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 SPANISH VERSION OF THE FATIGUE ASSESSMENT SCALE: RELIABILITY AND VALIDITY ASSESSMENT IN POSTPARTUM WOMEN
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper “The Spanish version of the Fatigue Assessment Scale: Reliability and validity assessment in postpartum women (#17227)” presents the cultural validation and initial psychometric properties of the FAS in postpartum women. The structure of the paper is adequate, contents are properly arranged in their sections, comments are not mixed with results, the discussion is well supported by the reported results, the methodology used is ade4quate for the aim of the study and the sample used has enough size.
The paper is written in a way easy to understand although some English editing would be welcome. Some of the terms and expressions difficult to understand are pointed out bellow.
Experimental design: The design is adequate for the aims of the study although some data analysis should be improved.
Validity of the findings: The validity of results is supported by the large sample used. Methods are adequate, but perhaps incomplete, and regular procedures for questionnaire cultural adaptation have been followed. Sensitivity to change is still to be tested.
Additional comments: To main issues are to be distinguished in the paper. One is the cultural adaptation into Spanish of the original FAS, the other is the existing differences in structure between versions.
As for the first part, the paper is straightforward and results are really worth, specially taking into account the large sample used in the validation process. These findings are very useful in usual clinical practice and it is interesting to have a Spanish version of the instrument. Perhaps it would be interesting to have some additional data about the normative values obtained with this the sample, such as percentiles, in order to make it easier to know the meaning of the fatigue value obtained by a patient.
As for the second part, there is nothing wrong in finding that the structure of an instrument might be different in other cultures. Nevertheless, I personally feel that the approach followed by the researchers is incomplete, but easy to work out. Reading the two items giving some trouble, they do remind other items used to measure anxiety and depression (like in the HADS scale). It is not easy to select proper items for a scale and the researchers are not the ones to be blamed for it. But some other methodological strategies are available to ensure that this two items are rather “noisy” different from the ones used by the authors.
First. Estimated factor loadings are rather mild for a uni-dimensional scale. It could be the case that the authors have not considered the ordinal nature of Likert response scales and that the estimations method is not really the best one. I would recommend using MPlus defining ordinal metric for itmes and a better estimation method such as MLMV or WLSMV. Lisrel using the polychoric correlation matrix could also give good results. It would be interesting to mention in the paper the structure obtained by the original authors in English to compare.
Second. The extraction method used in the exploratory factor analysis should be reported, and the obtained structure matrix to (even if the graph of rotated factor loadings is reported). Furthermore, it is not a good idea to use a Varimax (orthogonal) rotation when you are expecting items to be load in a single dimension. An oblique rotation would be more suitable, and the correlation between factors will give a hint on the real proximity of items in the rotated structure. The authors should keep in mind that they are not willing to improve the scale and hence they should not discard any item. At most, they should find better versions of the original items (¡and repeat the data gathering!).
Third. The varimax solution will not give you the proper picture of the differential functioning of the two conflictive items. It is known that bi-polar dimensions (with a positive and negative end, and with items located at each one of the ends) tend to be treated as separated or independent dimensions by the rotation algorithms. The problem here is that the rotation procedure is not able to distinguish dimensions at 180º from those at 90º. This is a known analytical artifact, which should be thoroughly checked.
Fourth. Given that the authors think that the negative wording of the offending items could be introducing a methodological bias they could use more sophisticated structures to test if this is so. For instance, setting free the correlation between error terms for items 4 and 10 (theta-10-4) would estimate the amount of relation of this two items due to wording, and subtract it from their relation with the underlying latent dimension. Other procedures as a bi-factor structure, a multy-trait multi-method, or a second order factor structure will also help understanding the structure and assessing the response bias due to negative wording.
Fifth. The authors could always cross-validate the results splitting their sample and comparing both subsamples.

From the results obtained (Line 225) It looks like there is not a big departure from the normal distribution (z=2.46) for the size of the sample used (n>850). If the authors are willing to compare mean values, they could safely use the t-test, since the distribution of possible sample mean values will be normal with such group sizes (no matter if the distribution of scores are not). Furthermore, it is more interesting to adjust for unequal group variabilities (when selecting the proper degrees of freedom for the t-test) than to prevent for deviations from normality (using the Man-Whitney U test). Z scores have the benefit that they give a feeling of the effect size for differences between groups, something much more difficult to do using the U.

Some other minor comment follow.
Line 58. The way the sentence is written makes you think that the fact that it is sort will make it more discriminant, or will give better psychometric properties. Please separate concepts.
Line 58. Consider changing the expression “since it is brief, does” to “since it is brief, it does”.
Line 62. Consider using “1=Never to 5=Always”.
Line 63. Please modify the sentence. Only two items 4 and 10 are worded in a negative way, the other eight are positively worded but they ask for negative aspects or negative impacts on health i.e.: deterioration.
Line 65. I suspect that the scores given to items 4 and 10 are not “negative scores” but rather “reverted” scores. See also Line 141.
Lines 69. “reliability indices”. Only one reliability coefficient is reported. It should be singular.
Line 105. Use “maintain”.
Lines 109-110. The team ensuring semantic equivalence should have been the original English authors and not the developing team.
Line 111. ¿How many interviews where carried out?
Line 132: Use “and” for “ant”.
Line 168. The name of local institutions is never translated. Although you may offer a translation in brackets.
Line 182. How many cognitive interviews were carried out?
It is customary to report a dispersion statistic (e.g.: standard deviation, interquartile range, etc.) accompanying the mean when average values are reported. See lines 176, 183 & 193.
Line 195, 216. When particular figures and tables are addresses in the text, they should be mentioned in capital letters, i.e.: “Table 3”.
Lines 199, 201, 259, 270. Please use the term “Goodness-of-fit statistics” or “Goodness-of-fit indices”, instead of “Indices of fit”, which is the standard for this kind of indices.  Otherwise, use “fit indexes”.
Consider rephrasing Line 199: “Goodness-of-fit statistics for the single dimension model containing all items (Model 1) were good.”
Page 202. It is more frequent to use “factor loading” instead of “factor weight”, although it is not strictly incorrect.
Line 208, please use chi-square (or 2) instead of c2. Furthermore, report the degrees of freedom after the chi-square value and using an equal sign: chi-square=2242.8, df=45, p<0.01.
Line 229, 230. Use “FAS-e score” instead of “Score FAS-e”.
Line 231. Use an equal sign between Spearman Rho and the reported value.
Line 240. “owing to variance in method”. Consider using “due to a methodological bias”.
Line 254. Consider using “no evidences have been provided” instead of “have data been provided”.
Line 257. Consider using “support” for “attest to”.
Line 265: it is difficult what the authors mean by “without leaving the common dimension”.
Line 266. “problem of method variance”. Consider using “problem of variability due to method” or “variability due to method bias”. And modify Line 279 accordingly.
Line 278: consider using “increase” instead of “exceed”.
Line 281: Please review the following wording: “a sample of mothers to children aged 0 to 5 years old”.
Line 290: I am not sure what the authors mean when using “diminish”. Perhaps they are intending to mean “discard”, but they should note that the kind of design they are using is not prospective and hence they may not infer if the FAS scoring (after birth) has any screening properties on self-efficacy (as related to vaginal delivery).

Table 3. It should be mentioned that items 4 and 10 have been reverted before carrying all computations. Otherwise some results, such as the item-total correlation or the sign of the factor loading are difficult to understand.
Table 3. Review translation for item 1.
Table 3. Items should be numbered to make it easier the reference.


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 SPANISH VERSION OF THE FATIGUE ASSESSMENT SCALE: RELIABILITY AND VALIDITY ASSESSMENT IN POSTPARTUM WOMEN
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors have succsesfully reviewed and modified the draft accordint to  comments and suggestions made in previpous review. Paper may  be accepted now.
No more comments to add
Experimental design: No more comments to add
Validity of the findings: No more comments to add
Additional comments: No more comments to add


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 SPANISH VERSION OF THE FATIGUE ASSESSMENT SCALE: RELIABILITY AND VALIDITY ASSESSMENT IN POSTPARTUM WOMEN
Review round: 2
Reviewer: 2

Output:
Basic reporting: The new version of the original paper “The Spanish version of the Fatigue Assessment Scale: Reliability and validity assessment in postpartum women (#17227)” has improved noticeably and the answers given by the authors to the reviewer suggestions are sound and clear. I would like to congratulate the authors for their efforts in improving their work.

I would like to pose one minor suggestion. The term “group factor” is used to distinguish the content specific dimensions in the bi-factor solution from the overall factor/dimension (the later including all items). See lines 142, 229, 230, 239, etc. Although changing “group” by “grouping” could make it easier to understand the text it is usual, in the existing literature, to refer to such factors as “specific” factors as opposed to the “general” overall dimension (see Muthen & Muthen, 2010; Morin, Arens & Marsh, 2000; Reise, 2015). I would suggest using “specific” instead of “group”, especially when two samples have been used in the study, and it may induce readers to think about a multi-group cross-validation analysis using both samples. Please also correct it in Table 3 footnotes.

Line 153 and footnote in Table 2. Use “goodness of fit index (CFI)” instead of “goodness fit index (CFI)”

Line 185 and table 1. Use a dot as decimal placeholder instead of a comma.

Line 213. Use “error terms” instead of “residues”. Avoid using “residuals”, since residuals in SEM models refer to the reproduced covariance matrix based on the model parameter estimates.
Experimental design: No commnent
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: THE SPANISH VERSION OF THE FATIGUE ASSESSMENT SCALE: RELIABILITY AND VALIDITY ASSESSMENT IN POSTPARTUM WOMEN
Review round: 3
Reviewer: 1

Output:
Basic reporting: No comment
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: ESTIMATING THE AGE OF HELICONIUS BUTTERFLIES FROM CALIBRATED PHOTOGRAPHS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article entitled “Estimating the age of Heliconius butterflies from calibrated photographs”, by Dell’Aglio and colleagues, investigates whether the hue variation in the forewing dorsal red band of a Heliconius butterfly species is associated with age. The authors shot digital photos from several wings dissected from vouchers with known biological ages, calibrated the images to avoid bias related to light conditions and scale loss, projected the images on color space, and extracted information of the red-green opponency to use as data in the analyses. The results indicate that redness of red band and butterfly age are negatively correlated, suggesting that a red fading in the wings of Heliconius melpome butterflies is expected when adults get older.

In general, the article is well written and have good quality data. The manuscript has a good discussion regarding the ecological and evolutionary implications of wing color changing in butterflies, and speculate about some studies that could be done in the future using the method presented in the paper, what I consider an inspiration for the scientific community. I really believe the method presented here represents an advance in the field.

I do not have many criticisms regarding the paper. The only two concerns I have are: (1) why have been stated that categorical data was used in the analysis if only qualitative data has been used, and (2) why authors make the statement that analysis was based in human visual perception if all data came from a machine assisted visual perception?
Experimental design: The experimental design is majorly ok, but the issues regarding (1) categorical vs. quantitative data analysis and (2) human vs. machine vision need further revision.

IIn page 4 (lines 83-84), authors made the following statement: “we used an analysis based on human visual perception of wing colour to investigate the correlation with the age”. When I read that, I thought there would be an analysis based on human subjective categorization of red fading (see in figure 1), but to my surprise all analyses were done using quantitative data obtained from computer processed images. In the Material and Methods section, authors have justified why they consider that human perception had been used, but the truth is that "naked human eye" has not been used to identify the association between "redness" and age. Instead, machine processed photos, shot under standard conditions and with no noise produced by scale loss, were examined. Although all imagens had been taken under standard white light and processed considering only visible light spectrum, using RGB channels, which we humans can see, no human eye is capable of precisely identify a hue value of redness and at the same time exclude information from scale loss. Thus, the way I see, at least we should consider that a “machine assisted vision” was used. In addition, I did not find any analysis concerning the three categories of red (crimson, red, fade red) as described in lines 90-97. The only reference to the subjective age/red categories is made on figure 2, where authors discriminate the red categories of all wings measured using a*value in the same plot. Even so, all data used in the statistics and discussed in the results section came only from quantitative data (a* values).

I think authors should consider that "real" human vision have not been used to identify the redness on the set of wings analyzed. Plus, I also recommend the authors to rethink about the necessity of include any reference to categorical data in the manuscript, since it not a major concern to answer the main question of the study (Is red fading of the wings associated with butterfly aging?). If authors choose to keep the references to the three classical age categories defined in the early 70's, I think it is needed to include another analysis comparing naked human eye efficiency in the identification of age classes using photos that have not been processed (scale loss edition).
Validity of the findings: The manuscript have good quality data, and unequivocally indicates that red fading in the wings of Heliconius melpomene is associated with aging of adults. The issues regarding human vs. machine vision, and categorical vs. quantitative data do not affect the validity of the findings. Although similar results are expected in other species of Heliconius, the results presented here refer only to one species of the genus. Perhaps should be important to make this clear in the title of the manuscript.
Additional comments: Although not discussed in the article, the results presented also raises important questions regarding the reliability of using only naked human eye and subjective categories based on color fading to identify the age of a butterfly. Figure 2 is very clear in showing that subjective red categories as a proxy for butterfly age are not good at all, since there is a massive overlap among categories. I think this issue could be included in the discussion (although not mandatory).


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: ESTIMATING THE AGE OF HELICONIUS BUTTERFLIES FROM CALIBRATED PHOTOGRAPHS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This study investigates whether the colour variation in the red ban exhibited by the butterfly Heliconius melpomene rosina is related to age. For this purpose the authors used digital photography and calibrated colour images of 55 individuals of this species whose age was known. The authors found a strong correlation between hue and age, according to human visual perception, so that younger individuals display a more intense red band (crimson) whereas older individuals present a faded red. The interpretation of these results is framed within literature on age-related colour fading, mate choice and possible relation with predator avoidance.

The figures are relevant for the paper, and the one related to the results is self-explanatory. The references cited are appropriate for the topic of the study. The paper is well written in general, although I have some suggestions for improvement.
Experimental design: I appreciate the information provided, considering that many of these assumptions (i.e. ‘redness’ is related to age) spread despite not having been tested. However, I think that the justification of your study needs to be reformulated. You say “Given the importance of red patterns in mate choice, we here investigated the influence of butterfly age on red colouration. We used an analysis based on human visual perception…”. If the rationale for your study is related to mate choice and, for example, whether or not age (through “redness”) could influence mate choice, using human visual perception is a strange choice. According to L164., vision has been studied in related species, so data should be available to give “butterfly values” to the differences in redness among individuals, according to your calibrated images. With the current knowledge on avian visual models, you could also check whether birds (potential predators) detect that variation in “redness”. However, with your choice of human perception these questions cannot be addressed. Thus, you need to re-formulate the justification of the study, placing more emphasis, for example, on why it would be useful for researchers to have a phenotypic indication of age. This would also make more ‘acceptable’ to include speculation in the discussion section, and would be a first step, as you imply, to address the relationship between colouration and age.

L114: The line about the statistical analysis is confusing. You state that you checked for a correlation between two variables using a linear regression, and then report a ‘c’ value in line 126… is this ‘r’ (from a correlation analysis)? A regression analysis is used when you want to predict a Y-value for a varying X-value, usually which is controlled by the researcher. I agree with your statement saying: “to test for a correlation….”, as this is what you can do to see to what extent, if at all, age and ‘redness’ are related. Also, you need to mention whether you did a parametric (Pearson) or a non-parametric (Spearman) correlation? Finally, you report no differences in colour between males and females with a t-test (L124). I would suggest you use a one-way ANOVA instead (I am assuming your colour data are normally distributed)?

L125-127: Probably the most important line in your paper, yet not clear in terms of the statistical approach. Is ‘c’ the correlation coefficient or an r2? If the former, that means you did a correlation analysis (which is, in my opinion, the right thing to do) rather than a linear regression. Much more accuracy about what you did is needed in the results section, even if I can see from the figure what the results are.
Validity of the findings: RESULTS ---> L125-127: Probably the most important line in your paper, yet not clear in terms of the statistical approach. Is ‘c’ the correlation coefficient or an r2? If the former, that means you did a correlation analysis (which is, in my opinion, the right thing to do) rather than a linear regression. Much more accuracy about what you did is needed in the results section, even if I can see from the figure what the results are.
Additional comments: See below a list of more specific comments.

L50: Please add references to support this statement!

L51: change ‘particular’ to ‘particularly’; add an ‘s’ at the end of ‘exhibit’, as here you are treating Heliconius as a genus (i.e., single)

L52: replace “that they are toxic” with “of toxicity”; also, insert a comma (,) after the brackets

L53: something is wrong here, I think? Do you mean “and find and choose mates based on the same colour signals that are involved in predator deterrence”? If I understand correctly, you want to say that the same colour signals are used to attract mates and repel predators… Right?

L58: ‘Melinaea’ should not start with capital letters

L62-63: change “for variation in colour” to “of colour variation”

L64: change ‘are’ to ‘is’, as you are referring to ‘gene expression’ (singular)

L73: insert a comma (,) after ‘genetically’

L78: … and predator avoidance(?)

L80: delete ‘the’ at the end of this line

L79-83. Consider splitting this line in two

L93: replace ‘captured’ with ‘taken’

L146: add ‘in’ before ‘which’

L162: remove the ‘s’ at the end of ‘shifts’

L163: add a comma (,) after sensitivity and replace ‘and allows’ with ‘allowing’


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: ESTIMATING THE AGE OF HELICONIUS BUTTERFLIES FROM CALIBRATED PHOTOGRAPHS
Review round: 1
Reviewer: 3

Output:
Basic reporting: see the 'General comments for the author' below
Experimental design: see the 'General comments for the author' below
Validity of the findings: see the 'General comments for the author' below
Additional comments: The work reported here investigates whether the hue variation in the forewing dorsal red band corresponds to the age of the butterflies. Tested with 55 digital wing images, it is claimed that red colour can be used as indicator for age based on the strong (negative) correlation between age and a* values. As evident in Fig 2., all Crimson wings were <10 days and faded reds were about 30+ days old. So these two subjective colour labels could only put estimated age in these bands. The labelling of ‘red’ seems to cover a wide range (from 1-40 days) and hence not at all useful for age prediction.

On the other hand, a* values showed stronger correlation with age but this was not thoroughly investigated. Is this correlation value due to the distribution of the limited data in two fairly distinct clusters? There are very few samples in the age range 12<age<30. Hence the regression line is unlikely to be a good predictor of age. This could easily be tested  by setting aside a subset of samples (as test set) from the regression analysis and the regression line obtained from the remaining data be then used to predict the age of the test set samples. Not being a bio-scientist/ecologist myself, I am not sure what sort of precision is generally expected or necessary in such age prediction exercise. But my personal feeling is that the proposed approach is not adequate in ‘estimating the age’ precisely enough. [I was curious to know if the two wings of the butterflies demonstrated similar colour values since they are the same age]. The authors may explore other colour representations as the discriminatory feature and preferably use a much larger data set to see if better age estimation is possible. Alternatively, if a rough estimation is good enough, this should be explicitly stated and then demonstrated how accurate are the age estimations under this definition.

The paper is generally well structured, language easy to read. Some (very few) typos still managed to get in which can easily be fixed.


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: ESTIMATING THE AGE OF HELICONIUS BUTTERFLIES FROM CALIBRATED PHOTOGRAPHS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am happy with how the authors have addressed my comments from a previous version.
Experimental design: The authors have done the suggested changes to the manuscript in order to make their aims clear.
Validity of the findings: Ok
Additional comments: Thanks for having carefully addressed my previous comments. I have nothing left to add.


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: IDENTIFICATION OF REFERENCE GENES IN BLOOD BEFORE AND AFTER ENTERING THE PLATEAU FOR SYBR GREEN RT-QPCR STUDIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: ─	With respect to the volunteers the clinical and experimental information should be expanded and some basic characteristics should be provided, e.g. age, sex, time spend in the plain before moving and time spent on the plateau before blood was drawn. Did any of the six volunteers they show clinical signs of hypoxia at the time of examination?
─	There are some minor typos that should be corrected, e.g. line 86 “qRCR RT kit”, line 129 “quantitative quantification method”.
Experimental design: ─	The limited number of volunteers the experiments are performed on should be discussed critically.
Validity of the findings: ─	Please report the number of replicates the measurements of the different housekeeping genes was performed on.
─	What do the authors think is the reason that these housekeepers reliability is different depending on the evaluated altitude?
Additional comments: In the presented study, the authors assessed the stability of eight different human housekeeping genes in standard SYBR Green RT-qPCR under normoxic and hypoxic conditions. Different algorithms (geNorm, NormFinder, BestKeeper and RefFinder) to evaluate the stability were applied. In their study, they identified RPL13A as most reliable housekeeping gene for evaluation of gene expression in normoxic and hypoxic conditions.


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: IDENTIFICATION OF REFERENCE GENES IN BLOOD BEFORE AND AFTER ENTERING THE PLATEAU FOR SYBR GREEN RT-QPCR STUDIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: English proficiency requires improvement throughout the paper.
Examples:
-line 44: In the abstract: "Interestingly, RPL13A was selected as the
ideal reference gene to normalize the target gene expression in human blood before and
after moving to the plateau." I suggest changing the selected to identified, or found ...
- line 52: What do you mean by "Hypoxia is a major geographic feature of high-altitude regions", the word geographic does not fit here, may replace with biological?
- line 53: the following sentence is not clear: "In hypoxic environment, specific genetic programs and molecular mechanisms initiate various genetic events."
- line 54: "hypoxia-inducible factor (HIF) oxygen-signaling pathway" do you mean alpha not oxygen?
- line 154: what is (Vn / Vn + 1 = 0.15)??? please explain.
-line 172: "is based on the coefficient variance (CV) and standard deviation (SD)" of what? please complete the sentence.
- line 203: what do you mean by: "at both stages of entering the plateau"?
-Figure 3: A, B , and C, why it is connecting line, these are separate values, are they related to each other?
-table 5, 6, what do you mean by whole stage and whole stages, is it plain and plateau combined?
Experimental design: suggestions to authors:

please provide more details related to the study design, how many samples were collected from each individual and when, how many days after they were moved to the plateau.
Validity of the findings: Overall, the idea of the study is interesting and might be useful for future researchers in the field of hypoxia and the selection of appropriate housekeeping genes.
Yet, the authors do not explain the variability in their findings related to the different ranking scores among the different validation programs they used. This limitation of the study should be addressed in their discussion. Also further discussion should focus on the limitation and reliability of each of the used programs (geNorm, NormFinder and BestKeeper).

Would it be feasible for researchers to validate their finding in an experiment where cells are placed in hypoxic chamber and the same reference genes are assessed?
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: IDENTIFICATION OF REFERENCE GENES IN BLOOD BEFORE AND AFTER ENTERING THE PLATEAU FOR SYBR GREEN RT-QPCR STUDIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The English - including the newly added parts - would still benefit from improvements.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: IDENTIFICATION OF REFERENCE GENES IN BLOOD BEFORE AND AFTER ENTERING THE PLATEAU FOR SYBR GREEN RT-QPCR STUDIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript is still unclear, professional English editing is critical and required for this manuscript before being accepted.

examples:
Line 78: what do you mean by “Gene sequences were deposited in the NCBI database under GenBank accession numbers indicated in Table 1”

Line 96: “correlation coefficient (R2 ) of each candidate reference gene were calculated for (Table 2)” calculated for what???

Line 100: “The geNorm (Vandesompele et al. 2002) program is a measurement of gene expression stability 101 (M)” the program is not a measurement.

Line 113: add “in subjects” after the word reference genes

Line 138: need to explain in the text what the formula means, what V is.

Line 181: “However, there are few studies on the evaluation of optimal reference gene(s) 182 between low- and high-altitude conditions” this sentence is redundant.
Experimental design: details are still lacking:

RNA samples and cDNA synthesis: this section still lacks a lot of details, such as how samples were processed, were the mononuclear cells isolated? What method as used? Or did they pelleted the whole blood? How did they extract the RNA

There is no positive control to confirm that hypoxia has occurred in the blood of the subjects after 3 days of being in the plateau. A measurement of hypoxia related gene is needed, and/or validation of these data in experimental hypoxic conditions
Validity of the findings: fig. 1: why there is no band for TBP and very faint band for SDHA? and there was no mention in the text regarding this

Table 5: what is CP?

Discussion: it does not address the limitation of the study, the tools that are used, and the significance of their finding. It is more or less repetition of the results.
Additional comments: Since the experiments related to validating these findings in hypoxic chamber is underway, these data should be feasible to add.


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: ESTIMATED EFFECTS OF IMPLEMENTING AN OPEN ACCESS POLICY FOR GRANTEES AT A PRIVATE FOUNDATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.	The methodology is not very detailed (insufficient detail for replication), with some errors (see below).
2.	A structured abstract would be preferable to make it clear this is considered research.
3.	It would be helpful to have a basic description of the number of grants and the size of grants. The total amount of funding the GBMF provides annually should be provided, to provide a frame of reference.
4.	“OA journals provide access to all content immediately online.” Most definitions of open access also include Creative Commons licenses, but they are not addressed until the last paragraph of the article and their benefits are not mentioned. If the authors are not considering CC as part of this evaluation, they should define up front that the type of OA being analyzed refers to free content only.
5.	“We then estimated the annual cost for making these articles OA by multiplying by a low ($1500) and high ($3500) APC estimate (Solomon 2013).” This reference is not included in the reference list (and should be) so it wasn’t possible to verify that the estimates are reasonable and appropriate for the journals in the study.
6.	“Instead, they are often more concerned with publishing in the most relevant, highest impact journal for their field (Priem 2013).” Priem 2013 doesn’t appear to say this—it is a thought piece about the future of how researchers will disseminate their work and indicates that researchers are already changing in how they do so. Is the reference wrong?
7.	“To explore potential impacts of an open access policy at GBMF, we analyzed 2650 publications produced by GBMF grantees between 2001 and 2017” Did the choice of journal change over time?
8.	“Figure 1. Breakdown of journal type (open, hybrid, or closed) used by GBMF grantees for the 2650 articles (left) published in 573 journals (right).” This notation of journal vs article is opposite what the figure shows. Which is correct?
9.	Dataset: would be more transparent to review if Post Print Policy indicated Y for authors are allowed to publish and N for they are not allowed to (rather than 1 or 0).
Experimental design: 1.	The novelty and importance of such an analysis is not addressed. Have any other foundations published their analysis? Why is it important to share this information?
2.	The design is not strong; the authors have no way of knowing how complete the data are; certainly the data in 2015 imply that the rest of the years are underestimated. The estimates vary 10-fold. The estimates for APC charges are simplistic and the reference for them is not listed.
3.	The authors don’t actually provide the calculus of weighing pros and cons besides concluding that gold OA would be expensive (apparently – they don’t actually say that they concluded it would be too expensive for the foundation). The fact that gold OA would cost more than green OA is apparent without doing the analysis.
Validity of the findings: 1. The authors do not know the number of papers actually published (the statement “We identified more than 800 publications in 2015 (compared to approximately 300 and 500 in the years before and after, respectively). In 2015, the newly funded Data-Driven Discovery Initiative in the Science Program began systematically collecting data from its grantees about publications, resulting in the large spike.” suggests that the articles in other years are substantially undercounted.
2. The gold PA cost estimates have a 10-fold range and are based on assumptions rather than actual charges; they acknowledge that the actual amounts may be lower or higher.
3. Factors such as institutional membership that would reduce expenses, or OA journals that do not charge APCs, are not taken into account.
4. The authors do not estimate the value of OA, and in fact only mention the benefits of OA in the introduction.
5. They don’t consider Creative Commons licenses.
6. Title, “Expected effects of an open access policy at a private foundation” This study does not address effects (including impact of the research if it is made freely available after a year, immediately, or never), only costs and journals that authors could publish in. Perhaps “Estimated costs of implementing an open access policy at a private foundation”
7. The authors state, ““OA offers a number of benefits including increased citations counts (Gargouri et al. 2010), accessibility for building research capacity in developing countries (Chan et al. 2005), enhanced visibility of research (Tennant et al. 2016), and decreased financial pressure on academic and research libraries (McGuian and Russell 2008).” They state, “In an effort to increase access to the research results it funds” but which specific benefits were of greatest importance for the GBMF? How does their new policy address these benefits?
8. Why did the GBMF feel it was important to let authors publish where they normally would rather than encouraging them to publish in OA journals
9. “grantee’s preferred journal” – it’s unknown what their preferred journal was; this was the journal they published in.
10. “GBMF plans to revisit the efficacy and impact over time for the newly implemented policy. There are several variables that can be altered to potentially strengthen the OA policy. These may include (1) restricting embargoes on archiving OA versions to six months (compared to 12 months); (2) requiring CC-BY licenses for all publications; (3) setting aside funds for covering grantees’ OA fees (independent of their grant funds); (4) mandating particular repositories for OA archiving; or (5) expanding the policy to include outputs other than peer-reviewed journals (e.g., data, software, books, etc.).” It is surprising to see this statement after the analysis. Why was the decision to use the green approach made and what factors would make GBMF rethink that decision?
11. “GBMF funds research in basic science, environmental conservation, patient care improvements, and preservation of the San Francisco Bay Area.” “Moore Foundation grantees tend to publish in hybrid journals (74% of journals; 72% of articles), with open (16% of journals; 17% of articles) and closed (10% of journals; 11% of articles) journals less represented.” The ratios of gold to green journals vary substantially by field (see Björk et al., 2010, doi: 10.1371/ journal.pone.0011273.g004 ). It would be useful to see whether the calculations vary substantially by field.
12. Cost estimates don’t take into account memberships (eg, In “Cambridge RCUK Block Grant spend for 2016-2017” https://unlockingresearch.blog.lib.cam.ac.uk/?p=1463 : “The average article processing charge was £1850 – this is significantly less than the £2008 average last year, reflecting the value of memberships”)
Additional comments: This paper provides the assessment conducted by a foundation in determining what OA policy to implement, and you should be lauded for being more transparent about your decision making than is often the case. However, the paper has a number of limitations. The limitations are in part due to the challenges of finding all the publications supported by GBMF and taking into account the actual APCs instead of the estimated APCs. However, if you don’t provide the caveats and frame the discussion appropriately, another foundation might look at this and make the same decision without digging deeper, which would be unfortunate. The decision-making process presumably involves weighing pros and cons, not simply (apparently) "that's a lot of money, we can't afford that." Therefore, while the transparency is laudable, the analysis is fairly simplistic and it doesn't really rise to the level of research. While a formal cost-benefit analysis is presumably more than you are willing to undertake, what proportion of grants would have to not be funded to make up for the expense of funding OA? This sort of estimate would be useful.


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: ESTIMATED EFFECTS OF IMPLEMENTING AN OPEN ACCESS POLICY FOR GRANTEES AT A PRIVATE FOUNDATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper presents an initiative of the private funding company for changes in their policy related to the open access to the articles written by the grantees. The study involves “more than 2000” publication in “more than 500 journals”, and approximate cost of OA, according two suggested OA policies, has been calculated and discussed.
There are wrong definition on gold and green OA present: “Gold Open Access” journals which are considered only as journals with APC business model. It is well known that many gold OA journals do not charge authors. Also "Green Open Access" is not related with the journals but with authors who deposit their works (not only journal articles) into different institutional, subject based or other type of OA repositories.
In the focus of the study are possible OA policies, but it is not clear why the funder wants to mandate OA. Benefits of OA for funders and researchers are not discussed. Funders have encouraged or mandated OA because enhanced visibility and discoverability increases the return of their investment, making the results of the funded research more widely available. Funder’s OA policy ensures the results of the research they fund can be read and used by anyone, including industry and society. Also, funder adopting OA policy avoids funding duplicative research, creates transparency, and encourages greater interaction with results of funded research. There are more benefits for researchers/grantees too. None of these are mentioned or discussed. There is only the phrase “potential implications” used in the discussion, but none “potential implication” is mentioned or discussed.
The manuscript was written in clear and professional English. Literature references, although not sufficient, are context provided. The missing literature includes mostly papers discussing OA mandates of other big funders. The manuscript is well structured and two figures are provided. Raw data is shared partially. Data on journals are included, but data on articles are missing.
The title is somehow misleading since no “expected effects of an open access” are discussed in the manuscript
Experimental design: Research questions are defined as an interest “in understanding (1) whether grantees would be restricted from publishing in their preferred journals, and (2) the financial ramifications of a policy advocating for and funding Gold OA when available.” Authors are not mentioning possible influences of the funders and the present research assessment criteria on the “preferred journals”, which could contribute to the study.
There is also kind of confusion with the years included in the study:
50 “In an effort to increase access to the research results it funds, The Gordon and Betty Moore Foundation (GBMF) began considering the implementation of an open access policy all publications produced by its grantees in 2016.”
65 “To explore potential impacts of an open access policy at GBMF, we analyzed 2650 publications produced by GBMF grantees between 2001 and 2017.”
76 “We also calculated an annual estimate of Gold OA costs for 2009-2016.”
Also, APC price ranges are not used consistently:
39 …on the order of $1000-3500 USD – USD needs to be deleted
	 later on, estimating the annual cost for making articles OA, authors are multiplying by a low ($1500) and high ($3500) – is it “low” $1000 or $1500??
Limitations of the study are not present.
Validity of the findings: Other minor changes include:
37 …OA are available publicly online.
77 …by 0.89 – what kind of data from Sherpa/Romeo was used to calculate this percent?
88 “Although we have no information on the percentage of those articles published in hybrid journals that were published Gold OA, we assume the percentage is low since this was not a requirement for grantees.” – information on OA articles by grantees could be easily retrieved, there is no need to estimate
102 “Based on these proposed policies, we calculated that the percentage of articles not compatible with Policy 1 is 0.7 - that is, 99.3% of articles would have been compatible with Policy 1.” – please leave not compatible, OR compatible part of the sentence.
104 two times “were”
105 Annual reviews are “explained” but there is no single reason present which can explain why they are close
120 “since these are the years where we have data for more than 100 articles.” – what kind of criteria is that??
121 in the Results expressions like “more than 800”, “approximately 300” and “approximately 500” cannot be used – please state accurate numbers
Additional comments: An interesting topic was presented that has been somehow. superficially elaborated.


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: ESTIMATED EFFECTS OF IMPLEMENTING AN OPEN ACCESS POLICY FOR GRANTEES AT A PRIVATE FOUNDATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is substantially better reported and nearly all the original concerns have been met. There are a few points that should be clarified, below.

1. Title is better but still could be more clear, eg, "Estimated costs of implementing an open access publication policy for grantees of a private foundation"

2. Background: The title was revised but the Background is still overly broad. Perhaps: "The Gordon and Betty Moore Foundation (GBMF) was interested in understanding the potential costs of a policy requiring that grantees publish their peer-reviewed research in open access journals."

3. "Anecdotal evidence suggests most authors do not select journals based on their level of openness or their policies around self-archiving. Instead, they are often more concerned with publishing in, instead choosing the most relevant, highest impact journal for their field.": Without a reference the evidence is anecdotal, therefore the language should be more equivocal, eg, "anecdotal evidence suggests that authors may not select journals based on..."

4. "We also determined whether the journal allowed authors to archive post-prints (green OA)": "Post-prints" is not a commonly used term--"archive accepted or published manuscripts in a publicly accessible repository" would be more clear.

5. "Based on the data reported here, the OA policies considered by GBMF are unlikely to have significantly impacted the grantees’ choice of journal due to lack of compliance.":
"due to lack of compliance" is unclear -- maybe "would not have substantially altered the journals in which the grantees published their work"  ?
Experimental design: The authors now adequately describe the limitations of the design in the Methods and Discussion.
Validity of the findings: The authors have addressed issues regarding impact and novelty, and corrected previous errors. Conclusions are appropriately circumspect.
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: ESTIMATED EFFECTS OF IMPLEMENTING AN OPEN ACCESS POLICY FOR GRANTEES AT A PRIVATE FOUNDATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: BEFORE: “Although we have no information on the percentage of those articles published in hybrid journals that were published Gold OA, we assume the percentage is low since this was not a requirement for grantees.” – information on OA articles by grantees could be easily retrieved, there is no need to estimate
REVISED: „Although we have no information on the percentage of those articles published in hybrid journals that were published gold OA, there is evidence that without funder mandates, the percentage of articles that are published OA is low (Tennant et al. 2016).“
Authors' response: This work is beyond the scope of the project and would require a significant amount of additional research and work. It was not part of our original research questions. The authors are not aware of where this information can be “easily retrieved” in bulk.

Could not agree that this is „beyond the scope of the project“. It is very important from the funder perspective to know exactly what percentage of articles are already OA (without additional funder's investments in OA), and before the implementation of the OA policy (mandate). Since the hybrid journals are the most represented group (74%) such an evidence should be the starting point of this study. There is the way to do it „in bulk“ for the articles in HTML and PDF formats. If authors cannot do it „in bulk“ for various reasons, the data for the last two or three years (2014-2016) could be checked manually and provided.

„We were also interested in whether a grantee’s journal choice would be impacted by two possible OA policies being considered. Policy 1 would require OA within 12 months of publication, either via the green or gold route. Grantees could comply by either publishing in open journals, by publishing OA in a hybrid journal (gold OA), or by publishing non-OA and self-archiving within 12 months (green OA). This policy would preclude grantees from publishing in journals that are closed and restrict self-archiving for longer than 12 months. Policy 2 would require immediate access at the time of publication (gold OA). Grantees could comply by either publishing in open journals, or by publishing OA in a hybrid journal. This excludes journals that are closed and/or restrict self-archiving at the time of publication.” - The only difference between Policy 1 and 2 is the 12 month embargo period which reflects only on articles from the closed journals and the green OA (self-archiving) share. Green OA is free of charge, and there are no differences in costs for OA between Policy 1 and 2. Since there are different journal policies on self-archiving, some articles from the closed journals will be allowed for self-archiving immediately at the time of publication (or even before!), and some not. Both policies include gold and green route to OA. This is not clear from the descriptions of the Policies.
Validity of the findings: Abstract: “Based in part on this study, GBMF has implemented a new open access policy that requires grantees make peer-reviewed publications fully available within 12 months. – the authors did not consider the usage rights (Creative Commons licenses), although it would be necessary for such an analysis, and this should be corrected in „available for reading“.

The articles that would not have been compatible with Policy 1 were exclusively from the family of Annual Reviews. These journals are not typical publications since they do not publish original research; they are review series in specific disciplines in science and social science. – there are Annual reviews also in other disciplines (Annual Review of Applied Linguistics, Annual Review of Biomedical Sciences, Annual Review of Clinical Psychology, Annual Review of Energy, Annual Review of Genetics, Annual Review of Immunology, Annual Review of Neuroscience, Annual Review of Nutrition, Annual Review of Pharmacology and ToxicologyAnnual Review of Public Health, etc.)

„The estimated maximum cost for implementing Policy 2 (i.e., gold OA for all publications) ranged from $401,835 in 2008 to $2,538,725 in 2015. (Figure 2).“ – the estimated cost is valid for both policies since the only difference is embargo (and green OA respectively).

„For example, we identified 814 publications in 2015 (compared to 328 and 501 in the years before and after, respectively). In 2015, the newly funded Data-Driven Discovery Initiative (https://www.moore.org/initiative-strategy-detail?initiativeId=data-driven-discovery) in the Science Program began systematically collecting data from its grantees about publications, resulting in the large spike.“ – the given explanation does not explain the lower number of publications in 2016 when Data Driven Discovery Initiative was still in place.

“Our estimates of number of publications per year (and therefore estimated maximum APC costs) rely on either the grantee self-reporting to the foundation, or the grantee including GBMF in manuscript acknowledgements that can be harvested by Crossref. Our range of costs is therefore likely an underestimate for earlier years that have lower publication counts due to the increased difficulty in tracking down data from those years.” – It is not clear are the difficulties in tracking down data for the most recent years solved or not, and are the numbers of articles provided for the most recent years in the analysis accurate. For example, it is not explained why the number of articles in 2016 is significantly lower, compared with 2015.
Additional comments: This is improved version of the article, but the general impression is that experimental design has not improved significantly. The number of articles per year is not complete, and even though the authors state limitations in the collection of articles, it is unclear why the data for the latest years (except 2015) are not more reliable. The data on the share of articles already available in the open access is missing, and I strongly suggest the authors to add this, if not in this one, then in their future research. The authors' opinion is that usage rights and licensing are beyond the scope of the study, but this is an important issue for funders and should be considered as a part of the implemented policy. Open access is more complex than "gold" and "green" route.


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: ANANKE: TEMPORAL CLUSTERING REVEALS ECOLOGICAL DYNAMICS OF MICROBIAL COMMUNITIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper was well written and the figures were useful. No problems with basic reporting, but see comment about Preheim et al. 2013 in the general comments below which I think should be cited.
Experimental design: The research identifies a problem, and definitely addresses it. They perform some analyses based on simulated data that is nice and well described. Some of the short comings of the algorithm and future directions are clearly stated.
Validity of the findings: The conclusions are one of the strengths of the paper where they do a great job of recapping the positives and negatives of the approach.
Additional comments: Hall et al. Ananke Review

The contribution by Hall et al. provides an informative description of the bioinformatic approach they have developed. This software enables clustering of exact sequences across time-series based on their ‘dynamic similarity’. The paper is very well written and the software is a timely complement to OTU based approaches. The approach may be even more useful to help analyze datasets partitioned with finer resolution such as DADA2 and Minimum Entropy Decomposition, as more investigators transition their analyses to these methods.  In addition to Ananke, the Shiny-based visualization is very cool, useful, and is key to assessing Ananke’s ability to discriminate temporally similar sequences.

Below I highlight some aspects that I find should be addressed, roughly, in order of importance.
An important point, in general, is that the authors seemed to leave out what would seem to be an important reference to work that is similar. They need to cite and discuss a paper by Preheim et al. 2013, “Distribution-Based Clustering: Using Ecology To Refine the Operational Taxonomic Unit.” The Preheim et al. software uses both sequence similarity and distribution of their abundance across samples, including discriminating above 97%, similarity as Ananke does. The authors need to explicitly address the similarities and dissimilarities between these two approaches, which seem quite similar. Ananke is different in that it does not require sequence similarities, so it can find co-occurrence clusters between non-closely-related taxa. Which may or may not be considered an advantage.

Line 300: Ananke does not perform consistently across datasets of variable lengths, and they speculate that it might differ based on sequencing depth and diversity. They suggest that the user needs to go use the visualization tools provided (which is very nice and works great) and set their cutoff thresholds based on detailed assessment of the data. However, I find this requirement at odds with their statement in the title of section at Line 103: “Unsupervised clustering of time-series distances”.  I recommend omitting “Unsupervised”, here because even if they calculation is unsupervised (like OTU clustering), the assessment and analysis, does not seem to be so.

Section starting at Line 178: Title seems to disagree with my understanding of Line 95 and others. The authors found that more data meant less similarity to the “ground truth” not that data sets were “accurately clustered”. Authors state that the algorithm has a difficult time on taxa that are normally distributed with high or low variance, and on datasets with many time-frames, I appreciate their forthrightness. Though I recommend that the authors reflect this in the title of the section: Perhaps, “Assessing accuracy of Ananke with simulated datasets”

Line 319: I recommend the authors expand the point to include it’s ability to complement non-OTU based approaches like DADA2 (Callahan et al. ), MED (Eren et al.), and the Tikhonov method.

Line 214: Ananke cannot be used on taxa that are detected in less than 15 or 20% of samples. Given the importance of the rare biosphere, of course this is a drawback. I think that the authors should state this, but can also point out that these taxa will be found in the “noise bin”? It is a good example of why Ananke should be considered as a complementary approach to other methods, as stated in the conclusions.

Line 250: Many of these analyses may be performed on more powerful computers than a standard desktop. How is Ananke expected to perform on these rare taxa if one doesn’t filter them out? I imagine Ananke will perform well on some of these periodic taxa if they become very abundant on a few days, and not so well if they are just always around the limit of detection (very stochastic).

General comment: I think that the software would be more popular, accessible, and more cited if the authors wrote some additional guidance in the github page to give users examples of how Ananke could be used in parallel with other extremely common pipelines (QIIME and mothur) or (where I think it will be most useful) very quickly up-and-coming methods (MED and DADA2). This wouldn’t need to be in depth, just some general guidance.

Also, the software was very easy to install with root privileges, great job!  Might consider guidance for users without root privileges.  Also might consider providing a test dataset for testing if installation was fully successful and working as expected.

Line 53: Probably want to cite earlier work, e.g., Eren et al. 2013.

Line 57:  The Callahan reference is now published in Nature Methods, 2016.

Line 63: Is Ananke an acronym for anything?

Line 230-232: Authors should keep in mind that some taxa may have multiple copies of 16S and sometimes the sequences can vary (I’m not sure about E. coli). This could be a type of positive control for their, or other investigators, analyses.

Section beginning at 298: The influence of the user’s selection of epsilon values on the results is very clear and appreciated.

Line 311 Aren’t Actinomycetales and Acidimicrobiales relatively closely related? Perhaps an indication of the sequence similarity of these taxa would be useful.


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: ANANKE: TEMPORAL CLUSTERING REVEALS ECOLOGICAL DYNAMICS OF MICROBIAL COMMUNITIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: see General comments for the author
Experimental design: see General comments for the author
Validity of the findings: see General comments for the author
Additional comments: Hall et al. developed a software Ananke to cluster the time-series microbiome data. There are several major issues in this study.

The processing pipeline in Ananke consists of: 1) Tabulate unique sequences 2) Filter out sequences with low counts 3) Calculate short time-series distance and 4) Cluster using DBSCAN.

Unique sequences in the microbiome data can be easily calculated using 100% identity OTUs in the software QIIME or Mothur. Calculation of unique sequences was not performed in the previous studies, which was not due to the technical or software problems.

The aim of the operational taxonomic units (OTUs) clustering is not only the data simplification but also minimizing the influence of sequencing errors. The sequencing errors occur in all the sequencing platforms, particularly higher in 454 pyrosequencing. Using unique sequences rather than OTUs would make the analysis intolerance of sequencing errors. The 97% sequence similarity as OTU clustering cutoff was widely used in the 16S rRNA gene analysis, largely representing the community of the gut microbiome at the species level. 98% and 99% OTUs were used in the oral and skin microbiome studies as well. Unique sequences or 100% OTUs do not necessarily increase the resolution of the data analysis in the hypervariable regions of the 16S rRNA gene analysis.

In addition, Ananke takes the fasta file as input, ignoring the quality information (scores) of the sequencing data.

As shown on the simulated time-series data sets in the study, Ananke performed well with as few as ten time points. However, the data noise or error significantly affects Ananke over a large number of time points. Ananke has also the trouble in clustering normally distributed time-series data.

The analysis based on unique sequences significantly increased the computational memory requirement and the running time. The software performance, RAM usage and running time, was not evaluated in the study.

Thus all the above suggest that the rationale of the 1st step in the method does not make sense. It’s not a good idea to analyze the unique sequences in the microbiome study.

To make the method feasible, in the 2nd step, Ananke minimized the number of unique sequences by filtering out the ones with low abundance. A large proportion of data were missed in the downstream analysis, ignoring numerous species/strains in the microbiota and affecting the calculation of the microbial diversity. In contrast, the previous OTUs analysis utilized all the sequences in the samples. As shown in the study, a maximum of 157 and 635 Ananke TSCs were found with an average Ananke TSC comprising 0.6% and 0.2% of the data set in the human gut microbiome and in the freshwater lake microbiome, respectively. This result only represented a small subset of the microbial community. The clustering segregation is not apparent at all if TSCs are not manually highlighted in different colors.

Ananke uses the non-phylogenetic metrics (STS) in the 3rd step to compute the distances between unique sequences. However, the phylogenetic metrics, such as UniFrac distance, were more common in the previous microbiome studies. More metrics should be available in the software (http://qiime.org/1.6.0/scripts/beta_diversity_metrics.html).

The clustering parameter ε is hard to be chosen in 4th step of the software. The optimal number (or the robustness) of clusters can be estimated using the Calinski–Harabasz index and the silhouette analysis on k-means clustering. Ananke, as an unsupervised clustering though, needs to provide the measure to help the users determine the optimal number in a similar way.

Figure 1, Figure 3, Figure 4, Figure 5, Figure 6 and Figure S3 have no units and no exact scales labeled in all the y-axes and in some of x-axes. The results of the study cannot be evaluated.

The authors didn’t pairwise compare the results from Ananke to the ones identified in the original papers.

The paired-end Illumina sequencing has been widely used, however, Ananke cannot analyze this type of the data.


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: ANANKE: TEMPORAL CLUSTERING REVEALS ECOLOGICAL DYNAMICS OF MICROBIAL COMMUNITIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment.
Experimental design: no comment.
Validity of the findings: 1) The finding that 16S identity does not necessarily imply similar organismal ecology is not new, as the 16S rRNA gene has been shown since the discovery of its usefulness as a universal marker not to necessarily reflect the genomic diversity of the organisms (Abstract, Introduction). Yet, methods, such as Ananke, that aim at discovering finer ecological patterns are welcome.
2) The aim of the method is not clear: reading the Abstract and Introduction sections, it seems as if the authors propose to replace the current definition of OTU based on sequence similarity by clustering based on temporal profiles. Yet, the authors do not follow up in this direction in the Conclusion section (line 319), but seem to suggest otherwise its usefulness also for taxonomic purposes (e.g. lines 294-297).
3) The idea of OTU originates from the inability in microbiology to define the appropriate unit of evolution and selection. Therefore an "operational" definition is often used. Therefore one main question this study should discuss is whether a cluster of sequences defined based on a similar temporal pattern can constitute a unit of selection or evolution. How long should the time-series be then? How to standardize and compare across studies to compare those new temporally defined units? If we take several plant species for instance that are fluctuating similarly over time does this mean that they are under the same environmental triggers, under the same evolutionary pressure, etc.? I don’t think so, as this may be just a "guilt of association" case, especially if the time-series is short. Thus the important point of implications for evolution or selection should be discussed in the study. Also, the claim that “Ananke facilitates identification of potential microbial interactions" line 298 seems to go beyond what the tool can realistically provide (i.e. it can identify similar statistical patterns, not necessarily biological interactions). As a hypothesis generating/exploratory tool it seems however to be well suited.
Time was chosen as the main factor to cluster sequences, but one could envision the same being done using an environmental gradient instead. This approach is also not new and is what constitutes the core of the ecological modeling and community ecology disciplines.
4) Methodological aspects. The method computes short-term changes in slopes between sequence abundances at successive time points. Looking at the methodological procedure several points need to be particularly checked:
 a. The sequence "abundances" are relative as they were standardized at each time point by sequence depth. Therefore, these abundances are not independent from each other anymore. The authors should consider including appropriate methods to deal with compositional data in their approach.
b. The equation line 97 seems not to be scaled, i.e. that if longer time-series are used the distances will de facto increase. In most computation of distances, there is a scaling factor to make sure that the distance is scaled to [0, 1] for instance to allow meaningful comparisons.
c. Lines 161-166, 214-245, 248-249: the procedure seems to arbitrarily exclude rare events or other types of sequences before computing further quantities. Therefore varying amount of singletons for instance which are then removed will lead to changes in relative abundances in the sequences that are kept for downstream calculations. Sequence depth is then affected.
d. The authors based their work on the Möller-Levet et al. 2003 paper that clearly states that the method they developed is meant to be used for short time-series with uneven sampling points. Yet, the authors of Ananke used long-term (191 time points, lines 212-213) and rather evenly sampled data (daily samples; line 134). Is the approach then appropriately applied?
e. In fact the authors used an OTU definition of 100% identity here because they investigated the changes in abundance profiles of unique sequences over time. What is the impact of organisms having several copies of the marker genes with potential sequence differences among the copies? (In the case of 16S rRNA operons, one would expect on average more than one copy per genome).
f. There is a danger in proposing to "explore individual patterns" (e.g. lines 325-326), when no overall test for temporal changes when all data is considered altogether is performed beforehand. This would be akin to performing multiple pairwise t-tests instead of initially determining whether the ANOVA for a whole dataset is significant. Using an appropriate omnibus test is the only way to reduce the chance to observe false positives just by chance. There are some techniques to deal with time series for whole communities (i.e. multivariate time-series) and the authors should probably compare their approach to those established methods.
Minor comments
-Line 120: "Normal distribution" should be better explained because it is not clear whether the authors want to model a constant mean and constant variance over time (stationarity) or changes in variance over time even though the mean is constant (non-stationarity). In figure 1, other simulated "patterns" describe changes over time (x axis), whereas “normal” seems to refer to what happens on the y axis.
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: ANANKE: TEMPORAL CLUSTERING REVEALS ECOLOGICAL DYNAMICS OF MICROBIAL COMMUNITIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I appreciate the reviewers professional, complete, and satisfactory response to my initial review.  The paper is well written, and Ananke is an excellent contribution. I commend them on the visualization code accompanying the manuscript that enables the user to easily plot and consider appropriate epsilon values for clustering.


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: ANANKE: TEMPORAL CLUSTERING REVEALS ECOLOGICAL DYNAMICS OF MICROBIAL COMMUNITIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I do not have further comments and agree with the changes made by the authors.


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: GENE EXPRESSION OF BENTHIC AMPHIPODS (GENUS: DIPOREIA) IN RELATION TO A CIRCULAR SSDNA VIRUS ACROSS TWO LAURENTIAN GREAT LAKES
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: This study reports the transcriptome analysis of environmentally sampled Diporeia exhibiting differences in CRESS-DNA viral load. This report appears to be the first to explore transcriptional responses to infection with this virus in invertebrates. An analysis of differential expression was performed using RNA-Seq and standard methods, supported by qPCR data across 3 selected genes. DEGs between animals with high and low viral load are discussed in the context of their KOG classification and association with immune response. Interestingly, transcriptional changes in genes such as those involved in innate immunity were observed among the 3 sampling sites investigated.

This is an interesting article within the scope of this journal that is well written and clearly presented. The authors provide a good amount of data to support their findings and I have been able to confirm the raw sequence submissions at NCBI.

The main considerations relate to information surrounding the analysis of the RNA-Seq data in this study. Some detailed comments are listed below.

Results and discussion
It appears that there are multiple extant Diporeia species, can species be differentiated using COI gene analysis?  It is unclear in the manuscript if the Diporeia sampled in the study are of the same species, though this was assumed with the mention of sub-species in line 189. The authors mention in Line 205 “the lack of clustering between samples is likely as a result of high variability between organisms”, this might be expected of the comparisons if the samples are distantly related. I feel that the term “haplotype clades” needs to be clarified in the context of defining relatedness between samples.

Line 200: The reported contig N50 is rather low (290 nt), and read mapping results are quite poor (as low as 16% and not greater than 62%) as outlined in Table S4. It is possible that the reference assembly is still rather fragmented. The authors should clarify  how this has been handled in the analysis (assembly metrics file seems to be missing – see General comments).

Sample MI40(130) has a very low sequence yield compared to the other samples which may have introduced some bias to the DE analysis, unduly causing some dissimilarity with genes expressed in low levels. The authors should provide some support for retaining this sample in the study.

Line 108: The authors noted that reads mapping to the SILVA database were excluded from the assembly. Were there reads mapping in high abundance to database entries for potential pathogens of Diporeia, that may suggest a possible co-infection? If so, this may be interesting to mention in the manuscript.

It appears from Table S4 that a large proportion of reads map to the rRNA database, which seems to impact heavily on the overall sequencing depth. I would suggest that the authors offer a comparative example with another similar study in terms of their sequence yield.
Validity of the findings: no comment
Additional comments: Files and Figures
Summary of transcriptome assembly and annotation statistics doesn’t appear to be included in the Supplementary Table S4 file as the file name suggests. This file seems to contain only information on raw read and trimming/mapping results. These results should be included.

Supplementary Fig 2 appears to be missing? Can’t seem to locate the transcriptome stats mentioned in the manuscript.

Supplementary file Raw_Ct_peerJ.d0.xlsx it appears should be named Supplementary Table 3.

Minor grammatical correction required with the use of hyphenation being inconsistent for “over- and under-expressed”.


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: GENE EXPRESSION OF BENTHIC AMPHIPODS (GENUS: DIPOREIA) IN RELATION TO A CIRCULAR SSDNA VIRUS ACROSS TWO LAURENTIAN GREAT LAKES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The MS is well written and easy to follow. The figures and tables are well laid out and i don not see any issues with this.
Experimental design: The experimental design is good.
Validity of the findings: Data is is statistically sound based on the methods used by the authors.
Additional comments: I enjoying reading this MS. It is well laid out and relatively easy to follow. I like the concept of the MS and the aim to address the poor knowledge of the viral dynamics of LM29173 in Diporeia sp.

I have a few minor suggestions and questions

1) Abstract and else where: 0-3x10E6. 0x10E6 = 0. So perhaps change to "up to 3x10E6"
2) Lines 135-139: can this be put in a supplementary table to make it easy to follow?
3) Line 330-331: change "(PCV1; Allan & Ellis 2000); TTV; Okamoto 2009)" to "(PCV1; Allan & Ellis 2000; TTV; Okamoto 2009)"
4) In your transcriptome analsysis did you find other CRESS  DNA viral transcripts or RNA viral transcripts that may be co-infecting Diporeia sp and thus some of the up or down regulation may be as a result of a complex of viruses rather an only LM29173?


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: FILTERING OUT PARASITES: SAND CRABS (LEPIDOPA BENEDICTI) ARE INFECTED BY MORE PARASITES THAN SYMPATRIC MOLE CRABS (EMERITA BENEDICTI)
Review round: 1
Reviewer: 1

Output:
Basic reporting: In the first line of the Introduction (L12) – the phrasing is rather awkward and should be changed to read “Parasites can be generalists that infect many different host species, or specialists that only infect a small number or even a single host species.” Additionally, the author should also provide a general reference for this statement, which can be one of the following:

Poulin, R. (2006). Evolutionary ecology of parasites. 2nd ed. Princeton University Press.

Schmid Hempel, P., & Schmid-Hempel, P. (2011). Evolutionary parasitology: the integrated study of infections, immunology, ecology, and genetics. Oxford University Press

Loker, E., & Hofkin, B. (2015). Parasitology: a conceptual approach. Garland Science.

At L25 poor reasoning was given for why that the unidentified nematode species might be a generalist. There are many non-host manipulating parasites which are specialists that infect only a few or even a single species. This should be modified to provide a better explanation for why the nematode might be a generalist.
Experimental design: No comment
Validity of the findings: In the Result section at L100, it would be very helpful for the read to also report the range (minimum – maximum) of parasite intensity. While this could be worked out by looking at Figure 2, this is not as exact as if actual numbers are provided.

In the Discussion section at L146, the author stated “E. benedicti in this population is usual not only because…” – did they actually meant “unusual”?

I have a suggestion about regarding the different patterns of cestode and nematode infection in the two crustacean species. Could there be some differences in the behaviour or other aspects of the two species’ ecology which makes one more susceptible or exposed to acquiring the infective stages of the parasites? This is especially worth considering since the unidentified parasitic nematode was absent in E. benedicti, which also infected far less frequently by Polycephalus larvae and in much lower numbers. For example, see:

Koehler, A. V., Gonchar, A. G., & Poulin, R. (2011). Genetic and environmental determinants of host use in the trematode Maritrema novaezealandensis (Microphallidae). Parasitology, 138(1), 100-106.

Differences in the body size of the two species may also be a contributing factor to why one species is more heavily (and in the case of the larval nematodes, just one of the species was infected) than the other. For example, see:

Leung, T. L., & Poulin, R. (2008). Size-dependent pattern of metacercariae accumulation in Macomona liliana: the threshold for infection in a dead-end host. Parasitology research, 104(1), 177-180.
Additional comments: The findings of this study are interesting and scientifically robust. The analyses used were appropriate and the interpretation of the findings was generally sound, therefore, once the author has made the suggested changes, it should be accepted for publications 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: FILTERING OUT PARASITES: SAND CRABS (LEPIDOPA BENEDICTI) ARE INFECTED BY MORE PARASITES THAN SYMPATRIC MOLE CRABS (EMERITA BENEDICTI)
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a nice little study consisting of two parts. Firstly, parasite abundance was compared between two co-occurring sand crab species. Secondly, behavioral tests were conducted on one of them to investigate whether the cestode Polypocephalus sp. induces behavioral changes, which may indicate parasite induced trophic transmission to the final host. This is of particular interest because the parasite has been linked to behavioral changes in a different crustacean (Carreon et al. 2011), and the behavioral tests on Lepidopa benedicti and the quantification of parasites in that species provide the main story of this paper.
There are some issues related to the comparison of parasite data between the two species, and there are some potential issues related to the interpretations of the behavioral data, which I will address in more detail in the relevant sections of my review below.
1)	The study system is well introduced. However, the concept of PITT deserves to be defined and introduced earlier in the Introduction followed by a general reference. In this case, Lafferty and Shaw, 2013 would be a suitable reference. Moore, 2002 is another good general reference (book).
2)	Line 22-23: I think it is reasonable to assume that species sharing the same habitat are exposed to the same set of parasites. However, there could be many physiological and behavioral reasons why some parasites successfully infect one species and not another species. Therefore, it is a stretch to assume that co-occurring species harbor the same set of parasites. I recommend that you rephrase the sentence accordingly. I think it is important to not produce a too simplistic view of host specificity. Many other factors than the ability to change host behavior could be important. For example, parasites, which have to negotiate a potentially strong immune response are often host specific.
3)	Be clear and consistent in the use of terminology. Parasite intensity refers to the number of parasites in infected hosts only. If uninfected individuals are included (which I believe you do), then use the term parasite abundance, which includes all individuals examined (including uninfected individuals). Refer to Bush et al. 1997 for a more detailed outline of different parasitology terminology.
4)	L. 108-110: This sentence belongs in the Discussion (not part of this study).
Figures
5)	In Figure 3 I believe that the scale bar is incorrect in either A, or in B and C (the size of the parasite is very different between photos). Also in Fig. 3, I would only provide two photos, one from Lepidopa benedicti and one from Emerita benedicti, each of them indicating parasites in tissue by arrows.
6)	Fig. 5. In the Figure legend I suggest that you define the abbreviated term SEG. Sub-esophageal ganglion may not be known to a wider audience.
7) There are quite a few typos/spelling mistakes throughout the manuscript, which need to be addressed (e.g. lines 41, 57, 80, 114, 141, 146, 150, 160, 168, 169).
Experimental design: 1)	The research question states that behaviour would be tested in both species (L. 50-53). However, this was only done for Lepidopa benedicti. Rephrase the statement accordingly.
2)	It is problematic that you compare nematode data collected at different times between the two sand crab species. This is simply not meaningful in many cases since parasite abundance may vary greatly both spatially (within even a few meters) and temporally.  My recommendation is that you remove data on the unidentified nematode (Fig. 2). You can mention in the Results section that you did not find the nematode in Emerita in this study, and then refer to the previously published study reporting nematode infections in Lepidopa (Joseph and Faulkes 2014) as long as you do not directly compare the two findings.
3)	The methods are not explained in sufficient detail for replication. For example, how and where specifically were the animals collected? (it only says that they were collected). Also, how were Emerita dissected to examine for the presence of nematodes?
4)	L. 70-72: A minor comment, but behavior alterations may not necessarily be intensity-dependent. Therefore, presence/absence of a parasite may still provide an indication of if a parasite may change host behaviour.
Validity of the findings: 1)	My main concern regarding the interpretation of your results is that the effect of crab size on behavior was not investigated. You report that crab size was significantly and positively related to the number of Polypocephalus per individual (Fig. 4). That could also mean that the negative relationship between the number of Polypocephalus and digging time observed (Fig. 6+7) was influenced by the effect of crab size. Maybe you can use crab size as a co-variate in your analyses to correct for the potential confounding effect of size.
2)	You use parametric tests to test the relationship btw size and parasite numbers, and digging time and parasite numbers. To me it looks like your data violate the assumptions of homogeneity of variance in parasite numbers (y values) across x values (size). It is clear that variance in parasite numbers increase with increasing size of the sand crabs. I therefore suggest using a Spearman rank test instead of a Pearson correlation or Linear regression analysis. You may also be able to transform your data so that you can still use a parametric test (especially if you want to include size as a covariate).
3)	I wonder if you measured the dimensions of the larval Polypocephalus in any of the two host species or in white shrimp? Molecular techniques are necessary to determine the identity of Polypocephalus collected from different hosts, but morphological measurements may indicate obvious differences.
4)	Along the lines of the point above, I think you should mention that white shrimp generally occupy a different habitat from sand crabs (sea grass beds as juveniles and deeper waters as adults in contrast to the swash zone of sandy beaches), which may suggest that we are dealing with a different species of Polypocephalus.
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: FILTERING OUT PARASITES: SAND CRABS (LEPIDOPA BENEDICTI) ARE INFECTED BY MORE PARASITES THAN SYMPATRIC MOLE CRABS (EMERITA BENEDICTI)
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am satisfied with the revised version of the manuscript and recommend that it be accepted for publication.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: FILTERING OUT PARASITES: SAND CRABS (LEPIDOPA BENEDICTI) ARE INFECTED BY MORE PARASITES THAN SYMPATRIC MOLE CRABS (EMERITA BENEDICTI)
Review round: 2
Reviewer: 2

Output:
Basic reporting: I have no further comments
Experimental design: No further comments
Validity of the findings: No further comments
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 DARK CUBE: DARK CHARACTER PROFILES AND OCEAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is a standard descriptive study with all appropriate details included.
Experimental design: While not experimental, the research design is clear. I am troubled with the assumptions made in the cube design. While the authors notes the limitations of median splits in brief I think more needs to be said about problems with assuming traits are categorical as opposed to continuous and how this approach is better than a latent variable approach. The authors repeatedly allude to the unification or dark dou but it is unclear whether the present analysis is best here. The important point that might be missed in relation to the former is that it is the SHARED variance not the unshared variance that is of interest to many DT researchers. In reference to the second point, the two factor solutions have reliably been detected in very large samples which introduce more correlated errors--errors that M and P people may make systematically more than N people.
Validity of the findings: The findings are purely descriptive in nature. This study does not advance any DT theory is not one. The use of the B5 is a descriptive tool that allows us to understand the DT traits. As the B5 have become the language of all personality psychology, framing the DT in terms of the B5 helps others understand what is meant by the traits. However, all we really have here is correlated semantic agreement. The study does not advance any theoretical model and instead adds to the noise of B5 studies on the DT. While the authors have adopted a novel method, the results should not be oversold as resolving any conflict or question.
Additional comments: I find it notable that you write an entire paper on the DT and not cite me one time. This is especially problematic as I was the one who first postulated the presence of a DT factor; a finding that has been replicated both by my work but also other work by Figueredo et al. (2015; Evolutionary Psychology). The primary limitation of this paper is that is lacks any real thoeretical heft. It is completely descriptive in nature but the authors seem to overstep their mark here.


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 DARK CUBE: DARK CHARACTER PROFILES AND OCEAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript ’The Dark Cube: Dark Character Profiles and OCEAN’ by D. Garcia and F.R.G. Moraga addresses an important issue in the research of the Dark Triad (DT). Namely they argue to investigate the possible combinations of high and low DT traits in relation to the Big Five. This line of research is of high importance because the unity of DT traits has been questioned by several authors. The current study tries to make good for the lack of consistent relationships between DT and the Big Five throughout the literature.
The introduction gives a concise but clear outline of the problem and of previous research in the field. However, I found some of the phrasing somewhat misleading throughout the manuscript. I will list all three of them here.
(1) Labelling the mnp profile (low Mach, low narcissism, low psychopathy) as ‘agreeable’ might be confusing, because it posits agreeableness as an a priori anti-thesis of the DT (which is in fact the case in many studies). I would suggest to label mnp as ‘beneficent’ in contrast to the label of MNP (i.e. maleficent).
(2) Authors highlight the importance of investigating non-linear relationships between DT and OCEAN. I found it also misleading, because linear relationships are investigated (comparing two groups can only be linear). At the same time, I agree with authors about the importance of investigating conditional or moderated relationships. I would suggest two use on of the previously mentioned terms instead of non-linear.
(3) Although it has been already published (Garcia and Rosenberg, 2016) – and I can accept if authors chose to stick with their original phrasing –, labelling the character cube by Cloninger as ‘light’ might be also confusing. Cloninger’s TCI measure is frequently used in the assessment of personality disorders that are mainly based on character traits (especially SD and C). Simply omitting ‘light’ would easily solve this problem.
Moreover, please spell-check the manuscript throughout. E.g., p. 11 row 3 would go correctly ‘… is negatively associated to …’.
Experimental design: The study used a self-report cross-sectional design. The limitations resulting from this design should be mentioned somewhere in the Limitations and concluding remarks section. Authors should also report, which statistical software they used for the analyses.
Validity of the findings: The findings in their current form cannot be considered as valid. I will list my concerns below in detail.
(1) Dividing the sample into groups representing different Dark Cube profiles leaves the authors with two problematic groups. MNp consists of 11 participants and mnP consists of 17 participants. Using these groups in any comparison makes the validity of the results highly questionable. Suggested solution: authors should at least add a dimensional test of moderated moderation (or three-way interaction) for DT traits. This would be the same statistical approach as in Garcia and Rosenberg (2016). Using modules like e.g., PROCESS for SPSS would also enable authors to trace the conditional effects of DT traits on OCEAN.
(2) Since gender distribution is uneven in the sample and both DT and OCEAN are gender-sensitive, authors should at least report the gender distribution for each profile group. They might be also willing to control for effects of gender (and perhaps age) in statistical analyses.
(3) Although it might not fit in one table, but somehow group descriptives (M and SD) should be reported, maybe along with Cohen’s ds as indices of power.
Additional comments: I would be really happy to see your manuscript published, because it could stir up the water in DT research. However, half of the sample categorized either as mnp or as MNP leaves me unpersuaded whether it is correct to talk about a Dark Cube. This distribution shows that M, N and P are highly correlated, whereas a cube has three orthogonal dimensions. Maybe establishing national standards for SD3 on a representative sample would help with categorizing anyone over 50 T as high on a trait and equal to or below 50 as low on a trait. It would give us a realistic picture about the proportion of any profile in the population (I would be really sad if – as your sample shows – we would have 25 % of the population as maleficent).