maximum Parsimony to infer your phylogeny, why not Maximum Likelihood as well?

Results:

Paragraph lines 187-193: I think it is very important that you run separate analyses with the mitochondrial loci and the morphological characters besides the combined, because they are both going to give you very different results. The lemniscatus group is found to be inferred as part of the nigromaculatus and not the chiliensis (where the alticolor-bibronii group sits) by molecular evidence, and that should be reflected in this paper, since it is going to give you substantially different biogeographic results.
Validity of the findings: Discussion:

In your initial paragraphs you are discussing the different and congruences between your results and previous studies. You should mention that the main difference is that your study agrees with others that use morphology but disagrees, mainly on the placing of L. lemniscatus, with the ones that are based on molecular evidence. This is why I stress that you should run independent phylogenetic analyses separating molecular from morphological evidence, and discuss the implications and drawbacks of both and of using combined data.

You need to compare the biogeographic models with different adjacency matrices in a likelihood framework, either by Likelihood ratio tests or by ranking them by AICc (corrected Akaike Information Criterion)

References:

Check for some errors, for example line 645: “Systematic Biologic”
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: PHYLOGENY, TIME DIVERGENCE, AND HISTORICAL BIOGEOGRAPHY OF THE SOUTH AMERICAN LIOLAEMUS ALTICOLOR-BIBRONII GROUP (IGUANIA: LIOLAEMIDAE)
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have followed many reviewer’s suggestions that in my opinion have clearly improved the ms. However, I still have some concerns about the analyses. One of them is the calibrating point. I have expressed my concern about assigning a mean age of the basal node considering a fossil whose position in the tree is not clearly determined (only its placement as part of the subgenus is determined). If this fossil is in fact placed as sister of particular clade within the subgenus, all the ages estimated will be higher. The authors should at least be explicit about this point in the manuscript.
   As suggested, the authors have repeated both the dating and the biogeographical analyses considering parsimony and MI topologies. However, the biogeographical discussion is still based only in the BI topology.  Using the likelihood of the biogeographical analyses to choose the phylogenetic hypothesis is not a valid procedure. In my opinion, the discussion should explicitly include references to results that are incongruent in both analyses.
Finally, having a SPR distance of about 0.6 cannot be considered as supporting “congruence between topologies”. Indicate that there is congruence in the major groups but clear differences within those groups that produces that level of incongruence between parsimony and BI.
Experimental design: Indicated above and in the original review
Validity of the findings: Indicated above and in the original review
Additional comments: Indicated above


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

Input:
Title: PHYLOGENY, TIME DIVERGENCE, AND HISTORICAL BIOGEOGRAPHY OF THE SOUTH AMERICAN LIOLAEMUS ALTICOLOR-BIBRONII GROUP (IGUANIA: LIOLAEMIDAE)
Review round: 2
Reviewer: 2

Output:
Basic reporting: I am satisfied with the revisions done by the authors to mine and the other reviewer's comments. I think the paper has improved substantially and is more methodologically robust.
Experimental design: I think the design has improved and is sound now.
Validity of the findings: I think the conclusions are well supported by the data and results. I would though have some discussion on species not included in the analyses that belong to the group.
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: STATUS OF THE UNDISTURBED MANGROVES AT BRUNEI BAY, EAST MALAYSIA: A PRELIMINARY ASSESSMENT BASED ON REMOTE SENSING AND GROUND-TRUTH OBSERVATIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Unfortunately, the English quality is so poor as to render the paper unreadable in parts. I am only critical of English in scientific papers when it interferes with meaning or understanding, and the use of English in this paper makes sections difficult to comprehend. The first few sentences all have significant structural issues making them difficult to understand and much of your abstract better belongs in an introduction. In addition to the English problems and suitability for an abstract, the sentences are missing necessary information such as the year of measure yet contain superfluous information such as the joint administrative structure of Brunei Bay (again not abstract material). I highlight these problems as they are consistent throughout the paper. Below are the first few sentences and a proposed solution.

“Out of 709,700 ha total mangrove cover in whole Malaysia, East Malaysia (i.e. Sabah and Sarawak) is supporting as high as 596,867.90 ha whereas West (Peninsular) Malaysia only 112,832.10 ha. The mangrove vegetation at Brunei Bay is jointly shared as well as administered by East Malaysia and Brunei Darussalam. Four major estuaries namely, Limbang, Sundar, Weston and Menumbok are supporting the entire stretch of bay mangrove complex.”

How about..

As of 2012, Mangrove canopy cover in Malaysia was 709,700 ha with East Malaysia containing 596,868 ha of mangrove and West Malaysia 112,832 ha. The four estuaries of Limbang, Sundar, Weston, and Menumbok contain XX% of the total mangrove forest cover in Malaysia.

Others use Riverine, Basin, Fringe or sub-categories of these (see Ewel KC, Twilley R, Ong JE. Different Kinds of Mangrove Forests Provide Different Goods and Services. Global Ecology and Biogeography Letters 1998, 7: 83-94) for a good example. Nobody uses bay mangrove complex that I am aware of. I am not clear what a bay mangrove complex is, and I would advise against defining another type of mangrove from the traditional grouping.

Your abstract needs a complete rewrite. I made some notes and rewrote your first three sentences above as an example.

My advice is to hire an English speaking scientific writer.

The writing does improve after the abstract.
Experimental design: Lines 96 – 99, it is really water temperature that matters.

How did you ensure the accuracy of the topo-map?

Line 105 – How did you know it was mangrove, why manually digitized, why was this “better?” What digitizing protocols did you use. You are saying you manually digitized mangrove but how did you know it was mangrove?

Why a 4-year difference from RS collection to field validation? How may this cause issues?

Line 125 – How can a singular GCP be more than 100m2 in area?

Line 146 – Why 100m transects? Why these transect locations?

The methods need expanding to answer the questions above.
Validity of the findings: Line 211 – I would say RS is the standard now and has been for some time, it is not the alternate.

Due the questions I raise in your methods I cannot honestly say that the validity of your results are sound.
Additional comments: Line 60. This is not scientific writing, “luxuriant growth of pristine mangroves at Brunei Bay,”

Line 208. what is, "authentic mapping"?

The abstract assumes knowledge of the area to the village level. This should not be the case.

Line 55. These cites are quite dates and newer and improved estimates exist.

Line 62, I find this hard to believe, I know some work has been conducted on Malaysian mangroves.

Remove Lines 67 – 71.

The massively long paragraph around Line 216 goes off-topic.

The discussion is too long and off-topic.


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: STATUS OF THE UNDISTURBED MANGROVES AT BRUNEI BAY, EAST MALAYSIA: A PRELIMINARY ASSESSMENT BASED ON REMOTE SENSING AND GROUND-TRUTH OBSERVATIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1.	In lines 95 to 97, how are the monsoonal regimes going to affect the mangroves in Brunei Bay? How does it alter the temperature and precipitation? Could you elaborate on the effects?
2.	For line 151, if species’ Importance Value is a combined measure of relative density, relative dominance, and relative frequency, is it redundant to calculate it, or why is the combined measure better?
3.	For line 152, could you please explain how Complexity Index is calculated?
4.	For the ground inventory in general, could you include how these measurements are going to improve our understanding of the ecology of the mangroves or the impact on the estuaries?
5.	In lines 187 to 193, you commented on the variation in basal area and density for mangroves in different estuaries. Do you have any explanation on the drivers behind these variations? For example, how does the water quality (dissolved oxygen, salinity, nutrient level) and flow dynamics differ in these estuaries?
6.	In lines 271 to 273, could you explain why the influence of bay water will decrease basal area? Are the trees inundated with bay water?
7.	For table 1, it might be helpful to provide the total mangrove cover for west coast, east coast, and East Malaysia for ease of comparison. It can also be beneficial to include a column of percent area to give the audience a better idea of the distribution of mangroves in your study area.
8.	For table 3, it will be nice to have the percent area for each mangrove species.
9.	The language is professional throughout.
10.	The figures are very relevant, of high quality and clear to follow.
11.	It might be good to include some information on the spectral profiles of the different species for future studies.
Experimental design: 1.	The research question is well defined, and the area is understudied in the literature.
2.	The processing of the remote sensing data is standard. (Does the ALOS dataset come with the atmospheric correction?)
3.	In line 108, could you be more explicit and elaborate on your supervised classification step? Did you train on four classes of dominant mangrove taxa and the unclassified, and how many samples did you train on for each class?
4.	The use of GCP in the experimental design makes the result more rigorous. The ground data of dominant mangrove taxa provides good information on color and texture for the remote-sensing work.
5.	The accuracy assessment with quantity, exchange, and shift is rigorous.
6.	In line 139 to 140, how would you expect the spectral signature of mangrove to be affected with inconsistency in time between satellite image and fieldwork?
Validity of the findings: 1.	The findings from the ground-truth and remote sensing data are in agreement.
2.	The data is robust, with both field and remote sensing data.
3.	The subject of the study (mangroves at Brunei Bay) is novel and comprehensive.
4.	The conclusion links back to the research question and clearly states the potential use of the result.
Additional comments: The manuscript can be improved to involve more scientific background on the different mangrove species and possible explanations of the different distributions of species among estuaries.


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: STATUS OF THE UNDISTURBED MANGROVES AT BRUNEI BAY, EAST MALAYSIA: A PRELIMINARY ASSESSMENT BASED ON REMOTE SENSING AND GROUND-TRUTH OBSERVATIONS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The English language should be improved to ensure that your international readers can clearly understand the information provided effortlessly. In particular, I was found numerous instances of sentences/ paragraphs starting with link words (e.g. despite, nevertheless, although, while)   One option is requesting any of your native English speaking colleagues to review the manuscript. Some examples where the language could be improved include lines 22-23, 42-46, 139-144, 165-167, 176-180, 226-230, 276-280, 284-286

In the title a better choice would be ‘undisturbed’ instead of ‘pristine’.

Your introduction section needs more details on use of remote sensing technology for mangrove mapping. The material in discussion section is a better fit for introduction section. See my comments in discussion section. You should also expand upon the knowledge gap in both the study area and mangrove mapping using remote sensing.

L36-40: You are reporting estimates of multiple properties which is not always desirable in abstract. It will be helpful if you can simplify this reporting.

L40: The readers have no idea of the Complexity Index after reading first few lines of the abstract.

L49: It is not clear why “bay-mangrove complex, forest nature” are chosen as keywords.

Line 53: Sixth rank for what? In terms of area?

L66-67: Scientific attention for what purpose?

How is the statement in L194-196 is connected to the next (L196-204)

L319: ‘can serve’ not ‘can be severed’

L323: ALOS data not ALSO

I could not find the table and figure title which made it difficult to comment on those.

Table 2: No need to include both errors and accuracy -- reporting just the accurries would be sufficient.

Section 2.3: Field photographs would be useful for the readers.
Experimental design: The remote sensing component and ground inventory can be linked in various aspects. You have used only the location information for species mapping. With the rich ground inventory you have collected, I would strongly suggest to include a section on estimating the complexity/diversity using of mangrove species remote sensing data

Section 2.2: I find the remote sensing methodology section to be particularly weak. Why did you use ALOS data for this study? For e.g. freely available Sentinel 2A data has similar spatial resolution as ALOS data and could have provided up-to-date imagery for this research. Please provide a clear list of input bands for classification. Why did you use maximum likelihood classification (MLC) only? Fassnacht et al (2016) reported that nonparametric classifiers (decision trees, random forest, support vector machines) performs better than parametric methods like MLC for vegetation classification. (http://www.sciencedirect.com/science/article/pii/S0034425716303169)

I like the use of accuracy assessment following the method by Pontius and others, however more description about this method would be helpful for the readers.

L152: Please provide a description of the complexity index.

L153: In what context did you use P-DATA PRO software?
Validity of the findings: Section 3: Please divide the result section in relevant subsections with headings. E.g. 3.1 Classification accuracy of mangroves

L187-188: Same information has been provided in L176-178. You can merge the reporting and mention that similar observations were found in both remote sensing and ground observations.

How is the statement in L194-196 connected to the next (L196-204)?

Section 4:
L207-212: better fit for introduction section
L216-226: better fit for introduction section

L 224-226: I don’t agree completely. Mangroves are mostly seen in tropical areas where cloud is a big challenge for remote sensing community. To regularly map and monitor mangrove extents, SAR data could be as good as optical data if not better.
Additional comments: The manuscript reports current status of mangroves in Brunei Bay using Remote Sensing technology and extensive field observations. There is definitely a huge need for this kind of study to monitor and protect one of the vulnerable ecosystems of the world. However, the study designs are not adequate and manuscript needs language editing.


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: STATUS OF THE UNDISTURBED MANGROVES AT BRUNEI BAY, EAST MALAYSIA: A PRELIMINARY ASSESSMENT BASED ON REMOTE SENSING AND GROUND-TRUTH OBSERVATIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Writing was among the biggest concern for this manuscript. However the current manuscript has improved a lot thanks to the extensive language editing.
Table 4: Please remove the black-background for the ‘total’ estimates. You can perhaps use font in bold for that row.
Figure 1: Scale needed for left hand inset; scale bar is not visible on the ALOS image.
Figure 4: Should the title be “mean spectral reflectance…” or “average spectral reflectance…”
Experimental design: I am not quite satisfied with the reason you provided justifying the use ALOS data. The time difference between ALOS data and field data collection is 4 years. For Sentinel-2, the time difference with field data would be 1 year only, which makes Senitnel-1 a better choice. Perhaps you can add this information in the section where you mention the possible issues with time gap.

I am also not fully convinced with the reason behind the selection of MLC over other non-parametric classifier. It is completely wrong to say that MLC is still considered as the benchmark for mangrove mapping related study based a single paper. You can cite the paper by Kuenzer et. al., 2011 (http://www.mdpi.com/2072-4292/3/5/878) to justify the choice of MLC. However, please remember that numerous studies in the last 6-7 years have used more advanced methods. Mangrove mapping is not an isolated problem of remote sensing image classification. While the majority of remote sensing community is moving towards a non-parametric image classification methods, it will unwise to not to adapt/test those methods for mapping mangroves.
Validity of the findings: None to comment
Additional comments: None to 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: ACUTE SLEEP FRAGMENTATION DOES NOT ALTER PRO-INFLAMMATORY CYTOKINE GENE EXPRESSION IN BRAIN OR PERIPHERAL TISSUES OF LEPTIN-DEFICIENT MICE
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript ' Sleep fragmentation does not alter peripheral or brain cytokine gene expression of leptin-deficient mice', the authors investigated two factors, acute sleep deprivation and leptin deficiency (obesity) on the production of pro- and anti-inflammatory cytokines in peripheral tissues and the brain. The study shows no significant interaction between sleep fragmentation and leptin deficiency in regulating the inflammatory conditions. Although the results of this study do not conform with some of the published work and did not demonstrate their own hypothesis, it is described with professional langue with sufficient background information, literature research as well as detailed result discussion. The authors further discussed some of the potential caveats at the end of the discussion, which is good for the authors to draw their own conclusions.
Experimental design: One issue with the experimental design is that the authors did not discuss why they only choose acute 24hr sleep deprivation for their study. The longer duration or chronic sleep deprivation monitor may be necessary to draw a more valid conclusion.
Validity of the findings: 1. In figure 1, the authors need to explain why without SF treatment, the control group mice also show weight loss.
2. In all figures, the way the authors describe the statistical difference between groups is very confusing. Instead of labeling with the bar with a/b or A/B, it is better with the more common way, asterisks system with lines to indicate between the different groups. In addition, in Figure 2C it is better to move the labels to 2A instead.
3. The authors concluded that leptin deficiency increased both pro- and anti-inflammatory cytokines in all the test areas of the brain. This is interesting but could not be easily explained, as of how can one factor leads to complete opposite effects at the same time. The authors need to explain this confounding results or further validate their data.
Additional comments: I would like to thank the editor for inviting me to conduct the review work. I really appreciate this chance to work with you and am looking forward to more opportunities to contribute to 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: ACUTE SLEEP FRAGMENTATION DOES NOT ALTER PRO-INFLAMMATORY CYTOKINE GENE EXPRESSION IN BRAIN OR PERIPHERAL TISSUES OF LEPTIN-DEFICIENT MICE
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this study, the authors used leptin-deficient mice to study the relationship between sleep fragmentation and cytokine gene expression. Overall, the authors provided sufficient discussion in the text. However, I have some concerns about this work.
1. In general, the whole text is fluent. But I think the author could do a better job if they revise and improve the language more carefully. There are still some grammatical mistakes in the paper. Meanwhile, some sentences are difficult to understand. My suggestion is to use simple sentences if the authors have any difficulties in writing complex and long sentences.
2. The authors should improve the introduction to tell the readers about pro-inflammatory cytokines, especially the genes that they studied in this work. More importantly, since they authors only studied 3 genes and several tissues in this work, is that appropriate to claim "does not alter peripheral or brain cytokine gene expression" in the title?
3. One of my major concerns is about the sleep status in leptin-deficient mice. As the authors mentioned in the text, previous study has shown that leptin plays an important role in regulating the sleep status and the leptin-deficient mice exhibited abnormal sleep cycle. I wonder whether it is appropriate to apply artificial sleep fragmentation on those animals since they already have problems in sleep. The authors should clarify and discuss this point.
4. It seems that in many samples (figure 2 and figure 3), the OB SF has a trend to increase or decrease. The huge variation in each group may eliminate the statistic difference. I think it is reasonable to add more animals into each group to make the conclusion more convincing.
5. Figure 1. The sample size of OB SF is 9 in the raw data. But it is 8 in the figure 1. The authors should clarify this.
6. The authors should mention the sample size of Figure 2 in the text.
7. Since the qPCR is the key experiment in this study, the authors should provide the data of primer validation, such as the images of a single band of the PCR product on the gel.
Experimental design: no comments
Validity of the findings: no comments
Additional comments: no 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: ACUTE SLEEP FRAGMENTATION DOES NOT ALTER PRO-INFLAMMATORY CYTOKINE GENE EXPRESSION IN BRAIN OR PERIPHERAL TISSUES OF LEPTIN-DEFICIENT MICE
Review round: 2
Reviewer: 1

Output:
Basic reporting: Overall, I am satisfied with the revised version. I only have two minor comments:
1. Line 105-106: "This value exceeds by an order of magnitude the number of baseline arousals that typically occur in ob/ob and wild-type mice, respectively, in similar conditions". The authors should re-write this sentence to make their point clear.
2. Figure 1 and Figure 4: As the authors mentioned in the responses, one mouse in the OB SF group was removed during the experiment due to health reasons. But it seems that they still used that mouse in Figure 4. The author should clarify this point.
Experimental design: no comments
Validity of the findings: no comments
Additional comments: no 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: HOW HAS OUR KNOWLEDGE OF DINOSAUR DIVERSITY THROUGH GEOLOGIC TIME CHANGED THROUGH RESEARCH HISTORY?
Review round: 1
Reviewer: 1

Output:
Basic reporting: The purpose of this paper could be made clearer. We know, for example, that our knowledge of the fossil record can change over time, but the figures all seem to show generally the same patterns of rises and falls. Some recommendations (section beginning L604) are made for future data collection, but the applied approach (SQS) can (and does) already correct for these biases (see Alroy 2010a-c, already cited in the manuscript and the notes in the Perl script included in the supplementary information). Similarly the correlations seem problematic as there is no clear precedent for either sea level or temperature to be correlated with dinosaur diversity (see also comments below). More broadly I'm not sure what to take away from the manuscript. At present there is only a weak attempt to establish predictive power for future dinosaur richness curves (L401-413). However, I am not convinced that the logic holds here (i.e., the largest differences between 1991 and 2015 richness correspond to the time bins where we can expect greatest volatility in future estimates). Instead it would make more sense to ask what drives the largest changes? For example, is it the discovery of new, or increased exploration of older, formations/basins that drives change? This would add the greatest relevance to the data. I also strongly feel that taxonomic revisions should come in here too, but these are not currently included in the data (see below).

Another potential question currently unaddressed, but potentially addressable concerns a different relationship - that between richness and sampling proxies. The authors themselves point out that this would be interesting (L365, L411-413), and this data is easily gleamed from the Paleobiology Database. This has already been partially addressed by Benton (2015, already cited), but there is clear room to improve and expand on his analysis. I would strongly urge the authors to consider addressing this as I think testing the hypothesis that sampling and richness become increasingly decoupled would lead to the most interesting result possible from their data (regardless of outcome).

The language is mostly clear but could be improved by increased brevity/formality (e.g., "increasingly more even", "newsworthiness") and although the reference list is large and the discussion well cited a number of key papers could be mentioned. For example, some other important historical approaches to the dinosaurian record, albeit with more of a phylogenetic focus, are Weishampel (1996) and Tarver et al. (2011). These seem worthy of mention, if minimally to establish precedent. (See also additional references below.) The title should also be changed as it uses time twice in completely different ways but without appropriate context. I suggest delineating these as "geologic" vs "historical" time.

There is currently a complete absence of the model/correlation results from the main manuscript which seems like a major omission. (I had to dig through the supplementary files to find these.) These should be moved to the main text as a table or tables. Otherwise I felt that the discussion focused more on dinosaurian diversity in general rather than on specific changes to the fossil record over the 24-year sampling interval. For example, the Jehol biota has dramatically altered our picture of the origin of birds, and the position of therizinosaurs has been settled upon. More recently, of course, the Baron et al. (2017; Nature) paper has rearranged key clades at the base of the dinosaur tree which can affect our understanding of the completeness of the early part of the Mesozoic dinosaur record.

As a final point the authors discuss the "redundancy hypothesis" (L376-377), but do not defend its criticisms of sampling corrected diversity (i.e., SQS), which weakens the manuscript. This point should be addressed directly.

J. E. Tarver, Donoghue, P. C. J. and Benton, M. J., 2011. Is evolutionary history repeatedly rewritten in light of new fossil discoveries? Proceedings of the Royal Society B, 278, 599-604.

Weishampel, D. B., 1996. Fossils, phylogeny, and discovery: a cladistic study of the history of tree topologies and ghost lineage durations. Journal of Vertebrate Paleontology, 16, 191-197.
Experimental design: In its current form many aspects of the experimental design are not made clear and there appear to be some critical omissions that the authors should minimally address in the text as they potentially strongly bias their results, if not modify their analyses to more directly account for them.

The most critical of these is that their historical approach is likely very misleading as it ignores other changes than just sampling. Specifically, we know that taxonomy, and dinosaur taxonomy in particular, fluctuate dramatically over time (Benton 2008), and can even be heavily influenced by single workers (Benton 2010). Here the authors appear to not correct for this, and thus their 1991 data adheres to 2015 (or likely even more recent) taxonomic opinions. Taxonomic opinions can be extracted from the Paleobiology Database and a new synthesis constructed, so this could be addressed directly. At present using modern taxonomic opinions will lead to the *appearance* of a closer relationship between 1991 and 2015 data that is bias and not signal. In a similar vain the stratigraphic resolution of fossil occurrences tends to become refined over time, as does the geologic time scale. Both these factors are likely to influence the data, although the former is likely to be harder to address and the latter may not be relevant if binning data by geologic stages. However, these should be discussed as we have seen, for example, Chinese formations thought to contain birds older than Archaeopteryx be re-dated as Early Cretaceous.

Some other issues likely just need clarification. For example, the authors use SQS, but key details are missing. One obvious one is the quorum level used. From examination of the Perl script a value of 0.4 seems to have been applied, but no justification for choosing this is made. In fact the authors later suggest multiple sampling levels should be used (L587-588). I think this is worthy of exploration. For example, lower quorums would (potentially) allow more data to be returned, and hence can modify the correlations (see also comments below). Similarly a major issue, already discussed in places by the authors, is that the Good's U term will be biased by the large number of singletons that are inevitably generated from publication-formed databases (L548-549, L610-612, L620-621). Implementations of SQS has always had some form of correction for this, for example the "single publication occurrence" correction (Alroy 2010a-c). However, it is not clear what correction (if any) the authors are using here. This is a critical point as without such a correction the SQS results are compromised.

Some changes to the correlations could also be considered. Currently it appears that the length of time series changes dramatically (based on the figures), i.e., 1991 time series often have missing bins that are filled in the 2015 data. This makes comparison across correlations difficult as any changes could be attributed *either* to the additional data *or* to the absence of key bins from the correlations. There is no clear way to fix this however, except perhaps for only using data from bins present in both 1991 and 2015 for each correlation. Similarly, it would be interesting to show graphically how the correlations change across *every* two-year value from 1991 to 2015. Are the changes monotonic or are there big shifts? If the latter, what changes to the fossil record precipitate these? It would also be interesting to correlate diversity with diversity and not just the external proxies. Visually it seems that there is not a major difference in many cases (i.e., data subsets), but it would be good to quantify these.

Finally, the authors use a genus-level approach, but others have noted how this can confound correlations between richness and non-biogenic time series (e.g., Wiese et al. 2016). As this is a primary aim of the manuscript this point should minimally be addressed in the text if not through quantitative analysis (i.e., a separate set of analyses at the species-level).

Wiese, R., Renaudie, J. and Lazarus, D. B., 2016. Testing the accuracy of genus-level data to predict species diversity in Cenozoic marine diatoms. Geology, G38347.1.
Validity of the findings: There are potential issues with both the SQS approach (singleton correction) and correlation (missing bins) that urge some caution in accepting the results as they stand (see detailed comments above). The database used is generally very solid for dinosaurs, but critical aspects (taxonomic opinion shifts) are not being exploited. The conclusions could be much briefer and stronger (e.g., after addressing for taxonomic changes over historical time).
Additional comments: No further comments.