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: ALLOMETRIC SHELL GROWTH IN INFAUNAL BURROWING BIVALVES: EXAMPLES OF THE ARCHIHETERODONTS CLAIBORNICARDIA PALEOPATAGONICA (IHERING, 1903) AND CRASSATELLA KOKENI IHERING, 1899
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is a correctly structured piece of research. The references used provide good context for the reader. Figures are ok (there are some issues with the captions though, pointed out in the attached PDF file). I would like to have a table or two reporting the results from some analyses in the main article (see Experimental design). On the negative side, I was not able to replicate the results reported in the manuscript using the supplementary data provided by the authors. However, my main problem with this article is its deficient English, which needs substantial polishing in order to make the manuscript publishable (I have made several corrections and comments in the attached PDF file aimed in that direction).
Experimental design: I think this work is good in both intention and execution, as it addresses the study of allometric growth patterns using longitudinal data (a relevant topic in paleobiology that requires accumulation of study cases like this) using an adequate quantitative toolkit (geometric morphometrics and multivariate statistics) and discussing relevant/interesting implications (taxonomic, paleobiological, evolutionary). However, there are some issues that need to be addressed. My main concerns are (see also comments in the attached PDF):

i) Some passages of the manuscript need further elaboration. In particular the geometric morphometrics paragraph at the end of the Introduction section, as well as discussion relating these study cases to the study of heterochrony at the end of the Discussion section, should be expanded.

ii) The report of multivariate regression analysis (MRA) is problematic. The authors do not mention the software they used, and the results reported are not those of an ordinary MRA (e.g., permutations and linear combination of response variables are not typical elements of an ordinary MRA). More thoroughness is needed in this regard to fully understand what the authors did. Also, I think that the information provided in Supplementary Data S4 and S5 regarding MRA should be reorganized as one or two tables and included in the main article, as these results are crucial to describe the covariation between size and shape in the studied taxa.

iii) The supplementary material provided by the authors does not allow replication of the procedures and results reported. In the case of Supplementary Data S2, some of the normalized (as I can infer from the name and number of columns) coefficient values from the last columns can not be read. In the case of Supplementary Data S3, it is not clear to me whether the table contains normalized or raw Fourier coefficients: the names of the columns suggest that these have been normalized (as coefficients start at D1), whereas the number of columns (28) and the values of the first three columns of coefficients (invariant when these have been normalized) suggest these are raw. Also, I analyzed the data from Supplementary Data S3 using the Momocs package in R, and was not able to produce the same morphospace as the one shown in Figure 3B.

Apart from this I think that, in general, the quantitative tools described in the manuscript have been adequately applied to answer a well defined and relevant question.
Validity of the findings: I think this work is a good addition to the literature addressing allometry patterns in fossil species. Concerns regarding MRA aside, the analyses used are an adequate choice for conducting a study of this nature, and interpretation of the results is correct. Findings are appropriately placed within the paleontological context of the study case, and their implications explored to a reasonable extent (with the exception of the discussion of heterochrony mentioned in Experimental design). There is nothing in the conclusions that is not justified from what the authors report. The results and conclusions seem valid to me, although the issue of reproducibility needs to be addressed to be completely sure.
Additional comments: Please check the manuscript and supplementary materials carefully and introduce the changes needed to improve the overall readability, comprehensibility and reproducibility of this work.


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: ALLOMETRIC SHELL GROWTH IN INFAUNAL BURROWING BIVALVES: EXAMPLES OF THE ARCHIHETERODONTS CLAIBORNICARDIA PALEOPATAGONICA (IHERING, 1903) AND CRASSATELLA KOKENI IHERING, 1899
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised version of the manuscript has greatly improved in readability and clarity, especially regarding the motivations and procedures adopted by the authors. Modified versions of figures represent a nice improvement as well (I particularly liked the new version of Figure 2). I still miss one or two tables reporting the results of regression analyses in the main article (I explain the reason below). I was able to repeat the main analyses the authors perform, obtaining the same results reported in the manuscript for the case of C. paleopatagonica but not for C. kokeni, something that needs to be addressed. I made some corrections in the attached PDF file, but these are all minor.
Experimental design: Having been able to properly analyze the data, I have two main concerns regarding the analytical approach adopted by the authors. The following comments are valid for the case of C. paleopatagonica, but are applicable to the case of C. kokeni as well:

1) The approach adopted by the authors is only superficially multivariate. Although three principal components are retained and analyzed by means of a multivariate regression analysis (MRA), the authors are focused exclusively on the changes along PC1, as both the figures and discussion provided reveal. I do not think this is a bad thing per se, especially considering that the shape transformation represented by PC1 is not only the main axis of variation in its own right, but also contains the allometric variation the authors are interested in. However, by including PC2 and PC3 in the analyses but not in the subsequent discussion, the authors give an unnecessarily complicated (and potentially misleading) picture of their study. I think that, given the primary interest of this work, a univariate regression between size and PC1 is both more adequate and easy to interpret.

2) By performing their MRA approach using the pooled sample of outlines, without structuring their analyses by individuals, the authors are effectively pseudo-replicating (i.e., several outlines can be extracted from the same individual, but these outlines are not statistically independent from one another), something that undermines the validity of the obtained p-value. Performing regressions in this way can still be valuable if a more nuanced, descriptive interpretation is attempted (i.e., looking for general trends in the values of slopes and intercepts rather than the concrete p-value for these coefficients), although the reason behind this decision should be clearly stated. This is why I think the tables from Supplemental Data S4 and S5 are far more useful than the reported p-value, and thus should be included in the main article (rather than be relegated to the supplementary materials).

I do not think these flaws are fatal. I would recommend the authors to perform a univariate regression (one for each species) using PC1 as response variable and focus in the interpretation of slopes (p-values can still be reported, although as I already mentioned they need to be interpreted with caution). I am including this analysis in the R script I wrote to replicate the procedures. Alternatively, in the case the authors choose to retain the MRA approach, I would like to see a little more attention given to PC2 and PC3, both in the discussion of the significance of these shape transformations and in the figures (i.e., provide visual representations of the shape transformations implied by PC2 and PC3).

In addition, I was not able to replicate the results reported for C. kokeni using the supplementary data provided by the authors (Supplemental Data S3). In short, the axes resulting from the PCA of the normalized coefficients stored in this table are different from the ones depicted in the Figures (Figs 3B–C) (I performed the analyses in the R environment using the basic functions; the procedures can be readily repeated using the R script included in the general comments for the authors. This same script was used to correctly replicate the results reported in the manuscript for C. paleopatagonica). I assume the problem is the uploaded data; if so, replacing the file should be enough. However, if this discrepancy stems from an incorrect analysis the problem could be more serious, as this could compromise the conclusions of the study.
Validity of the findings: The results and conclusions seem well founded, and the implications are discussed to a sufficient extent. As noted above, Supplemental Data S3 must be replaced by the file containing the actual coefficients used by the authors to perform their analyses.
Additional comments: ## R script

## import the data (as csv file and skipping the first two lines)
data<-read.csv("/home/pablo/Insync/peerj-25256/supplemental/peerj-25256-Supplemental_Data_S2.csv", skip=2)
str(data)
head(data)
dim(data)

## store the coefficients, size and classification of the sample in different objects
coe<-data[,5:ncol(data)]
size<-data[,2]
class<-data[,4]

## principal component analysis on the matrix of coefficients
pca<-prcomp(coe)

## plot morphospace
plot(pca$x[,1:2], pch=16, col=c("red", "blue","black")[class])

## multivariate regression of PC1, PC2 and PC3 on size
mra<-manova(pca$x[,1:3]~size)
summary(mra)

## univariate regression of PC1 on size
ur<-lm(pca$x[,1]~size)
summary(ur) ## results

## plot the regression
plot(size, pca$x[,1], pch=16, xlab="Size", ylab="PC1")
abline(ur, col="red")


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: COMPREHENSIVE ANALYSIS OF MITOGEN-ACTIVATED PROTEIN KINASE CASCADES IN CHRYSANTHEMUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, the authors conduct a good study on MAPK cascades of chrysanthemum. With gene sequencing and PCR, a couple of CmMPK and CmMKK genes are characterized and expression pattern of these genes are quantified. In addition, the interaction between CmMMK and CmMPK are unveiled with yeast two-hybrid assay and their contribution to stress resistance of chrysanthemum are evaluated in various stressed growth conditions.

The author gains a huge amount of experiment data with solid work as well as a comprehensive genetic analysis. The conclusions are clearly stated in the manuscript and reasonably made according to the experiment data. Yet, there are several issues in this manuscript such as loss of statistic test and incomplete figure legend, which can cause the confusion and misinterpretation. Overall, the manuscript is publishable after all the issues are fixed properly. Therefore, I suggest minor revision on this manuscript.

Major Issues
1.	In figure 3&4, the author does NOT provide any statistic tests to show the significance of difference. To confirm this, statistical analysis needs to be added in the method part to explain like what statistical test is used, what p value is, etc.
2.	For line 323, the CmMPK13 and CmMKK4 have opposite expression level in root according to figure 3a and 3b, (MPK 13 is low but MKK4 is high). Given root is the main organ responsive for osmotic stress, should this need to be involved in the discussion here? Also, it seems that the expression level data in figure 5 showing the similarity comes from the whole plant but not the root, so it is questionable that how relevant this data is to plant salt resistance. As shown in figure 3a and 3b, the expression of MPK13 and MKK4 in other part of plant (i.e. stem) may offset their difference in root, which leads to the overall similar expression.

Minor Issues
1.	Reorganize the abstract part following the instruction of Peer J. No need to highlight the background, method etc..
2.	In the abstract and line 20, the sentence that “qRT-PCR and yeast two-hybrid assay were used for the further analysis” is ambiguous, the author should clearly state what analysis is done by qPCR and yeast assay.
3.	Beside the figure, author should also state what type of plant each sign (blue circle, green square and yellow triangle) represent in the figure legend.
4.	In result 3.1, the author should be clear on what criteria or standards to divide all the motifs into four groups for the comparison. If they are grouped by software, then what logarithm does the software use should be mentioned.
5.	In figure 4, what is CK, C4, and H40 stands for? Clarify them in the figure legend.
6.	In line 224, what is the resistance that MPK3 plays role in?
7.	In line 249, should be among not between the MKKs.
8.	In line 317-319, figure 5 should be referred after “its expression was significantly increased after PEG and salt treatments” since the figure3 doesn’t have data to support that.
Experimental design: no comment
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: COMPREHENSIVE ANALYSIS OF MITOGEN-ACTIVATED PROTEIN KINASE CASCADES IN CHRYSANTHEMUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: In their manuscript submitted to PeerJ, Aiping Song et al. present an interesting finding about the MKK and MPK genes from Chrysanthemum sp.. From phylogenetic and conserved motif analysis from different plant species, authors have characterized 6 MKK genes and 11 MPK genes from Chrysanthemum sp. and their response to phytohormones and stresses.
Introduction has been well-written with adequate references emphasizing on the important role of Mitogen Activated Protein kinases (MAPK) in plants and their crucial role in various signal cascade in response to stress or other physical requirements like growth, differentiation. The authors thus, successfully highlight the importance of 11 MPK and 6 MKK from Chrysanthemum sp and their interaction with each other in response to various signals forming different signal cascade finally emphasizing the novelty of this study. The manuscript has been drafted in accordance with PeerJ standards and all the figures are of high quality. However, for figure 4 author didn’t mention the meaning of the abbreviations CK, C4 & H40 in the figure legends which raises ambiguity in data interpretation. For each dot blot strip in figure 6, labeling of protein corresponding its dot is slightly misleading.
Experimental design: The authors through phylogenetic sequence analysis has identified 6 MKK genes and 11 MPK genes from Chrysanthemum sp.. Later, authors have functionally characterized these MKK and MPK genes using various experimental techniques. Experiments designed to address the unknown, are well defined and technically sounds good.
Validity of the findings: Authors reveal the important role 6 MKK genes and 11 MPK genes from Chrysanthemum sp. in response to plant growth, abiotic stress and phytohormones. The results/discussion as reported by authors need some edits as suggested below:
Authors for figure 4 didn’t mention the meaning of the abbreviations CK, C4 & H40 in the figure legends so it was difficult to interpret the results for section 3.3
The discussion is lengthy. I would appreciate if the authors make it more concise and interesting by including figure and less text.
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: THE EFFECT OF RUNNING VERSUS CYCLING HIGH-INTENSITY INTERMITTENT EXERCISE ON LOCAL TISSUE OXYGENATION AND PERCEIVED ENJOYMENT IN 18–30-YEAR-OLD SEDENTARY MEN
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is very well written, with only a couple of minor grammatical oversights.
The literature and references are primary and pertinent and sufficient background is provided to establish context.

The results shown answer the hypothesis provided.
Experimental design: This work is original. It performs incremental work within the areas of HIIT, NIRS and exercise prescription.
The research question is well defined, certainly relevant. If exercise adherence and health benefits within sedentary populations can be obtained through time efficient and enjoyable exercise modalities, this is then of obvious benefit.
The authors should perhaps mention that within the introduction/discussion that establishing the potential health benefit of one mode of exercise over another is not the answer to removing sedentary behaviour nor ensuring exercise adherence. It does however allow the practionner to direct an individual to a potentially more favourable exercise session- that may aid adherence, greater facilitate health benefits etc.
The experiment has been carried out with rigour, although I must admit to not fully understanding the rationale of not matching the workloads. If these are not matched, then comparisons between the two modes of exercise on physiological strain and self-report measures appears to be irrelevant, as clear differences will be present. The authors discuss matched workloads (submax/incremental) (lines56-59) within the introduction and state that this work has not been carried out with sedentary populations and so I wonder why this was not carried out as the experiment. I in no way mean to be obtuse.
The authors explain that as the workload between running and cycling is likely to differ it is important to describe this to better explain which modality is more ‘beneficial’ for sedentary individuals. This work therefore looks to detail the differences between different modes and intensities of exercises and therefore will find inherent differences. I again do not mean to appear dismissive, I just question the meaningfulness and perhaps this needs to be more explicitly explained.
Validity of the findings: Figure 1 is clear and well presented.
Figure 2 panel A may benefit from a scaling change to make the data more obvious
Figure 3 is clear and well presented.
Figure 4 is clear and well presented
Table 1 is clear and well presented
Raw data is suggested within a table or written within the results text for figure 3 as large SD's are shown for panel C (Power). It is important to see this data as whilst the authors point out bike and run 'HIIT' sessions were not matched, nor meant to be; the closer the matching of the work intensities the more relevant this work is. Further raw data would benefit the NIRS data with individual data shown. The concept of individual prescription is applicable in elite athletes and sedentary populations for exercise adaptation.
The conclusion is structured logically, discusses the findings in detail and is linked back to the original research question.
I do not agree that either protocol can be called a HIIT protocol. This is largely based upon Figure 3 panel B; HR values would need to be c.180bpm and Figure 4 panel B; RPE scores for HIIT RUN are also not of the required level for maximal to near maximal efforts. It is suggested that HIIT be changed for submaximal efforts, unless the data does support a HIIT protocol.
Lines 387-391. I am not sure if the lower metabolic cost of eccentric muscle actions can be used to as an explanation for the lower HHb findings in the RUN exercise as RUN exercise has both eccentric and concentric actions. Perhaps the explanation should be removed. Lines 380-387 provide ample explanation.

I must admit again that I do not fully understand the rationale of the research. The authors state in lines 554-555 the perceptual responses to the two modes of exercise which essentially that; Exercising at a lower physiological stress, is reported as easier by the participants.
I welcome the authors to explain the importance and make this clear and obvious to the readers, so they like myself largely question why the workload was not matched.
Additional comments: I must commend the authors for this written work. It is well presented and has been carried out well.
I do not mean to dismiss the rationale behind the work, I just do not fully understand the premise or not work matching the cycle and run protocols.
I do feel that data individualisation will benefit the work and show the individual responses to both modalities, as with all exercise studies valuable data can be lost with the means.

Separate point:
Lines 209-212: I am interested in the reported movement artefact during the rest periods. This is unusual. Did this occur in the TSI% signal as well?

Minor grammatical:
Line 181: ofHITT ,
Line 202: previously(
Line 391: HIITRUN (full stop missing)


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

Input:
Title: THE EFFECT OF RUNNING VERSUS CYCLING HIGH-INTENSITY INTERMITTENT EXERCISE ON LOCAL TISSUE OXYGENATION AND PERCEIVED ENJOYMENT IN 18–30-YEAR-OLD SEDENTARY MEN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Scientific bakground for this study is insufficient.
Structure of the manuscript should be reviewed in depth.
Please see General comments.
Experimental design: The introduction needs more detail and to be targeted on the main factors.
Some parts of the experimental design are not related to the research question.
Experimental design as proposed appears incomplete.
Please see General comments.
Validity of the findings: Data cannot be judged and discussed properly based on the experimental design used.
Please see General comments.
Additional comments: General comments

Authors want to study the effect of 2 modes of dynamic whole body exercises (running versus cycling) during high intensity intermittent exercise on various physiological variables and perceived enjoyment in sedentary adults. This topic is of interest.  A high intensity interval training (HIIT) exercise format was proposed in a single session.

As currently proposed, HIIT is not really defined and characterized throughout the manuscript. Authors should refer to a stronger scientific background on HIIT. What is lacking is any consideration on “high intensity” beside the low volume for HIIT. HIIT is an enhanced form of interval training involving brief, high-intensity, anaerobic exercise (ranging from 85% to 250% VO2 max for 6 s to 4 min) separated by brief, but slightly longer bouts of low-intensity aerobic rest (ranging from 20% to 40% VO2 max for 10 s to 5 min).
With regards to the methods and results sections, less information on exercise intensity is proposed. We can only extract from Figure 3 (and Table 1) that intensity level during the two exercises is around 60-65%VO2 max, <80%HRmax with a mean power output of 400W. Please adjust accordingly. Finally one fundamental question is to know what HIIT format / model was really used in the present study? How it was used ?
	Two modes of exercise were compared. However, the two modes seem not matched according to some points highlighted below.
First, in their experimental design, authors used free-paced cycling compared to constant-paced running HIIT. However, constant- and free- paced movement produce likely different levels of physiological stress without considering the mode of exercise (running vs. cycling). Thus, mode of pacing is one confounding factor. Authors have to comment on this choice that represents a serious issue.
Second we do not know the workload that was manipulated for both modes of exercise (it only stated during the warm up phase). In addition to control the movement pace, similar intensity in terms of absolute workload and relative workload (based on % of VO2max for a specific exercise mode) are needed for comparison purpose. Methods are poorly detailed on intensity for the two modes. Only based on Figure 3, we can try to judge what were the intensity levels. See previous comments on that issue.

The Introduction and Discussions sections are too long. I would ask the Authors to re-arrange them in order to make the manuscript easier to read and understand.

In the Introduction, there are no real rationale on the use of running or cycling in terms of physiological / perceived responses to single HIIT session. Authors have to inform readers that the two modes of whole body exercise are based on different muscle action patterns (concentric for cycling and eccentric/concentric balance for running according to the slope; uphill running being more concentric, see reference of Minetti et al.). Importantly, information is lacking to understand why authors proposed this hypothesis. What are the relevant parameters that readers should know for such expectation on running? This is unclear.
In the Methods, authors proposed to investigate several muscle sites for evaluating oxygenation patterns but nothing appears in the introduction on this second independent factor. Again, what we know or not on regional muscle oxygenation profile for running and cycling deserves information and comments? What are the possible expectation on this point according to the 2 modes of muscle exercise? This is again unclear. All text on prefrontal cortex oxygenation is out of scope (as for fatigue ..) and should be removed. Please focus only on muscle oxygenation patterns during HIIT for 2 modes of whole body exercise. The last independent factor (time or repetition) needs also to be introduced.
To sump up, introduction, as currently proposed, is incomplete and not focused.

The description of the methodologies should report more details about the different methods used for estimating exercise intensity during the HIIT protocol used for running and cycling. In the current version, most of the details are reported by means of references to previous or other works. I would suggest to insert some formulas to allow the reader to directly comprehend the steps of the protocols and analysis.

Specific comments

Introduction
Page 7, first paragraph. It is important to define in a complete way what is HIIT and to inform clearly on what we know on the effects of a single HIIT session in running / cycling. Authors just reported “these investigations examined… have been evaluated previously etc..” but no findings are highlighted.
Page 7, second paragraph, L 56. What means “greater cardiorespiratory..” please inform readers. “Matched workload” has to be precised: absolute, relative, and domains of intensity?
Page 8, sentence 64-70 needs to be rephrased.
Page 8, line 75. What does mean “component”. Please explain.
Page 8, lines 75-77. What we have to retain from these references?
Page 8, HHb is not giving the same information on muscle as compared to cerebral tissue and cannot be used as currently proposed. As said before, only muscle oxygenation profiles have to be studied.
Page 8, Lines 83-84.. This needs to be argued. Please do so.
Page 9, line 86. The sentence like “local tissue oxygen utilisation has not been compared across exercise modes in three distinct locomotor muscles and the pre-frontal cortex” cannot justify a scientific study!
Please try to give information on the primer muscles used for each mode to explain the possible differences in muscle oxygenation profile according to the muscle sites.
Page 9, lines 87-91. This sentence needs to be argued. Please use adequate and relevant references for that purpose.
Page 10, line 110. The rationale based on scientific background on the possible differences between running and cycling for pulmonary oxygen consumption is absent.

Methods
Line 126. A protocol was done in constant pace while the other protocol was done in free pace. This is an important issue that could flaw the results.
Lines 163-168. This paragraph needs to be completed. See major comments.
Lines 172-175. The validity of this approach has to be commented.
Line 179. An incremental cycling test to exhaustion in order to get specific VO2max to the mode of exercise is needed in the design.
Lines 180+. What were the intensities of the HITT format for running and cycling exercises?
Line 189. Replace by “muscle oxygenation” here and thereafter.
Remove all information on prefrontal cortex.
Line 197. Please report also the ICC values for the reliability testing.
Line 210. Please explain this sentence and especially the values of SNR “during the passive recovery periods of the HIIT sessions, attributed to a low signal to noise ratio.” This is unclear.

Line 267. Results. For all statistical tests, report F values then p values and effect size estimates.
As stated before, since there is no rationale on the 3 factors (only 1 was partially introduced: mode of exercise) used in the introduction, this paragraph should be reviewed accordingly.

Figures: please, make them clearer (most of the panels are hard to understand, and they should be separated in different figures) and with higher quality. Also, some of the results could be transformed in statistical graphs rather than reporting all. Text and figures are redundant.

Several results have been reported throughout the manuscript. However, most of them are not statistically significant. I would suggest to report only the significant ones to emphasize the evidences, and make the manuscript easier to read.
The Discussion section is too long and should be re-arranged in order to report only the main findings and wrap up the impact of the work.

Note that there are some format errors (for reference and punctuation) throughout the manuscript.


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

Input:
Title: THE EFFECT OF RUNNING VERSUS CYCLING HIGH-INTENSITY INTERMITTENT EXERCISE ON LOCAL TISSUE OXYGENATION AND PERCEIVED ENJOYMENT IN 18–30-YEAR-OLD SEDENTARY MEN
Review round: 1
Reviewer: 3

Output:
Basic reporting: Well written and organized.
The introduction and discussion are rather lengthy and could be consolidated.
Experimental design: I appreciate the work undertaken by the authors - it is an important and relevant area of study. Moreover, the effect of HIIT modality on physiological and enjoyment responses is a novel area of study. The authors are to be commended.

In general, the experimental design is robust.
However, I have two primary concerns for the authors to address in their revision:
1. Was an apriori power calculation performed to identify necessary sample size?
2. It appears based on Figure 3C that participants were overly ambitious on the first bout of HIITCYC and consequently experienced a sustained decreased in power output for the remaining trials.  Not surprisingly, physiological responses were higher (maybe not significantly but meaningfully yes) and also RPE. Accordingly, and again not surprisingly, PACES scores for HIITCYC were lower. In contrast, power outputs were sustained across bouts 1-4 for HIITRUN with associated lower physiological responses and RPE values coupled with higher PACES scores. My sense is that if power output across bouts of HIITCYC were consistent with those for HIITRUN that the findings would have been entirely different.
Validity of the findings: Per my last comment in the experimental design section - I don't question the validity of the findings based on the existing workload performance differences between HIITCYC and HIITRUN across bouts 1-4.  However, had these been controlled and not existed the findings would have been much different. From an ecological validity standpoint and my own clinical experience with HIIT - it would be highly unusual to let previously sedentary individuals self-select their own HIIT intensity for the exact reasons observed in this study. If an individual with limited experience on a modality (i.e., cycle ergometer) is permitted to self-select the intensity, the exact scenario that occurred in this study is predictable. Individuals over-extend themselves early and become overly fatigued by the conclusion of the session (and don't have a positive response). A further problem is the high number of adverse responses experienced by the HIITCYC with the free-paced approach.

In summary, I suggest the authors address this fundamental limitation to their experimental design and findings and revise accordingly whilst taking these into account.
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: THE EFFECT OF RUNNING VERSUS CYCLING HIGH-INTENSITY INTERMITTENT EXERCISE ON LOCAL TISSUE OXYGENATION AND PERCEIVED ENJOYMENT IN 18–30-YEAR-OLD SEDENTARY MEN
Review round: 2
Reviewer: 1

Output:
Basic reporting: Article is well structured as a whole. However at some places, the length of the manuscript can be lowered.
Experimental design: Clarity for the experimental design remains an issue (see below).
Validity of the findings: Data is robust. See below one comment on the use for the three factor, repeated-measures analysis of variance.
Additional comments: Thanks to the authors for this well revised manuscript that now clearly stated that the study aims to determine the physiological load between two “self-selected” modes of HIIT exercise (running vs. cycling). Authors provided adapted responses to the first comments and argued for some methodological choices. Initially, for the methods section, it was requested to inform more as a whole. Sorry for some misunderstandings in previous comments.

A few more comments need however to be taken account:

Abstract
L 23. The “efficacy of this format exercise” cannot be evaluated with the experimental design of the study. Change accordingly.

L 25. Since this study did not match the intensity in absolute and relative objective mechanical / physiological indices (=dependant variable) between the two modes of exercise, authors have to state here and throughout the manuscript the “self-selected pace strategy” they have used.
If authors included in their study “bouts of Wingate cycling exercise and bouts of maximal speed running exercise” (as reported in their responses), please give this information for clarity purpose. But in this case, maximal speed running exercise is not a constant-paced running task as underlined? This is still confusing.

Introduction
L 100-104. This sentence is not useful for building the rationale of the study. Only discussion could use such perspective.

L 131-135
“The HHb in the pre-frontal cortex is increased during high intensity cycling exercise (Kriel et al. 2016; Smith & Billaut 2010), compared to pre-exercise values and could be a potential mechanism contributing to exercise cessation (Shibuya et al. 2004) and therefore influence the physiological responses to HIIT exercise.”

HHb is not the good signal of interest at the cerebral level to highlight. Local oxygenation mechanisms at the muscle are clearly different from those at the cerebral level. More important, since the present descriptive study does not aim to determine “potential mechanism influencing the physiological responses to HITT exercise”, all parts on frontal oxygenation is out of scope. Authors have to target on physiological (and perceptual) responses at the systemic and muscle levels. In addition, length of the manuscript needs to be lowered.

Methods
L 252; “30 s bouts of HIIT”; once again just report here the requested intensity level: “all-out” “self-paced”… See comments below and above on this issue.
L 269. Based on previous comment, PFC should be removed.

L 335. Scientific background in the introduction is well emphasised on the effect of condition (exercise mode). However, at this stage, we do not know why authors want to look at the influence of bout and site (included in the 3-ANOVA) on the dependant variables. No background (goal and hypotheses) was proposed on these two factors. Please clarify accordingly where needed.

Results.
L 345. Only one paragraph on Tissue oxygenation is enough; it is not necessary to write for each muscle one dedicated subsection.
L 356. Based on previous comment, this paragraph has to be removed.
Discussion
Comparison with other studies needs to report when needed how the level of workload was matched (subjective or objective) between modes of exercise. Otherwise comparisons cannot be done.

L 538-540. This is highly speculative.
L 541-545 : L 566-570. To remove
L 563. Please refer to the recent review on this topic (doi: 10.1007/s40279-017-0820-1)

L 689. The statement on “matched intensity running and cycling HIIT” is wrong.
How free-paced cycling HIIT was matched to constant-paced running HIIT?


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

Input:
Title: THE EFFECT OF RUNNING VERSUS CYCLING HIGH-INTENSITY INTERMITTENT EXERCISE ON LOCAL TISSUE OXYGENATION AND PERCEIVED ENJOYMENT IN 18–30-YEAR-OLD SEDENTARY MEN
Review round: 2
Reviewer: 2

Output:
Basic reporting: Basic reporting satisfies all criteria.
Experimental design: My previous comments on experimental design have been sufficiently addressed by the authors in their revised paper.
Validity of the findings: My previous comments on validity of the findings have been sufficiently addressed by the authors in their revised paper.
Additional comments: I have no further comments.
I appreciate the work the authors committed to revising their paper per my previous remarks.
This paper makes a strong contribution to the literature.
The authors are to be commended.


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

Input:
Title: THE EFFECT OF RUNNING VERSUS CYCLING HIGH-INTENSITY INTERMITTENT EXERCISE ON LOCAL TISSUE OXYGENATION AND PERCEIVED ENJOYMENT IN 18–30-YEAR-OLD SEDENTARY MEN
Review round: 3
Reviewer: 1

Output:
Basic reporting: My previous comments on this point have been sufficiently addressed by the authors.
Experimental design: no comment
Validity of the findings: My previous comments on validity of the findings have been sufficiently addressed by the authors in their revised paper.
Additional comments: I have no further comments. I appreciate the revised manuscript based on previous 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: WEAK POPULATION STRUCTURE IN THE ANT FORMICA FUSCA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors report an interesting study on an ant inhabiting unstable/recently available habitats in Finland. It expands previous knowledge on the population genetics of Formica fusca at a higher geographical scale using numerous and adequate analyses. The main result of the manuscript comes from the fact that for the first time a female-biased dispersal rate is reported for an ant species. The reading is fluent and the language is clear. I would recommend its publication in PeerJ after the authors correct some reference issues and consider some of my comments below:

-	In lines 317-331 the authors comment about young and old habitats, suggesting a male-biased dispersal in the young and a female-biased in the old. According to their results of panmixia in the locations analysed, these would be then considered as old but there is no formal statement about this in the text. In a previous work from some of the authors (Hannonen, Helanterä & Sundström, 2004), they clearly reported the age of the populations studied but in the current study it is not mentioned. Do the authors know the age of the sampling localities or just guess that they should be old due to results of female-biased dispersal?

-	In the discussion the authors also state that the highest dispersal is expected in new optimal habitats whereas subsequent colonization would lead to higher nest densities. Then, in the latter situation long distance dispersers would not be likely to occur, which could be interpreted as a change in male strategy: reduced dispersal as a way to increase their mating opportunities. Reading the manuscript one could get the idea that the females would actively disperse at higher rates than males in old habitats but maybe it should be worth discussing a bit more about this under the male’s perspective.

-	The format of the references should be seriously checked as I found numerous mistakes: PeerJ journal states that in-text citations of four or more authors should be abbreviated with the expression “et al”; however the expression “& al” can be observed throughout the text. Also, the comma before the year is also missing in several references. In the case of three authors, these should be named completely but, however in the manuscript I could find a few times the same reference cited in two ways, one according to the journal rules and another as first author et al. (e.g. Bargum et al., 2007; Sündstrom et al., 2005). In other cases, three author references are only treated as first author et al. (e.g. Sanllorente et al., 2015; Gyllenstrand et al., 2004; Drescher et al., 2007).

-	Figure 1: The word “text” appears in the middle of the map, it should be removed. Also in this figure, the haplopyte H (yellow color in the NJ tree) is not represented in any nest or at least I am unable to distinguish it.


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: WEAK POPULATION STRUCTURE IN THE ANT FORMICA FUSCA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper investigates the population genetic structure of the pioneer facultatively polygynous ant Formica fusca at a large spatial scale (35 km2) using 8 microsatellite markers and a mtDNA sequence. In ants, breeding systems (monogyny or polygyny) is often associated with the mode of colony foundation (dependent or independent colony foundation) and thereby with female dispersal abilities. At small spatial scales (hundreds of meters of few kilometers), restricted female dispersal is known to lead to population viscosity with dispersal mainly biased towards males. The expected pattern of population genetic structure is less clear for independent founding species. In this study, the authors found a merely absence of population substructure for both types of markers even though the population genetic differentiation was slightly significant for microsatellite markers.
I found the manuscript clearly written and the analysis seems appropriated (though see some in the section experimental design). I however identified three main weaknesses (1) in the way the research questions are defined (see my commentin the experimental design), (2) in the choice of the sampling design to assess population genetic structure at large scale (see comments in the experimental design) and (3) in the interpretation of the results that conclude to panmixia in the species (the main conclusion given in the title) (see comments on the validity of the findings).
Experimental design: The hypotheses being tested are not clearly developed in the last paragraph of the introduction and the rationale of the study is not that straightforward to me as explained in the following comments:

2.a. The introduction focuses only on the biological traits of ant species that could affect population structure with the idea that polygyny is more often associated with dependent colony foundation and therefore with restricted female dispersal. This was indeed shown by Keller (1991 in Ethology, Ecology and Eovlution) but using only 24 European ant species and with some exception. This association allows the authors to claim at the end of the abstract that the nearly absence of population genetic structure was unexpected in this facultatively polygynous ants. However, knowing that females are winged and found new colonies independently in this species, I do not see why the results are unexpected even if the species is slightly polygynous. More importantly, at large spatial scales, landscape connectivity, geographical barriers, population demography and colonization history can be more important in shaping the population genetic structure than species dispersal abilities. Moreover at large scale, the influence of genetic drift is strong relative to gene flow (Hutchison & Templeton 1999). Hence, if the aim of the study was to assess dispersal abilities of the species (which is the main focus of the introduction), I do not think that the large spatial scale is the more relevant scale to consider. May be it would be better to introduce earlier the idea that even though both males and female are winged, ants are not very good flyers. Dispersal of sexuals might then be sufficient to maintain panmixia at small scale but not necessarily at large scale.

2.b. If a higher genetic structure could indeed be expected at larger than small spatial scale (as I noted above), it is however not clear to me why this should be due to social organization as mentioned line 141. The authors should make the expected pattern more precise by indicating for instance whether they know the level of polygyny in the populations sampled. Given that in a population with both monogynous and polygynous colonies, no structuration was found at a small scale, why would the effect of social organisation be more pronounced at a larger scale?

2.c.  I have the same concern with sex-biased dispersal. Given that sex-biased dispersal was not observed at a small spatial scale (which is in agreement with the fact that both sexes are winged), why would the authors expect sex-biased dispersal at a larger scale? Are there some biological reasons to believe that the scale of sampling will change the results? Indeed at a large spatial scale, as noted above, extrinsic factors will be more important than dispersal abilities in shaping the population genetic structure. For now, it seems that the authors just emphasized this point because of these results (they found a slightly higher dispersal in females, a pattern rarely found in ants). I doubt that they would have addressed the question of a change in sex-biased dispersal at larger scale if they had not found this slightly higher female dispersal.
I would therefore advise the authors to clearly introduce the different forces that could shape the population genetic structure at large spatial scale without focusing only on the species dispersal abilities and to provide a more rational and precise expectation of which pattern of population genetic structure would be expected in the species studied.

2.d. A total of 443 individuals was sampled (Table 1) out of 93 colonies from 12 populations with most populations having less than 10 colonies sampled. In some way, this sampling does not allow to properly assess social organization since five workers is not enough to get precise estimate of within colony relatedness. Given that the aim was to conduct a population genetic study, it would have been more relevant, for the same sample size, to analyze more colonies with a single worker per colony.  Because a previous study shows that colony relatedness could be as high as 0.8, workers from the same colony cannot be considered as independent. The low number of colonies sampled by locality probably decreases the validity of the conclusions (see below in section 3).
Validity of the findings: The main conclusion of the paper, emphasized by the authors in the title (line 42-43), the abstract (line 42-43) and the discussion (line 289-291, line 296, line 303, 304), is that at the geographical scale analyzed (35 km2), dispersal is not limited and the population is panmictic across the entire study area. I do not doubt that dispersal should be quite important (as expected since both sexes are winged) but I questioned the fact that mating is panmictic at this scale. This is bit overstated for various reasons:

3.a. First, the effective sample size is quite low given that many workers can be considered as sort of pseudoreplicate as they belong to the same colony and thereby likely share part of their genes. Using only 8 microsatellite markers and such a small number of colonies within localities might not represent a sufficient sample size to properly test for deviation from panmixia.

3.b. Second, it is somewhat surprising to claim that there is panmixia whereas a low but significant genetic structuration was detected with the microsatellite markers (but given my above comment, it is difficult to be confident with these small sample sizes).

3.c. Last but not least, as already mentioned above, it is important to consider other factors than dispersal to explain the results. For instance, because the species leave in temporally instable habitats (line 124), recent colonization could also explain the lack of structuration and the absence of isolation by distance pattern (line 307-308) as populations might not be at migration/drift equilibrium.  Basically, the pattern of population genetic structure (whatever the genetic marker considered) does not only reflect present gene flow but also the demographic history of populations.
3.d. The discussion gives too much importance to this idea of panmictic population (line 289-291, line 296, line 303, 304, line 307-315, line 353).

I have few other comments on the analysis:

3.e. line 188 why using a linear regression model (lm) for testing isolation by distance? This might be a problem because pairs of localities (or pairs of colonies) are not statistically independent, a Mantel test (specifically testing association between two matrices) or Moran’s I spatial correlograms are usually preferred (see for instance Diniz-Filho et al 2013, Genet. Mol. Biol.), even though I reckon that these technics can also be discussed (see for instance see Guillot & Rousset 2013 Meth Ecol Evol). Anyway I do not think that this would change the results but the authors should argue their choice of using a classic linear regression model for testing the correlation between two matrices whereas it is not the most appropriate test.

3.f. Information on the landscape surrounding the localities sampled could be useful to better understand whether it is homogeneous and would support the fact that ants could indeed fly across it or whether there is some kind of heterogeneity. I do not ask for a landscape genetic approach as I do not think the sample size is large enough to conduct such analysis but it would be good for the reader to have information about it. May be it is just completely homogeneous and favorable to ants which would confirm that dispersal is not limited by the landscape in this area and be agreement with the results.

3.g. The software STRUCTURE might not be very good at finding population structure with few microsatellite loci and few individuals (see original paper by Pritchard et al 2000). In such situation, subtle population structure can sometimes be more easily detectable when geographic information is used. Given that nests were geolocalised, why the authors did not try to consider geographic information either directly in STRUCTURE or in other software just as GENELAND?

3.h. The authors reckon that the formula used to estimate sex-biased dispersal (line 215), based on the Wright’s infinite island model has been criticized. However, they still use it and mentioned in the discussion (line 317) that they “directly test for sex-biased dispersal” even though they again reckon in the following sentences that violations of the assumptions of the island model might biased the results in an unpredictable way. So I think it is quite dangerous and not very logical to use a formula known to be potentially wrong to draw conclusion on a female-biased gene flow.
Additional comments: In addition to the main comments made in the above sections, I have some minor comments:

4. Line 67 to 70: the recent review by Cronin et al. 2013 in Annual review of Entomology should be cited here.
5.Line 81- 82: this sentence needs to have references to support the statement that substructure at the level of a population is often observed.
6. Line 96-97: please reconsider the structure of the sentence. As such the meaning is not that clear. Do the authors mean that when both mode of colony foundation exist in the same species, few winged dispersal queens may be enough to allow efficient gene flow?
7. Table 1: If the level of Fis given in the table estimated on workers without considering the colony structure?
8. The authors should make clear in the M&M that only a single individual per nest was used for estimating genetic differentiation among localities (as written in the result section line 279). How was the individual sampled (at random, only once ?)?  Why showing both the Fst results on all individuals (line 243-244) and on a single individual per nest? Given that individuals from a given nest cannot be considered as independent, why not only presenting Fst based on the reduced sample?  This was quite confusing to me. Moreover, when using STRUCTURE, having too many related individuals could also pose a problem.
9. Concerning STRUCTURE: Did the independent runs for each K give consistent results (which would support the idea of an absence of structure)? Finally, Pritchard et al (2000) reckon that it can be difficult to obtain reliable estimates of Pr(X|K) so that just examining them might not be the best way of determining the most likely number of clusters in the data (as done by the authors line 197). Evanno et al (2005 Mole Ecol) proposed a method for choosing the best number of K. Why not having use it? I reckon that given the results (no population structure), deltaK would not be informative. Anyway, to be convincing the authors should provide at least a graph showing the mean and variance of the log likelihood of the different simulations for each value of K tested.
10. Line 331: it is not clear to me why female-biased dispersal may be common among ants? And I do not think that female-biased dispersal is assumed often for monogynous species? On which basis are done these assumptions? Do the authors have references to add here in order to support their statement?
11. In the supplementary file containing the genotypes, there are information in column AA, AB and AC  and after the last line of genotypes. Is it a mistake or does it mean something?
12. In the table S1: there is a mistake for C. cursor, independent should be replaced by dependent.


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: SCRAPING MARKING BEHAVIOUR OF THE LARGEST NEOTROPICAL FELIDS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript “Scraping marking behaviour of the largest Neotropical felids” is a welcome contribution to the better understanding of scrape-marking behaviour of jaguars and pumas. The document is well written, but the text should be entirely revised to improve its quality:
- standardization of the name of biomes (e.g. Atlantic Forest and Cerrado, always with capital letters - proper nouns);
- the word “Reserve” must be with capital letter when is part of the name of certain study area (the same applies to other words in proper nouns);
- standardization of study area names (e.g. the authors use Reserva Natural Serra das Almas and Serra das Almas Nature Reserve, but the correct is Serra das Almas Private Reserve of Natural Heritage);
- the correct name is Viruá (Viruá National Park) and not Virua;
- review the appropriate use of comma or semicolon;
- see other adjustments (e.g. jaguars are much more abundant “than” pumas).

The Figures 2 and 6 should be improved (standardization of information as described in the text - Figure 2; and improve resolution – both figures).

Some figures are not correctly associated with the text in which they were referenced (e.g. page 21, line 493). Review all.

The information in the Supplementary Material (tables) should be translated into English (some cells are in Spanish). Likewise, date of records needs to be adjusted.

The raw data regarding the scrapes associated with faeces or urine and that had the identification of the feline made by DNA should be duly indicated from the other data in the table (Supplementary Material).
Experimental design: See "Validity of the findings" for methodological issues.
Validity of the findings: Abstract - The authors cited “a total of 349 felid scrapes along 467 km of paths surveyed, obtaining a finding rate of 0.560 scrapes per km”. However, this rate is related to other values. Review the text and use the appropriate values.

Study areas - The authors cite five areas and list four locations. At this point, I suggest considering four locations. In addition, other study areas are cited in the item "Felid relative abundance and assigning scrapes to species and sex", but they should be presented together with the main sampling areas. This is reinforced because the complementary areas are also presented in Figure 2. The legend of Figure 2 also needs to be revised.

Surveying for scrapes - The types of path surveyed (car tracks, trails and cross country) should be presented in this item.

Felid relative abundance and assigning scrapes to species and sex – The authors inform they “cannot be sure about the faeces or urine found over scrapes necessarily had to come from the species and individuals who made the scrape”. This issue needs to be better addressed. Is there previous information (from the authors or references) on the habit of felines demarcating on marks left by other species or individuals?

Data analysis – (1) General analysis strategies should be presented in this item and not only in the results. (2) According the authors: “A site was defined as an area where one or more scrapes were found within a given distance. To determine this distance, we used the maximum distance we found (21 m) between scrapes in two intensive scrapping sites that we found in the Angatuba area”. Would that maximum distance be biased? Considering that there are peculiarities in the different areas studied and that the marking behaviour also varies between areas (see data of the authors themselves), the authors' proposal needs to be better justified. The same must be done for the other distances (lineal distribution of scrapes). What was the criterion for defining the distances? (3) Similarly, the authors must to better justify the width of 22 m to adapt the Ripley´s function.

Results – (1) The authors found “269 scrapes of felids, which meant a scraping rate of 0.560 scrapes per km surveyed”. Inform the sampling distance considered in the calculation of the rate (if they sampled 467 km, the rate is wrong - it should be 0.576). (2) Inform the degree of freedom in all the results of statistical tests. (3) The results of chi-square test for differences among study areas (distance of scrap sites) and the results of linear distribution of scrapes should be informed in the text (page 14, lines 323 to 331). In the first case, I suggest using paired analyzes to compare the study areas and the different distance categories. (4) The presentation of the data needs to be standardized (e.g. page 16: length/width ratios = “mean ratio of outsiders = 2.74 ± 0.90, n = 13”, and the average = “1.26; n = 201, se = 0.04”).

Discussion – (1) According the authors, they “cannot discard that some of the smaller scrapes found in this study come from ocelots since in some occasion we have observed ocelot scrapes after tracking them in sandy soils”. The scraping marking behaviour by ocelots needs to be better addressed. Is there information on the size of ocelots’ scrapes? (2) Authors interpret that the “selection on microsite scale seemed to be conditioned by the type of substrate rather than to facilitating signal detection”. However, the avoidance of sites with grass and stones, or with rocky substrate (less “mouldable” than sand or clay soil) indicates to me the selection of microsites that facilitate the detection and maintains the marking for longer. The authors themselves consider that “stones might make scraping more difficult and less detectable”. Review these issues. (3) Author cited that “in Cockscomb jaguars seem to be much more abundant than pumas (ratio jaguar/puma faeces was 11.3), whereas in El Edén was just slightly higher for jaguars (ratio= 1.6)”. Are there population abundance estimates for these areas? Can the scrap marking rate be used as a direct indicator of abundance? Justify.

Conclusion - Add that the jaguar scrapes were also single scrapes (not only long scrapes).
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: SCRAPING MARKING BEHAVIOUR OF THE LARGEST NEOTROPICAL FELIDS
Review round: 1
Reviewer: 2

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

This contribution increases the knowledge about scrapping behavior of the biggest Neotropical felids, the jaguar (Panthera onca) and the puma (Puma concolor). The emphasis is on the comparison of scrapes characteristics and scrapping behavior of both pumas and jaguars in areas differing in the density of these species, and areas where only pumas were present. The working hypothesis of the manuscript is that both felids use scrapes for marking proposals, as well as to communicate with other individuals, and to signalize particular points or areas of interest.
I liked reading the manuscript, and enjoyed the figures of scraps and the video of the puma scrapping. I have little concerns and suggestions, and I indicate them in the list below:

Methods
1) Surveying for scrapes
#130-#134: The surveys were conducted between five days and two months, but it is not clear to me if the same path was surveyed once or twice or more times in one period (except for Serra das Almas). Could you give some details?
2) Selection of scrapping sites
#175: Why did you chose 5m as the distance between the 1x1m plot where the scrap is located and a 1x1 plot on the same path to test for selection of microsites? What did you rely on when selecting that distance (5m)? Could you briefly explain it?

Results
3) Field samplings and finding rate
#236:  you say you “…surveyed 467 km of paths once or more times……” and found a total of 349 scrapes. Later in #238, you wrote that you find 269 scrapes. In Table 1 overall kilometers surveyed are 467 and total number of scrapes found in the five study areas 269. So, could you explain this disparity?
Also #237 and #238: I find this sentence a little confusing in terms on the duration of the sampling periods and as I wrote above in “1) Surveying for scrapes”, it is not clear how many times the different paths were surveyed.
4) Position of scrapes in paths
#254: here you mention a total of 318 scraps including those far away from path from Angatuba. But the number is different from the total presented above (n = 349).
5) Re-marking rate and linear distribution of scrapes on paths
# 282: here is clear that you removed the 2 scrapes from San Ignacio from analysis (it is only a comment).
6) Size of scrapes
# 331 and #332: I think you mean that the length/width ratio of scrapes is more similar between Angatuba and Cockscomb than among these last sites and El Edén.

Discussion
7) Site selection for scrapping
# 391 to #394. Why do you think felids avoid abandoned paths for scrapping (or prefer not abandoned ones)? And in Cockscomb, why do you think felids prefer the more frequently used paths for scrapping? could you say something about this?
# 394: The last sentence is confusing: “ …so animals may be use to people using the path during daylight, when…” and need to be rewritten

Figures
Figure 2: you may also include the total number of scrapes found in each study area as a number in the figures. Please replace Belize by Cockscomb in the figure.
Figure 3: please include “(ISA1 and ISA2)”  after “….intensive scrapping points…”in the text of the figure.
Figure 7: please, replace “….on linear paths for all data altogether and for every study area” by “…on linear paths for each study area and for overall data”

References

Check the entire section, there are a lot of references that are not cited in the text (e.g. #511, #524, #534, #582, #591, #595, #605, #611, #614, #622).

Best wishes,

Sonia Zapata


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: SCRAPING MARKING BEHAVIOUR OF THE LARGEST NEOTROPICAL FELIDS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript entitled is overall well written and brings interesting information to the audience of PeerJ and increases the knowledge of predators’ marking ecology.
The structure of the manuscript and background information seems appropriate, as well as the amount and quality of figures.
Overall, the manuscript has some minor points that can be improved or corrected.
Please, see below.
Experimental design: The sampling design an analysis seems appropriate although there might be some source of bias. The magnitude of this bias might be minor or not but it would be important that addressed in the discussion by the authors.
Validity of the findings: The authors present an important amount of data often rare to find on this topic.
Additional comments: ## Here is a list of minor comments ordered by lines, followed by general comments mostly.

Line 71 – According to bibliography list the citation to Harmsen et al. 2010 should be 2010a or 2010b. This is repeated later in text (e.g lines 73, 364)
Line 73 – Remove the semicolon after Harmsen et al.
Line 88 - Ordering the hypothesis by scale would be easier to understand and a rough measure of size would be welcomed.
Lina 99 - Reserva Natural Serra das Almas should be 5 (4 is repeated).
Line 208 - Probably want to use “linear” instead of “lineal”, here and in the following lines.
Line 119 – “Private” instead of “privative”
Line 213 – “belonging” instead of “bellowing”
Line 221 – I suggest to add “off” before “areas”
Line – I would not say similar in most occasions, actually are quite different in two-thirds of the sites (Cockstaomb and Serra Almas), I would rather say that differences were more pronounced in Car tracks
Line 295 – provide the tests results.
Line 361 - If by “north Mexico” you want to refer to San Ignacio site, please specify otherwise provide a citation.
Line 364 -  “Harmsen” instead of “Harnsem”
Map - Mention why San Ignacio is not displayed in more detail as the other sites. Explain the meaning of the different types of symbols. Use “Cockscomb” instead of “Belize”, as in text.
Bibliography:
Some of the species names are not in italics.
In the Baddley and Turner 2005 citation, the name of Turner was written and only put the initial for last name.
Many citations are not mentioned in the text, some are in the following list:
Schenkel R. 1947. Expression studies of wolves. Behaviour 1: 1-129.
Vila, C., Urios V. and Castroviejo J. 1994. Use of faeces for scent marking in Iberian wolves
(Canis lupus). Canadian Journal of Zoology 72: 374-377.
Sunquist M, Sunquist F. 2002. Wild Cats of the World. University of Chicago Press, Chicago,
USA.

Sillero‐Zubiri, C. and Macdonald D. W. 1998. Scent‐marking and territorial behaviour of Ethiopian wolves Canis simensis. Journal of Zoology 245: 351-361.
Kitchener, A. 1991. The natural history of the wild cats. The Natural history of mammals series.
Comstock Publishing Association, Ithaca, New York.
Kohn, M. H. and Wayne R. K. 1997. Facts from feces revisited. Trends in ecology &
evolution, 12: 223-227.
Menotti-Raymond M., David V. A., Lyons L. A., Schäffer A. A., Tomlin J. F., Hutton M. K.,
and O'Brien S. J.. 1999. A genetic linkage map of microsatellites in the domestic cat (Felis
catus). Genomics, 57: 9-23.
Molteno A. J., Sliwa A., and Richardson P. R. K. 1998. The role of scent marking in a free-
ranging, female black-footed cat (Felis nigripes). Journal of Zoology 245: 35-41.
Pal, S. K. 2003. Urine marking by free-ranging dogs (Canis familiaris) in relation to sex, season,
place and posture. Applied Animal Behaviour Science 80: 45-59.
Peters, G., and Hast M. H. 1994. Hyoid structure, laryngeal anatomy, and vocalization in felids
(Mammalia: Carnivora; Felidae). Zeitschrift für Säugetierkunde, 59: 87-104.
Pilgrim, K. L., McKelvey K. S., Riddle A. E., and Schwartz M. K. 2005. Felid sex identification
based on noninvasive genetic samples. Molecular Ecology Notes 5: 60-61

General comments:
In the discussion, you start talking about “who scrapes” and then discuss about scrape characteristics (disregarding species) and then in the last section you go back to differences between jaguar and puma. I would suggest merging the sections where you compare species, and using more order similar to results.
If you are acknowledging that jaguar and puma differ in their likely to leave a scrape, an estimation of abundance ratio based on droppings on scrapes is most likely biased based on your conclusions. Given that is not an important topic on the discussion I would not include relative abundance estimations on the manuscript. If you like to include it, a discussion on this possible bias would be an important addition.
In the part of the manuscript on felid species discriminated by sex, the sample size for pumas is smaller than jaguars this might explain why you do not detect any female puma, also the number of female scraping jaguars is very low. I would say that scraping in females is rare in both species; I think a more general conclusion will be more suitable for the data set.
Probably a scrape in the middle of the forest is less likely to find that one on a trail. Additionally, your sampling technique was to search for scrapes along trails and the scraping sites out of the trails were found following tracks, you did not perform searching in the forests either account for differential detection probability. Harmsen et al (2010b) found that jaguars are more willing to use forest matrix (instead trails) than pumas, this might be influencing the conclusion that pumas scrape more often than jaguars (is a possibility that there are lots of hard to find jaguar scrapes in the forest). Since you sampled on trails only, making the conclusion that pumas scrape more than jaguars relative to markings on trails might be more accurate coming from your data. Although most authors agreed that pumas scrape more that jaguars, quantitative data is rare, for that a discussion regarding the possible bias on scrape detection would be appreciated.


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: SCRAPING MARKING BEHAVIOUR OF THE LARGEST NEOTROPICAL FELIDS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript entitled is overall well written and brings interesting information to the audience of PeerJ and increases the knowledge of predators’ marking ecology.
The structure of the manuscript and background information seems appropriate, as well as the amount and quality of figures.
Overall, the authors adressed the minor concerns mentioned by revisors.
Experimental design: The sampling design an analysis seems appropriate although there might be some source of bias (mentioned in my previous revision).
 The magnitude of this bias might be minor or not but it would be important that addressed in the discussion by the authors and besides I already expressed my concern the authors do not acknowledge this possible source of bias that they are not accounting for.
Validity of the findings: The authors present an important amount of data often rare to find on this topic.
Additional comments: I think the changes in the new version of the manuscript covers all my previous concerns.


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

Input:
Title: TRANSCRIPTOMIC EVIDENCE FOR INVOLVEMENT OF REACTIVE OXYGEN SPECIES IN RHIZOCTONIA SOLANI AG1 IA SCLEROTIA MATURATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: 1 Line80:corn sheath slight should be corn sheath blight.
2 Please explain expression pattern and its correlation for DEGs in RWF9SI, RWF9S and RWF9M with sclerotia maturation in GO and KEGG.
3 Line240: this is the first time that a survey analysis on the transcriptome has
been done on the sclerotium forming process of maize sheath blight (R. solani AG1 IA). Kwon et al. (2014) studied the proteomic differences in the process of sclerotial formation of R. solani for 5 days, 7 days, and 10 days respectively and obtained 55 differentially expressed proteins, finding that there is high expression of processing, carbohydrate metabolism, cell defense, amino acid metabolism, and cellular processes in the process of sclerotia. Please compare your data to the proteomic data, analyze the differences. Actually the results seem inconsistent with the reported.
4 ROS tests, NOX1 (NADPH oxidases), SOD(superoxide dismutase) and CAT (catalase) activities should be added in three stages.
5 Line 206-209:the conclusion lacks basis.
6 The expression pattern in FIG5 B should be explained in detail.
7 The accession number of sequence data in NCBI should be offered online.


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: TRANSCRIPTOMIC EVIDENCE FOR INVOLVEMENT OF REACTIVE OXYGEN SPECIES IN RHIZOCTONIA SOLANI AG1 IA SCLEROTIA MATURATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: While it was an interesting topic, the entire manuscript was hard to understand because it was not written in Standard English. For the entire manuscript, improvements should be made in the use of language, spelling, and grammar.
Experimental design: While the research question has been stated, very little information has been provided in the methods section. The authors have to expand the Methods section. For instance, the authors did not explain how the RNA was isolated from the cultures. For the quantitative PCR, how did they do the reverse transcription? Did they do a DNase digestion to eliminate the gDNA? What was the reason for the selection of 18S rRNA as the reference gene? Did they normalize the gene expression using only one reference gene?
Validity of the findings: While the data is very promising, the authors have not sufficiently expanded on their findings. For instance, what are the top 20 genes under each category? What is the significance of these genes?
Additional comments: Comments for PeerJ 2325

In this manuscript, the authors report the involvement of reactive oxygen in sclerotia formation in Rhizoctonia solani AG1-IA by carrying out transcriptomic analysis. It is an interesting study since sclerotia is the infectious propagule of the non-spore forming Rhizoctonia spp. The authors examined the transcriptome of the sclerotia formed by R. solani AG-1-IA. While it was an interesting topic, the entire manuscript was hard to understand because it was not written in Standard English. For the entire manuscript, improvements should be made in the use of language, spelling, and grammar. In addition, the authors have to expand the Methods section. For instance, the authors did not explain how the RNA was isolated from the cultures. For the quantitative PCR, how did they do the reverse transcription? Did they do a DNase digestion to eliminate the gDNA? What was the reason for the selection of 18S rRNA as the reference gene? Did they normalize the gene expression using only one reference gene? What are the top 20 gene under each category?
Most of the comments have been made to improve the readability of the manuscript. They are as follows:
1.	Line 13: Change “soil borne” to “soil-borne”
2.	Line 33: “soil-borne Basidiomycete fungus family”. Although I understand what the authors wish to state, however taxonomically speaking, it belongs to the class Agaricomycetes, and family Ceratobasidiaceae. Since this is a scientific article, terminology should be appropriate and not informal.
3.	Line 37: Change “forlong” to “for long”
4.	Line 42: it is not clear what the authors mean by “its pathogenic populations”. Is there a non-pathogenic population of R. solani AG1-IA?
5.	Line 43: what do the authors mean by molecular genetic mechanism? Either the authors should use this phrase or the phrase “molecular basis of sclerotium formation”.
6.	Lines 44-46 is unclear. What are differentiated substrates?
7.	Line 90: How did the authors screen for the pathogenic strains. Did they inoculate the plants and re-isolate it?
8.	Line 94: Did the authors store the cultures at -80 °C or 80 °C?
9.	The authors did not explain how the RNA was isolated from the cultures. For the quantitative PCR, how did they do the reverse transcription? Did they do a DNase digestion to eliminate the gDNA?
10.	Lines 130-135. What was the reference genome used? Was it another strain of AG1-IA? The authors gave the link of the NCBI website Genome but did not indicate which genome they used for the annotation purposes.
11.	For the qPCR, why did the authors chose the 18S rRNA transcript for the normalization? Have the authors conducted a validation assay for each of the 12 genes? The authors need to establish that under the three conditions used for this study, the reference gene expression was also stable and appropriate. Furthermore, the problem with the 18S rRNA is the overabundance of the transcript. Did the authors dilute the sample in order to read fluorescence? If this happened, did this affect the fluorescence detection of the 12 genes of interest? Please refer to the paper by Kozera and Rapacz (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3825189/) as well as by Petriccione et al. (https://www.nature.com/articles/srep16961).
12.	Lines 167-168 are unclear. What do the authors mean by quality contamination?
13.	To improve readability, perhaps the authors can name the condition (mycelial, sclerotial initiation, or sclerotial) rather than call it by the name of the transcriptome. This refers to the Lines 185-229.
14.	Lines 206-209: It is unclear why the authors conclude that because of the greater expression of transcripts associated with cellular protein metabolic process, carbohydrate metabolic process, and so on, active oxygen is involved.
15.	Figure 5. The most interesting panel in the data set is perhaps sub cluster _6 (where genes are downregulated during formation of sclerotial initials and sclorotial formation) and sub cluster _8 (where genes are upregulated during formation of sclerotial initials and sclorotial formation). Perhaps, the authors can create a table and list the top 20 genes in each category?
16.	Lines 230-238: The correct term to use for reverse transcription quantitative PCR is RT-qPCR and not qRT-PCR. Please refer to the guidelines for the minimum information for publication of quantitative real-time PCR experiments (http://clinchem.aaccjnls.org/content/55/4/611.long).
17.	Line 254: Change “furthered” to “further”
18.	Line 258-259: the authors indicate that eight clusters depicting expression patterns showed that sclerotial formation related genes were significantly up regulated. This is not an accurate assessment. In the study, the authors state that they examined genes with a p<0.05. However, Figure 5 shows the log2 ratio of FC. What are the p values associated with the FC? Do they all have p<0.05?
19.	Line 263: Change “passway” to “pathway”
20.	Lines 267-268: What does “hyperoxidant statedriven prevention by cell aggregation mean?


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: TRANSCRIPTOMIC EVIDENCE FOR INVOLVEMENT OF REACTIVE OXYGEN SPECIES IN RHIZOCTONIA SOLANI AG1 IA SCLEROTIA MATURATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Some minor edits are noted:

1.Line28-29, Gene Ontology and Kyoto Encyclopedia of Genes and Genomes analyses are abbreviated to GO and KEGG. In this part, you have made differentially expressed genes (DEGs),NADPH oxidase 1 (NOX1) and superoxide dismutase (SOD).

2.Line34, ‘sclerotial initiation and sclerotial maturation’ could be changed to ‘sclerotial initiation and maturation’.

3.Line74, However, the molecular mechanisms of sclerotia formation in R. solani remain poorly understood? Make sure the grammar.

4.Line87, hypothesis that reactive oxygen species (ROS) should be changed to ROS. You have mentioned this already.

5.Line119, sclerotia initiation should be sclerotial initiation.


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: TRANSCRIPTOMIC EVIDENCE FOR INVOLVEMENT OF REACTIVE OXYGEN SPECIES IN RHIZOCTONIA SOLANI AG1 IA SCLEROTIA MATURATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: The study has been well reported. The authors have indicated that they used Rhizoctonia solani Rhs1AP as the reference genome in Lines 153-154. The authors need to cite the publication associated with the genome sequence which is as follows.

Citation: Cubeta MA, Thomas E, Dean RA, Jabaji S, Neate SM, Tavantzis S, Toda T, Vilgalys R, Bharathan N, Fedorova-Abrams N, Pakala SB, Pakala SM, Zafar N, Joardar V, Losada L, Nierman WC. 2014. Draft genome sequence of the plant-pathogenic soil fungus Rhizoctonia solani anastomosis group 3 strain Rhs1AP. Genome Announc. 2(5):e1072-14. doi:10.1128/genomeA.01072-14.
Experimental design: Research questions have been well defined, and methods have been well described with sufficient detail.
Validity of the findings: Data is robust and statistically sound.
Additional comments: All the comments to the authors made previously have been addressed. Overall, the study has been well designed, studied, and reported.


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: COMPARATIVE DEMOGRAPHY OF COMMERCIALLY-HARVESTED SNAPPERS AND AN EMPEROR FROM AMERICAN SAMOA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, I found this paper to be well-written, clear and interesting to read. The introduction was well structured to provide context, and both the introduction and discussion generally well referenced (though see one minor comment in General comments below).
The figures are relevant, and generally well captioned. The authors should, however, take care to ensure captions can be interpreted without referring back to the text (i.e. there should be no acronyms or abbreviations).
Raw data has been supplied in an easily interpretable form.
Experimental design: The paper generally uses well-established and repeated laboratory and analytical techniques. The research questions are generally well-defined and relevant to the management of these species in American Samoa. The paper falls within the editorial scope of PeerJ.

One concern I had with the experimental design is that the authors have not sufficiently explained how the sub-sample of each species used for life-history analysis was obtained from those collected for life-history analysis. For each species, there is a large discrepancy in the number of fish collected for life history analysis and that used for various ageing and reproductive (histological) analyses. For example, from the MS Excel data file provided there were 481 individual Lutjanus gibbus obtained for life history analysis, but only 157 were used for gonad histology and less than 50% (236) were aged. Similarly, of the 217 Lutjanus rufolineatus obtained for life history analysis, only 100 were used for gonad histology and only 134 were aged. I can appreciate that for gonad histology at least the intent was to examine female maturation profiles and thus there would be a discrepancy resulting from the exclusion of male fish, however there appear to be large numbers of females excluded as well. The authors make no statement of how or why the sub-sample obtained for life history analysis was further sub-sampled (although they do caution the validity of their findings given low sample sizes for maturation in L. rufolineatus). I found this a little misleading as I was at first quite impressed with sample sizes used in the study, and would thus like to see clarification from the authors.
Validity of the findings: Aside from those points raised above, I found the data to be generally robust and statistically sound. Conclusions are generally well stated and limited to supporting results (through see general comments below).
Additional comments: General comments
Line 18: what is the difference between life-history biology and reproductive biology? To me, reproductive biology is a component of life history, thus its inclusion in this opening sentence seems somewhat redundant.

Lines 31-32: suggest adding ‘female’ here (i.e. low proportions of immature female…’, as male maturity was not assessed.

Line 80: Reference for Commercial Fisheries Biosampling Program, 2018, is not included in reference list. Perhaps this should be Sundberg et al. 2015?

Line 208: Sample sizes stated here seem incorrect, as least compare to the raw data file. According to the raw data file, there were 372 Lethrinus xanthochilus, 481 Lutjanus gibbus, and 217 L. rufolineatus obtained for life history analysis?

Lines 290-286: I found the inclusion of information on schooling behaviour of each species in this section a little misleading, as the sentence that leads up to this sets the reader up for a summary of ‘the information presented in this study’. This study did not explore schooling behaviour, and I suggest the statements on schooling be referenced or, better yet, omitted.


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: COMPARATIVE DEMOGRAPHY OF COMMERCIALLY-HARVESTED SNAPPERS AND AN EMPEROR FROM AMERICAN SAMOA
Review round: 1
Reviewer: 2

Output:
Basic reporting: a.	Clear and unambiguous, professional English used throughout.

•	The writing is clear and professional.
•	This is a very minor point and stylistic, but there are some instances where I questioned the word choice. I refer specifically to the use of ‘adequately’ (Line 250) and ‘tenuously suggest’ (Line 331), both instances have the connotation that they are pre-addressing reviewer concerns, but I question why this sub-text is necessary.

b.	Literature references, sufficient field background/context provided.

•	Missing reference Line 104-106, CFBP Report?
•	Line 129: Any daily ring validation in similar species?
•	Line 131: I would include a standard citation here on this technique.

c.	Professional article structure, figs, tables. Raw data shared.

•	Fig 2A: possible for temperature to be in light blue color or darker gray for ease of reading? Not distinctive from species lines/patterns and vision-impaired readers might have trouble even distinguishing the lines from the background color.
•	Figure 3A and C: The female line is hard to see, possible to switch the pattern of male and female or overlay the lines on top of the points?
•	I can understand the justification for including the gonad images (S1 and S2) in the Supplemental materials as they are not of ‘primary importance’ to your results. However, I would argue that they are relevant to your discussion, and therefore should be placed within the main part of the manuscript as SI often is overlooked. I have not found in the peer reviewer guidelines or the author instructions limitations on the figure/table numbers that would preclude you incorporating them in the main body of the manuscript. Further, they are of decent image quality and add to the Discussion.

•	Raw data is included in Supplementary data

d.	Self-contained with relevant results to hypotheses.

The authors have contained their findings to the hypotheses.
Experimental design: a.	Original primary research within Aims and Scope of the journal.

This primary research falls within the Aims and Scope of PeerJ.

b.	Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap.

While this research might be described as basic demographic research, the authors have presented an interesting comparison among the three species in a way that is meaningful for multispecies fisheries management.

c.	Rigorous investigation performed to a high technical & ethical standard.

Study was performed to a high technical and ethical standard typical of fisheries-dependent studies. There is a statement of animal ethics approval.

d.	Methods described with sufficient detail & information to replicate.

Methods were detailed and easy to follow.
Validity of the findings: a.	Impact and novelty not assessed. Negative/inconclusive results accepted. Meaningful replication encouraged where rationale & benefit to literature is clearly stated.

The authors argue their findings persuasively, but have acknowledged where there is need for greater replication or weaker results. Examples of this are easy to find in the manuscript:

Line 251: the authors anticipated that this was weaker result, but they have specifically stated that it should be interpreted with caution.
Line 331: “Our results tenuously suggest… small sample size…etc”

b.	Data is robust, statistically sound, & controlled.

The authors have provided data and methods are mostly standard for the field.

c.	Conclusion are well stated, linked to original research question & limited to supporting results.

Yes

d.	Speculation is welcome, but should be identified as such.

Some ‘speculation’ feels inadequately discussed. For example, Line 288 “responses…will differ among the three species”. I wish the authors would have expanded more on that thought or written more clearly their intention – at present it reads as incomplete and perhaps intentionally vague.
Additional comments: This manuscript is clear, the results and methods are sound, and data are elegantly presented. Demographic information like age and growth information is of utmost importance for fisheries management. The authors have written a compelling argument for contrasting life-history patterns among lutjanid/lethrinids, provided detailed methods and raw data, clearly stated where their results should be interpreted with caution, and discussed some interesting aspects of reproductive ecology. I see no reason why this research should not be published 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: COMPARATIVE DEMOGRAPHY OF COMMERCIALLY-HARVESTED SNAPPERS AND AN EMPEROR FROM AMERICAN SAMOA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is well written and thoughtfully organized.  There is enough background information and relevant citations.  For the most part the tables and figures are well done, I have a couple of issues will I will address below.  In the raw data I would have liked to see the agees for all three ageing attempts and not just a final age.  I will have more to say about that in another section.  Overall it was a very enlightening paper and adds a lot of new information to the existing literature.
Experimental design: The research question is well defined and the methods used to answer the questions were appropriate.  I have a few comments, first was there more than one person who aged the fish?  Did one person age teh fish 3 times?  Either way, I would have loved to see each persons age for each fish.  In any ageing study, precision estimates are very helpful indeterminate inf the structure being used to age is the appropriate one.  I also didn't see how the authors came up with the equations for the relationship between sagittal otolith weight and annual age.  in the results it was state that "Otolith weight was a strong predictor for age in all species, whereby the relationships were best explained using a standard quadratic equations fig.3"  I would have liked to see how you came up with those numbers.  Also, Otolith weight and fish length could also be strongly correlated, I am not questioning the results, I would just suggest explaining how you came up with the specific equations.
Validity of the findings: For the most part the findings and conclusions are supported by the data.  The correct statistics and procedures were used to reach the conclusions.  There is a lot of new information that will greatly add to the literature about the biology of these three species.  However, some of the statements in the discussion and conclusions about the impact to the fishery need to be addressed.  On line 290:  All three species were found to have low fishing mortality rates ...." This is the first time fishing mortality was brought up.  The statement is disingenuous, there is nothing in the manuscript that supports that statement.
Lines "301 - 303 Nevertheless, this preliminary information on mortality ratios and catch distribution relative to maturation size implies that these species are not approaching overexploitation in American Samoa"   Once again, there is no talk about exploitation in a fishery anywhere in the manuscript. Other than a section in the introduction Line 82: that talks about "the status of many reef associate populations is poorly understood"  This paper helps to address some of the data gaps to better understand the biology and some of the fishery characteristics, however until an assessment is conducted using the new information, the statements about exploitation and fishing mortality are a bit premature.   Also in the conclusions, Line 369: "...associated recovery potential...,"  I didn't see anything in the manuscript that supports that statement.
Finally, in the introduction line 89: ..based on validated age estimates..were you trying to used the edge analysis to try to validate the ageing method, or that confirming that the annuls was formed once per year?   I have a few specific comments about that below.   Because you didn't address that in the discussion, I would alter the statement and not use the phrase "validated age", at most the results suggest a consensus age, which is something that would be really good to see in the raw data.
Additional comments: Overall, it was a very good manuscript.  I have a couple of minor comments here.first: line 116:  "...one sagittal otolith from each species was selected at random.."  Why was that?  most age and growth studies pick the one for consistency.  line 214:  Annual patterns of edge deposition clearly demonstrate... Figure 2A is very busy, it isn't clear at all. everything is overlaid and I had to expand the graph a lot to see what was going on.  I would have figure 2a as a stand alone figure, I would also suggest a table with average edged deposition values per month, mainly because you don't have samples for all 12 months.  Finally, line 425 & 427, is it RE or RL, Johannes?