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: GENOMIC ANALYSIS OF MORPHOMETRIC TRAITS IN BIGHORN SHEEP USING THE OVINE INFINIUM® HD SNP BEADCHIP
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study, Miller et al. analyze the genetic basis of three sexually selected traits in a population of bighorn sheep that has been monitored for a long time. The authors use an Ovine Infinium BeadChip and morphologic data to perform genome wide association studies (GWAS) and  identify SNPs that could be associated to these traits. The authors find a single SNP showing a low association with body length, and argue that the lack of association suggest that the traits should be controlled by many loci of low effect, instead of single loci of strong effect.
While the objective of the manuscripts is interesting, and the long term monitoring is very valuable and unique, I think that the authors could analyze with more depth the long-term dataset that they have. The main focus of the study is centered on the GWAS aspect of the results, even though they do not find any significant results. The authors argue that the lack of association is probably an effect of the phenotypic traits being regulated by many loci of small effect instead of single loci of strong effect. However, it is also possible that the lack of associations can be related to a low coverage of SNPs. I know that it can be difficult to have large amount of genomic data, and I do not believe this is a main problem in the manuscript. Given the lack of significant results, I think that this paper would be more interesting if they analyzed with more depth the genomics of populations of these individuals, including all the demographic information they have (genetic diversity, paternity analyses, etc…). In addition I would develop more the phenotypic analyses, perhaps also considering the demographic data they have. The authors have a very interesting set of data that could be incorporated into the analyses that would greatly improve the paper, instead of focusing only in the genomic part. In this regard, I have the feeling that in order to have more information, the authors perform LD analyzes and simulations to test for the power of their analyses. While these results are interesting, all this information is supporting the main results and not part of the objectives. I think analyzing with more detail the genomics of this population, and moving figures 2 and 3 to supporting information would make more sense.
I addition I have a few minor comments:
Lines 41-42: “For example by overdominance…..2013)”: The authors do not test or comment any of these examples in the discussion. I think this sentence should be removed.
Line 49: “Lek paradox”: The authors should explain what is the lek paradox, and how would the lek paradox apply for horns.
Lines 54-61: “The genetic basis … (Ovis aries)”: The authors mention that the genetic basis have been studied in this system. Then it is mentioned that breeders have been interested in removing the horns, and finally the authors explain other examples of horns. However the genetic information is explained later. I think it would be more logic to move this sentence to the part where the authors explain the studies that have analyzed the genetic basis in line 62.
Line 71: though should it be through?

Lines 97-99: “Found 21  regions …. (Kardos et al. 2015)”: Genomic studies on horns have already been done. I think it is important to here explain what is missing and why their study could be important. Mention that other traits remain to be analyzed?

Lines 106-107: “we contribute to knowledge on the genetic basis of complex quantitative traits”: I’m not sure this is true, since they only find one SNP with low association. As I mention before, I think it would be more interesting to also analyze the genomic diversity of the population, and focus more on the phenotypic aspect of the manuscript. If not, at least explain how they contribute to this knowledge because it is not clear for me.

METHODS:
Line: 113: “Most individuals are marked … known age”: I think this is very valuable and could be analyzed with more detail. Maybe test if consanguinity changes between generations, or something of this kind. Also comparing morphologic data between generations could be interesting. Exploiting this information could be valuable for the manuscript and build upon the genomic analyses.

Lines 151- 152:  “ We also estimated ….BLUPS)”: what is individual breeding values? The authors use this to select the individuals that are genotyped, but for somebody who is not familiar with the concept it would be important to explain it.

Line 167-168: The authors explain which SNPs are discarded, but it would be convenient to also mention the final number of SNPs, so the readers know the amount since the methods and not wait until the results.

Lines 178-183: The authors mention two steps, but they never explain whether the two steps are compared, connected or what is the point of having two steps. Is the first step used to control for the second step?

RESULTS:

Line 191: “used to quality filter loci” odd sentence, the authors should change it.

The authors remove SNPs based on missing data and MAF: What happens if they include some of the discarded SNPs. Maybe it is worth testing the same analyses using other SNPs in the genome. These analyses could go in supporting information, but might increase the power.

Line 201: ”genomic inflation”. Can the authors explain this?

Line 204: “examined” should be examine the

Figure 2 and lines: 204-215: This LD analyses are interesting, but I do not think that the result presented in figure 2 is a main conclusion or result. It is part of the methods and should go in supporting information. I would recommend rather putting a figure showing summary statistics or presenting the phenotypic data in another way.

Lines 226-228:  Two genes….not see an immediate connection with body mass”: I think this sentence should go in the discussion and that they should discuss this further. Explain why there is not a connection with body mass, and also explain why they found this association then.
Discussion:
Line 230: “several”, It is only three characteristics, this is not several.
Lines 233-234: “We found 1…. Poissant et al. (2012)”:  It is striking that they authors do not find any SNPs within the regions found by those described by Poissant.  SNPs should have a larger coverage of the autosomes. I think this needs to be addressed with more detail. Is it possible to map the candidate regions of Poissant and see if any SNP is found nearby? If so, all the candidate regions of Poissant could be false positives. Please develop further this result.

Lines 243-245: “However, based on … horns region”: The authors mention that they did not find a SNP in the region of RXFP. Maybe this is because they lost many SNPs that did not pass their filters. Could the authors verify if any of the SNPs from the chip appear in this region and analyze what happens if they include them in the analyses (Even if they are not in HW, or have a lot of missing data)? As they mention later, it is also probable that some SNPs are fixed in this population. Maybe it would be interesting if the analyze this. The sentence in lines 262-268 could be moved to this part.

Lines 247- 261: As with the LD analyses, the power analysis is not the main focus of the paper. This is interesting but not related to their objectives. These results could be moved to supporting information. Also, it would be important to explain better how they did the analyses, and explain better the parameters changed, because it is not very clear.
Experimental design: As I explain above, I think that it would be valuable if the authors develop more the genomics of populations and the phenotypic analyses. Also it would be interesting to include analyses that consider explicitly the long term study.
Validity of the findings: As I mention above, I think that the paper is too focused on the GWAS analyses, and that I would be more valuable to include other genomic analyses.
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: GENOMIC ANALYSIS OF MORPHOMETRIC TRAITS IN BIGHORN SHEEP USING THE OVINE INFINIUM® HD SNP BEADCHIP
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: In this paper the authors analyzed the genetic basis of three phenotypic features of  bighorn sheep.  They collected measures of horns and body mass from several individuals. Then, 95 individuals (76 used) were genotyped using a commercial SNP chip. The results showed no association for loci and phenotype (except one). The authors suggested that the results could be due to low sample/loci number or selective sweeps. The conclusions were referred to the need to increase the sample size as well as loci number.

Despite the negative results, I found this manuscript relevant and also well written. Although I have not expertise on QTL analyzes, I found the Methods well explained and in general understandable. However, the authors focused on the negative results, thus leaving aside interesting results.

-They showed the importance of the number of markers (lines 216-218)
-They actually found a locus having significant association, although without GO (lines 203-228)
-They suggested that there could be a selective sweep event that led to the lack of variation on the previous reported loci (line 262)

Considering the above mentioned, I suggest the following:

-There should be carried out tests of selection. This could give insights about the lack of variation found. If a signal is founded, it could be associated with sexual selection and/or hunting pressures, both of them also influenced by population demographics affected y anthropogenic factors.

Please check this paper for a compilation of methods of cattle breeds (Table 1)

Gutiérrez-Gil B, Arranz JJ and Wiener P (2015) An interpretive review of selective sweep studies in Bos taurus cattle populations: identification of unique and shared selection signals across breeds. Front. Genet. 6:167. doi: 10.3389/fgene.2015.00167

-The paper should be complemented with a discussion about  the biological factors that could lead to the observed results (as sexual and artificial selection, genetic bottlenecks, etc.), and not rely only in the assumption of the lack of samples/loci.

-Also there should be included reasons why the locus OAR9_91647990 could not be annotated. It was because a lack of well annotated  genome? Or the body mass could be affected by regulatory regions that are unknown? The locus in question could  have strong linkage with other locus? Are there reports of this?

-Finally, the title is ambiguous. I suggest that it should include something like "..the lack of association of phenotypic and genetic variation...".

Specific comments:

Some parts of the Results section should be moved to Methods.
Lines [192-193] (VIPER Software)
Lines [200] (Manhattan plots, add an explanation of how they were generated)
Lines [204-213] (PLINK Software)

Fig 1
Indicate the meaning of red and blue lines
Fig 2
Add an explanation for the gray scale


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: GENOMIC ANALYSIS OF MORPHOMETRIC TRAITS IN BIGHORN SHEEP USING THE OVINE INFINIUM® HD SNP BEADCHIP
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is interesting as the authors examined three sexually selected traits in bighorn sheeps using a SNP chip designed for domestic sheep and try to idendify candidate genes associated to these traits. I commend the authors for their extensive morphological data set, compiled over many years of field work.The paper is written in clear and professional English, nevertheless there are a few typos that need to be checked and corrected (see detailes below).
The literature reference provide sufficient field background. The introduction is clear, but there are a few concepts that should be explained for clarity such as lek paradox (line 49) and polled morphotype (line 69).
The article has a professional article structure, figures and tables. Raw data is shared. Nevertheless, supplemental materials needs more descriptive metadata identifiers to be useful to future readers.
Overal, the article is interesting. My main concern is that when using cross-species application of SNP chips, ascertainment bias and coverage have important effects in summary statistics, analysis of genetic structure and selection tests that reduce the power of selection tests and increase type I and type II error (see Lachance and Tishkoff, 2013 Bioessays 35:780-786). Therefore, the analysis and discussion of results should address if ascertainment bias was measured and corrected.
In addition, there are a few aspects on the biology of the species and methods used that should be included in the discussion (see below).
Experimental design: This article shows original primary research with a well defined question, which is relevant and meaningful. In addition, it is stated how research fills an identified knowledge gap.
The investigation is interesting, but as mentioned above, when using cross-species application of SNP chips, ascertainment bias and coverage reduce the power of selection tests and increase type I and type II error. Therefore, these issues should be addressed properly before acceptance.
In general, methods are well described. Nevertheless, there are a few aspects that should be described with more detail:
 In the methods section (line 166) the authors mention that "Genotypes were then exported to PLINK version 1.07 (Purcell et al., 2007) for additional filtering". Please explain more thoroughly what type of filtering was used and the parameters.
There are a couple of paragraphs (lines 204 - 213 and lines 223 - 225) in the results section that describe methods and should be moved to the methods section.
Validity of the findings: The discussion should include perspectives on how to perform a better analysis, either by focusing in amplifying the region of the RXFP2 gene (previously identified candidate for horn morphology) or increase genome coverage by using other massive sequencing approach such as RAD-seq.
Also, I think it is important to consider if including available data from domestic sheep will help assess asceirtanment data or even analyse if alleles fixed in the bighorn sheep population correlation with adaptive traits.
In the Method section the authors mentioned that the studied bighorn sheep population is isolated and philopatric. These characteristics of the population would result in high inbreeding coefficient and low genetic variation, therefore explaining fixed alleles in the population. I consider that it is important to include such aspects of the population and its effects on the analysis in the discussion.
The authors discuss that the traits they analyzed might be of polygenic inheritance. Nevertheless, this conclusion is speculative and it is importat to propose the kind of analysis needed to test this hypothesis.
Another point that should be addressed in the discussion is the effect of different selection regimes on the results, when there is strong sexual selection towards horn size in males, but not so in females.
Finally, I would recommend that the authors discuss briefly on the utility of SNP chips designed for domestic species in the study of wildlife.
Additional comments: Please check the following lines:
Line 187: "in in R version 3.2.4". Please remove one "in".
Line 204: "We were interested to examined gene annotations". Should it be "We were interested to examine...".
Line 215: "It interesting to note". Please change for "It is interesting...".
Line 249: "R script developed by (Minikel, 2012)". Please check for the position of parenthesis.


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: GENOMIC ANALYSIS OF MORPHOMETRIC TRAITS IN BIGHORN SHEEP USING THE OVINE INFINIUM® HD SNP BEADCHIP
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comments
Experimental design: no comments
Validity of the findings: no comments
Additional comments: Dear Dr. Eguiarte,
I have now read the new version of the manuscript entitled “Genomic analyses of morphometric traits in bighorn sheep using the Ovine Infinium HD SNP BeadChip” by Miller et al.
I think the authors have addressed well the comments made my editor and the rest of the reviewers. I have three suggestions or concerns that should be attended.
Lines 122-123: Is there a justification of why they measured these three traits and not others. A simple justification about their importance or why they were chosen for this paper would be nice.
Line 218-219: The authors mention that they keep 76 out of the 94 individuals that have measures. Maybe there is something I did not understand well, but they mention in the materials and methods that they chose individuals based on their individual breeding values.  Having individual breeding does not mean that you have measures? Maybe there needs to be a better explanation.
Line 229: “candidate markers”: isn’t it only one? In line 224 the authors only mention one candidate locus.


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: GENOMIC ANALYSIS OF MORPHOMETRIC TRAITS IN BIGHORN SHEEP USING THE OVINE INFINIUM® HD SNP BEADCHIP
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I found this new version pleasant to read. Also, I consider that all suggestions/comments were answered properly.

Therefore, I suggest that this paper should be accepted for publication.


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: GENOMIC ANALYSIS OF MORPHOMETRIC TRAITS IN BIGHORN SHEEP USING THE OVINE INFINIUM® HD SNP BEADCHIP
Review round: 2
Reviewer: 3

Output:
Basic reporting: As I mentioned in my previous review, the article is interesting and the paper is written in clear and professional English. I think the authors made a good work addressing my previous comments. I only have minor corrections that should be addressed upon acceptance.
Experimental design: Ok
Validity of the findings: Ok
Additional comments: I think the authors made a good work addressing my previous comments. I only have minor corrections that should be addressed upon acceptance.

Lines 219 – 222. Report the correlation values published in Poissant et al. 2012.
Line 229 and 231. Indicate the threshold used as breeding value. Define what refers to highest and lowest breeding values.
Line 240. Individual within loci does not makes sense to me. Please revise this.
Line 302. 3,777 instead of 3777.
Line 373. Parenthesis in italics.


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

Input:
Title: A BIBLIOMETRIC ANALYSIS IN GENE RESEARCH OF MYOCARDIAL INFARCTION FROM 2001 TO 2015
Review round: 1
Reviewer: 1

Output:
Basic reporting: Zhou et al aimed to evaluate the Global scientific output of gene research of MI and explore  their hotspots and frontiers from 2001 to 2015, using bibliometric methods.
This is an interesting paper based on a different concept of research articles.
The use of English language is adequate throughout the manuscript.
Literature references could still be improved, by mentioning and discussing more works related to this field.
Article structure and data are satisfactorily presented.
Results and outcomes are relevant.
Experimental design: The methods are appropriate.
Search strategies have well been illustrated.
Validity of the findings: Data is sound. Conclusion is adequate. However, addition of other relevant points could improve the significance of the conclusion.
Additional comments: Even if the quality of language is adequate, due to some minor language issue, further polishing of language will improve the quality of the paper.


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

Input:
Title: A BIBLIOMETRIC ANALYSIS IN GENE RESEARCH OF MYOCARDIAL INFARCTION FROM 2001 TO 2015
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the article is well-written, organized, and includes sufficient content. This review primarily suggests ways in which the authors can improve the writing and thoroughness of the paper but there are no suggested changes for methods or analysis.

1.  It is suggested that in the introduction section that a paragraph be added to address other bibliometric studies that have been conducted on MI research or conducted on genetic research.  This will provide the rationale for your study and indicate to the reader what this particular analysis is adding to the literature.

For example: Bibliometric Analysis of the Top 100 Cited Cardiovascular Articles ;The American Journal of Cardiology ; Volume 115, Issue 7, 1 April 2015, Pages 972-981

Cardiovascular disease research activity in the Middle East: a bibliometric analysis
S Al-Kindi, T Al-Juhaishi, F Haddad

Disparities in Cardiovascular Research Output and Citations From 52 African Countries: A Time‐Trend, Bibliometric Analysis (1999–2008)
GS Bloomfield, A Baldridge, A Agarwal

Global Cardiovascular Research Output, Citations, and Collaborations: An Ecologic, Time-Trend, Bibliometric Analysis (1999-2008)
MD Huffman, A Baldridge, GS Bloomfield… - 2013 - Am Heart Assoc

2. The article has a large number of figures and supplementary material, all of which are useful.  However, the figures alone are not very informative.  One option would be to see whether the figure can be expanded in order to view which label is near to which network/cluster.  The other option is to show one or two figures but the remainder of data switch the figure to the supplement and the table to the paper.
Experimental design: The research question is clearly stated and the methods of mapping are highly technical.

If you refer to this website: https://sites.google.com/site/citespace101/design-rationale/how-should-i-cite-citespace

You can provide more details about the strength of this methodology and include all of the relevant citations.
Validity of the findings: The major threat to the validity of this study is the search.  The authors should add a few sentences to the methods section to explain why they chose to search only in this search engine as oppose to using multiple search engines.  The evidence for adequate coverage in the search strategy should be stated.

The major weakness of the paper is the discussion and conclusion.  The current discussion largely focuses on a more detailed explanation of the results with some repetition.  The revised discussion should highlight the findings and compare these findings with the other bibliometric studies (e.g. are they in alignment regarding productivity by region or by institution, by journal etc.?).   Also, one unique component of CiteSpace is the analysis of burst keywords.  The results of this analysis and particularly the relevance and implication of the identified areas should be discussed.  Conclusion should be revised in order to state what exactly is the future direction of research indicated as a result of this study.
Additional comments: The remaining items are very minor

line 49: "genetic mystery" either explain what you mean by this term or remove it.
line 76: "simplily" is a typo but the term can be removed
line 96: "more likely"....I think that this statement is not supported by your evidence.  Either add evidence/reference or revise it.
line 99: change American to North American so that it is clear that you are referring to the continent and not the country.


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

Input:
Title: A BIBLIOMETRIC ANALYSIS IN GENE RESEARCH OF MYOCARDIAL INFARCTION FROM 2001 TO 2015
Review round: 1
Reviewer: 3

Output:
Basic reporting: A well written article reviewing the literature related to myocardial infarction.  According to me article is acceptable for publication after corrections are made (Minor revision)
Experimental design: Bibliyometric analysis (literature analysis) with co-citation analysis
Validity of the findings: The validity of the findings was examined by using the documents the authors uploaded in the supplementary materials. The findings are valid.
Additional comments: Analyzed in detail and given important findings on the subject but the following should be taken into consideration.

1) Authors should write a limitation of the study because the analysis were performed only with publications in the wos index (pubmed scopus et al. are not included).

2) Maps do not look nice and difficult for readers to understand. So this study was carried with the VOSviewer could have been better. Authors should read and cite the following study for corrections;

“Ozsoy, Z. & Demir, E. The Evolution of Bariatric Surgery Publications and Global Productivity: A Bibliometric Analysis, OBES SURG (2017). https://doi.org/10.1007/s11695-017-2982-1”

3) If descriptive footnotes are added to the figures, readers can understand more easily


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: AN OBSERVATIONAL STUDY ON RISK OF SECONDARY CANCERS IN CHRONIC MYELOID LEUKEMIA PATIENTS IN THE TKI ERA IN THE UNITED STATES
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this article ' A long term observational study on risk of secondary cancers in chronic myeloid leukemia patients in the TKI era in the United States' by Kumar et al., the authors used the updated SEER database, which released the chemotherapy treatment status of CML patients in April 2017. They systematically compared the SIR of secondary cancers status of these CML patients with the general population. They concluded that the CML patients have enhanced risk for SR, and indicated that TKI may not play a role in inducing the SRs. The paper clearly laid out the background information, their study design and nicely discussed the recent literatures in this field. Moreover, the limitations of this study in clearly stated in the discussion, which help better interpret the results and compare it with other studies.

The raw data shared is very clear, however, the two major figures of the paper are pretty small and blurry, which make it hard to read/comment on. The authors should improve the quality of these two figures.

One minor issue is the use of abreviations in the paper, i.e. SIR is not spelled out in its first appreance but the full name is spelled out more than once later on.
Experimental design: The main objective of this study is not clearly stated. As there are many previous studies that have already investigated the SR risks in CML patients, and some of these studies actually use the SEER database, the authors emphasize that one advantage of their analysis is that they included the chemotherapy treatment data for these patients. As these data are collected in the post TKI era, the authors stated their data could partially reflect whether TKI usage will affect SR development. However, the authors never state whether the aim of the study is to determine the impact of TKI on SR for CML patients. And if not, the authors should better explain what makes their study stand out compared to previous studies, i.e. what knowledge gap does this study fills in.

As the authors already mentioned in the discussion, their dataset only indicated whether patients were treated with chemotherapy or not. One does not know if the chemotherapy means TKI and should be caustious when making such assumptions, although TKI is one of the main chemo drugs used for CML in recent years. The authors should bring this explaination to introduction instead of mentioning them at the very end of discussion, to help readers understand the setup of the study from very begining.

If the authors would like to study the impact of TKI on SR development, a better way to analyze the data is to compare the SIR of SR rates between CML patients from pre-TKI era vs. those from post-TKI era, rather than comparing cancer patients data with the general population. This pre vs. post TKI comparion could eliminate factors such as the impact of genetic mutations due to CML on SR development.
Validity of the findings: The statistical analysis of this study is good in general. However, there are some issues that could be improved to better validate the findings.

1. In the patient selection criteria part, it is unclear why the authors exclude 141 patients since they developed 6 SRs. This has to be better explained.

2. It is not stated in the text how the authors get the SIR data of secondary cancer development in the general population.

3. The authors just compared the SIR of different groups but did not calculate the p-value of SIR to determine if the differences are statistically meaningful. The authors need to explain why p-value is not calculated.
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: AN OBSERVATIONAL STUDY ON RISK OF SECONDARY CANCERS IN CHRONIC MYELOID LEUKEMIA PATIENTS IN THE TKI ERA IN THE UNITED STATES
Review round: 1
Reviewer: 2

Output:
Basic reporting: I think the title uses the term “long-term observation study” but which was not well defined in the manuscript. One would also question if the follow-up duration for this group of patients with CML can be considered long enough to be called long term. I suggest the authors define the term accurately in the text and reconsider if this descriptive term is appropriate.
Experimental design: Cancers diagnosed in the period 2-12 months after the diagnosis of CML more likely could be a late presentation or remaining an overt characteristics of a synchronous double primary cancer. This period typically in an epidemiological study would be excluded from the calculation of secondary cancer. Therefore, I would like to see more likely "true" secondary cancer after the first follow-up year.

Line 116~117: The rationale to exclude this subgroup of patients seems not so justifiable.

After line 121: A subsection with a subheading of “Follow-up of Participants” or equivalent would be better to let readers understand the follow-up details.
Validity of the findings: Line 120 to 121: The authors stated that “A sensitivity analysis was conducted after excluding SCs which were diagnosed during the first year after diagnosis of CML to adjust for the surveillance bias.” Nevertheless, there are no ensuing results presented. I think it would be nice if a new figure 3 showing these results can be presented before acceptance.
Additional comments: The occurrence of chronic myeloid leukemia and chronic lymphocytic leukemia in the same patient is considered to be a rare event. However, this paper nicely quantitates the frequency of CLL after CML as 16/9200 = 0.17%, which, in my opinion, has added a contribution to the literature. Interestingly, case reports of CLL after CML also occurs in women, unlike the all-male result in this manuscript.

Table 1: Ethnicity: Would it be helpful to separate non-White into Black, Latin American and Asian-Pacific islanders?

Line 293 and line 265-266: In the Discussion, I think the authors can give us an idea of the estimated frequency of HSCT (which should be spelled out when first appears in the text) in patients with CML in the TKI era in the US.


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: AN OBSERVATIONAL STUDY ON RISK OF SECONDARY CANCERS IN CHRONIC MYELOID LEUKEMIA PATIENTS IN THE TKI ERA IN THE UNITED STATES
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall, the manuscript is very-well written with relevant introduction/references. It would be great if the authors could improve the quality of text in Fg. 1 & Fig. 2 as the current format is blurred/difficult to read.
Experimental design: The overall research question is very well defined and has clinical relevance.
Validity of the findings: The authors have extensively discussed the present study and compared with previous similar studies. The authors may want to add to the discussion as in what could potentially contribute to elevated risk for secondary cancers in CML in the TKI era.
Additional comments: Please see above.


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

Input:
Title: AN OBSERVATIONAL STUDY ON RISK OF SECONDARY CANCERS IN CHRONIC MYELOID LEUKEMIA PATIENTS IN THE TKI ERA IN THE UNITED STATES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors did a great job revising the manuscript. I have no further concerns and would recommend the publication of this work.
Experimental design: The authors did a great job revising the manuscript. I have no further concerns and would recommend the publication of this work.
Validity of the findings: The authors did a great job revising the manuscript. I have no further concerns and would recommend the publication of this work.
Additional comments: The authors did a great job revising the manuscript. I have no further concerns and would recommend the publication of this work.


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

Input:
Title: AN OBSERVATIONAL STUDY ON RISK OF SECONDARY CANCERS IN CHRONIC MYELOID LEUKEMIA PATIENTS IN THE TKI ERA IN THE UNITED STATES
Review round: 2
Reviewer: 2

Output:
Basic reporting: This study, at least from the results in the presented Tables and Figures, does not investigate the impact of TKIs on the development of SCs. Please revise line 95, 96 to "This study aimed to analyze the development of SCs among patients with CML in the TKI era in the United States."
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I think the Discussion Section has room to improve to make it more relevant and concise.


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: DESICCATION RESISTANCE: EFFECT OF CUTICULAR HYDROCARBONS AND WATER CONTENT IN DROSOPHILA MELANOGASTER ADULTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this work, Ferveur and collaborators study desiccation resistance in Drosophila by analyzing cuticular hydrocarbon composition and its relationship with water content and with survival. For this, the authors compared wild type strains, artificially selected desiccation resistance flies, transgenic lines with reduced desaturase expression, which should affect cuticular hydrocarbon composition and hence desiccation resistance, and mutant flies with reduced cuticular hydrocarbon levels.
Experimental design: The authors clearly explain how they carried out their experiments, and include important controls like differences between males and females, and they discard the possibility of unavertedly selecting other traits that would ameliorate desiccation resistance like seize, and biases for the generation of males versus females in the offspring of different genetic backgrounds.
Validity of the findings: The conclusions of this work are valid, limited to and supported by the data provided. The authors show that desiccation resistance can be acquired and fixed in a population after only few generations, which persist without further selection through several generations. The work highlights the complex relationship between desiccation survival and the variables measured in the study. According to the data, it seems that the resistance cannot be easily narrowed down to one or two variables, and this is already apparent in the different cuticular hybrocarbon composition of different strains, for instance, Zimbabwe and Dijon2000.
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: DESICCATION RESISTANCE: EFFECT OF CUTICULAR HYDROCARBONS AND WATER CONTENT IN DROSOPHILA MELANOGASTER ADULTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript includes sufficient background. It shows clearly the context.
The structure of the article is according to the required format by PeerJ.
Figures are appropriately labelled and described.
Experimental design: Although the research question is well defined and relevant, the results found seem be very preliminary. The experimental design incorporates many variables so the results are very difficult to interpret and to make precise conclusions.
Validity of the findings: The representation and statistic analysis of the data are appropriate. The conclusions are very general and are not completely consistent with the results found.
Additional comments: The manuscript entitled “ Desiccation resistance: effect of cuticular hydrocarbons and water content in Drosophila melanogaster adults” by Ferveur et al. addresses a very interesting topic.
The authors studied the possible relationship between desiccation resistance, cuticular hydrocarbons (CHs) content and relative water content. Ferveur et al. found that an increased proportion of desaturated cuticular hydrocarbons, but not the total amount, is associated with an increased desiccation resistance. Also, authors found that transgenic flies with a high proportion of water showed the lowest levels of resistance. They conclude that desiccation resistance and the proportion of desaturated CHs are tightly linked while a high water content negatively affect desiccation resistance, at least when a low level of desaturated CHs are presented.

Although this work provides some interesting data, I consider that the results are very preliminary for publication leading to complex and confusing interpretations. For example, they found that lines 77S shown increased desiccation resistance respect to the control, it increased resistance was no significantly different between these lines but the ratio desaturated CHs: linear saturated CHs (D:L) was significantly different. Authors say that these results suggest that CH composition and desiccation resistance are not identical (manuscript lines 235-236) however they conclude that increased resistance was linked with increased ratios D:L (manuscript lines 382-383). In my opinion, the results do not show a consistent relationship between these two characteristics (desiccation resistance and ratio D:L).

In experiments using the UAS-desat1-RNAi transgene, authors said: “Knocking down desat1 in all relevant tissues induced a reduction of both desiccation resistance and the ratio D:L. However, selective targeting of desat1 expression in oenocytes strongly decreased the ratio D:L, but did not affect desiccation resistance or water content” (lines 336-340). Again, these observations are not consistent with what the authors propose regarding to a relationship between desiccation resistance and the ratio D:L. The results regarding water content and desiccation resistance are not convincing enough.

In experiments using RNAi lines it is desirable to use more than one RNAi line to avoid off-target effects and include some RNAi control line like GFP RNAi.

Minor comment:

In manuscript line 119. Change “homozygous” to “heteroallelic”.


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: DESICCATION RESISTANCE: EFFECT OF CUTICULAR HYDROCARBONS AND WATER CONTENT IN DROSOPHILA MELANOGASTER ADULTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have modified the text in a way that further strengthens its readability. They explain what their results imply regarding desiccation tolerance in flies, and they clarify the use of their fly lines according to findings reported in previous publications.
Experimental design: No comments.
Validity of the findings: No 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: DESICCATION RESISTANCE: EFFECT OF CUTICULAR HYDROCARBONS AND WATER CONTENT IN DROSOPHILA MELANOGASTER ADULTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: The authors have adequately modified the conclusions doing these more consistent with the results found. Although I consider that the results are somewhat preliminary, these are interesting and provide of information for future studies about the relationship of desiccation resistance with cuticular hydrocarbons and water content in insects.


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: SMARTPHONE-BASED REMINDER SYSTEM TO PROMOTE PELVIC FLOOR MUSCLE TRAINING FOR THE MANAGEMENT OF POSTNATAL URINARY INCONTINENCE: HISTORICAL CONTROL STUDY WITH PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: a.	Line 16 the reference is listed as 1, and the rest of the paper is using author last names.
b.	Clear/English
i.	Line 43, I think you're trying to compare postpartum women to postmenopausal women? It may be more clear to state the group you are comparing them with. After all, postpartum women are non-pregnant women.
ii.	Line 86, I suggest "All data" instead of "All the data"
iii.	Line 113, Should it say "this data is not published"?
iv.	Line 118/119, I think you could say "The participant who agree to participate answered a similar initial questionnaire to the experimental group for background characteristics and current UI status."
v.	Line 185, the "two and 16" is confusing. Are these the participant numbers? If so, it isn't necessary and you could just state that two participants were excluded and the reason.
c.	References/sufficient background and context-Yes
d.	Raw data shared-Yes, I am able to open and view this file.
Experimental design: a.	Original-Yes
b.	Aime and scope-The focused aim for this study is a strength.
c.	Question well defined and meaningful-Yes, I believe it is interesting and meaningful research.
d.	Identified knowledge gap-There is a clear gap between the knowledge and the action of the women with UI. This study looks at this gap.
e.	Method described in detail-Yes, I believe this study could be replicated based on the description in the article.
Validity of the findings: Impact of this study was assessed. I believe this study could be replicated based on the description in the article.

Conclusion is well stated and linked to the original research question.
Additional comments: a.	In line 114, I think it would be nice to either have the same exclusion criteria or list the exclusion criteria for the control group so the reader knows there wasn't bias toward one group over the other.


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

Input:
Title: SMARTPHONE-BASED REMINDER SYSTEM TO PROMOTE PELVIC FLOOR MUSCLE TRAINING FOR THE MANAGEMENT OF POSTNATAL URINARY INCONTINENCE: HISTORICAL CONTROL STUDY WITH PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Thank you for the opportunity to review this article. The article provides sound findings regarding the effectiveness of the smartphone-based reminder system to enhance PFMT adherence and to manage UI in postpartum women. However, there are some issues that need improvement. These issues are outlined below:

Major Revision

I wonder about the withdrawal. You describe that the smartphone-based reminder system excel as a simple free way to assist postpartum women in performing PFMT in their free time. But sixteen women in the smartphone group did not record their current UI status after 8 weeks. It is 32.7% of enrollments. Why did not you discuss this point.

Minor Revisions

1.	Line 16
loss of urine.”1) In a population
Please delete 1).

2.	Line 56-58
I could not understand this sentence. Why do you put a parentheses.

3.	Line 79
Is ICI a mistake of ICS?

4.	Line 101
Who is a midwife? Does the midwife belong to the clinic?

5.	Figure 2
Historical control group and Smartphone group are assigned from a beginning in this research. I think that you should show a group name the upper part of the figure.

6.	Figure 2, Follow-Up section
 In the Historical control group, A parenthesis is not written.
Experimental design: Please provide more information about the exclusion criteria in the control group in the Materials & Methods section. You describe that it is similar to those in the smartphone group. It isn’t same. Please explain what is different.
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: SMARTPHONE-BASED REMINDER SYSTEM TO PROMOTE PELVIC FLOOR MUSCLE TRAINING FOR THE MANAGEMENT OF POSTNATAL URINARY INCONTINENCE: HISTORICAL CONTROL STUDY WITH PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Line 91, I think the parenthesis within the parenthesis should be brackets.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: This version of your manuscript is more clear and concise. Thank you for the opportunity to review your work.


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

Input:
Title: USE AND MISUSE OF TEMPERATURE NORMALISATION IN META-ANALYSES OF THERMAL RESPONSES OF BIOLOGICAL TRAITS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is generally well written in unambiguous language, sufficient introduction material and background with additional provision of theoretical context which greatly enhances readability for non-expert audience. In my opinion, the article would benefit from consistent use of the terms ‘traits’ or ‘rates’, which I have highlighted throughout in the PDF and ‘general comments’ section of the review. In additional some restructing in the introduction is suggested in the ‘considerations’ and additional points to consider which I think are essential for the discussion are also highlighted in the ‘considerations’ section of my peer review.

There is no statement of submission of data to a public archive, and the data in the supporting information did not download with correct formatting for me to adequately re-use or comment on suitability for re-use (perhaps a problem with a file conversion through the peer-review process).

Other than these comments, I have no major problems with the basic reporting of the article.
Experimental design: A clearly defined, and well tested, research question is explored throughout the manuscript which is undertaken to an impressive technical standard.

Lines 97-100 should clarify further the conditions for inclusion of these data in the article, additional a sentence describing ‘Biotraits’ on line 114 would be useful. Clarification is needed as to the software and packages used throughout the manuscript for full replication.
Validity of the findings: The general validity of these findings is likely to be high based on the robust analytical techniques and extensive database used, I believe the simulations are well designed an appropriately analysed and interpreted.
Additional comments: Thank you for providing an insightful and thought-provoking piece of work exploring the parameterisation of thermal performance curves and the consequent inflation of standardised performance estimates to review. It is clear the analyses are carefully orchestrated and undertaken with rigor and the resulting article is an interesting read. It is testament to the research that the article raises interesting questions which could be answered, I believe, within this piece if work – however I would consider these suggestions are at the authors discretion as the analyses are, in my opinion, sufficient in their current state. These suggestions are presented below with ‘considerations’ and ‘line-by-line’ points identified. I believe I have identified some necessary revisions to the manuscripts figures and additional points of discussion that should be addressed.

Considerations:
The article generally ignores discussing another key assumption that “a simpler version of the full model that ignores low-temperature enzyme inactivation is most often use” other than to acknowledge it. This assumption could be more strongly criticised than the assumption that Th is greater than Tref. While I don’t think it would be necessary for this particular publication that this assumption is explored (although it would be interesting and add to the paper), I think at least a discussion of the potential implications of this additional assumption should be included in the discussion, given that a seemingly more minor assumption of the model is explored in such detail throughout. Additionally, the analysis initially raised my concerns that a temperature of 0°C was chosen at Tref where I assume enzyme activity will be very low – while the assumption discussed here isn’t the main point of the article it would be better to acknowledge and discuss the implications of this assumption explicitly to avoid potential criticism that the analyses presented here ignores a potentially more important key assumption.

I light of the above comment, I think the analysis in “Identification of conditions that lead to a severely overestimated B0” would benefit from separating ‘cold adapted’ and ‘warm adapted’ species such that the assumption that enzymes are active at 0°C does not apply to the warm adapted species (i.e., set Tref to different values for these two groups? Or apply 0°C and 15°C Tref to both) – I think that the assumption that enzymes operate above 50% activity at 0°C for a tropical poikilothermic species is very weak, and the authors have a large dataset to choose to further test these ideas and assumptions.

The analyses using real thermal performance rate variation across temperature gradients may be strengthened by comparisons with simulations. For example, in the analysis “Inflation of trait value at reference temperature (B0)” a simple simulation coupled with the analysis of real data would provide an interesting comparison and be less biases by available data. Additionally, the behaviour of the simulation would be independent of biological heterogeneity. A comparison of expectations based on theory (simulation) with the resulting inflation of B0 in real traits would provide further insight to the magnitude of real inflation compared to potential for inflation (simulation) (i.e., is this as large a problem in real data as it could be?).

In the analysis “Implications of the inflation for investigations of thermal adaptation” the choice of Tref has been demonstrated as important in the previous analysis but is given as a fixed value here. Given that this is a simulation it would be relatively trivial to re-run over multiple values of Tref to explore the interaction between Tref and the negative relationship between Tpk and B(Tref) – I think this is important as currently I think the support for an ‘artificial’ relationship between Tpk and B(Tref), and thus false identification of MCA, is quite weak given the strength of the correlation. Furthermore, it would be better to justify where the choice of 7°C arises, other than it is below the minimum Tpk

A second suggestion for the analysis of “Implications of the inflation for investigations of thermal adaptation” that would support the take-home message of the paper, is to definitively show that MCA is not falsely detected when using the alternative approaches/models put forward by the authors. This should also be relatively simple given the simulation approach taken but would strengthen the authors argument that the Sharpe-Schoolfield model may falsely identify MCA but other types of models will not make the same error, and that therefore this is due to the assumption of the SS model.

Figure 2 isn’t as clear as it could be, although the information is fundamental to the paper. First, I think the equation defining the y-axis may be incorrectly printed as if B0 or Ppk is greater than B(Tref) then the equation suggests we take the log of a negative number? Second, I think the differences between B0 and B(Tref) should be presented in both absolute and proportional terms (relative to initial value and maximum rate – thus creating a 4-panel plot) because a doubling of a rate from 0.01 to 0.02 when the maximum value of the rate is 200 could be interpreted as less of a ‘problem’ compared to a lower proportional rate inflation of 10 to 15 which has a much larger absolute change. Second, the y-axis is very confusing and a value of ‘0’ to define when changes are non-negligible seems odd to me, it would be better if this were transformed such that data at 0 is a negligible change in B0 from B(Tref), and differences get larger with increasingly positive y-axis. Perhaps even a log(response ratio) may be useful here for proportional comparisons between B0 and B(Tref)?

On line 122-123 I’m not completely convinced that applying a cut off whereby rates = 0 at B0 were removed is valid, many species are likely to have performance rates at 0 for certain values of B0 depending on the thermal environment the species is adapted to. Can it be demonstrated this does not bias results, or that this cut-off was relevant for a small proportion of species (i.e., n=2).

Consistency in the use of ‘rates’ and ‘traits’ would be conceptually tighter. I personally would consider most TPCs to be derived from rates, rather than traits, and that the term ‘rates’ is more specific.

My supporting data files didn’t download properly, and a conversion from text to data in excel did not produce a dataset with standardised columns. Perhaps this is from transfer between the journal but may be worth double checking the files.

Line-by-line considerations:
4: This is a funding body/PhD program rather than an address?

26-32: I’m not convinced that the introduction benefits from this paragraph greatly. I think the work presented here is more broadly applicable to accurately understanding thermal variation in traits and comparative thermal physiology, which has relevance for climate change, but climate change shouldn’t lead the introduction in my opinion as your research is more fundamental and climate change isn’t relevant to later discussions.

24: Suggest changing keywords ‘model’ and ‘trait’ , ‘rate’ as very broad.

26-32: Given that the main importance the article highlights of accurately estimating B0 I would consider introducing metabolic cold adaptation early in the introduction

29: Garcia et al. 2014 isn’t relevant here.

30: Suggest changing ‘biological traits’ to ‘biological rates’

33: Suggest changing ‘are unimodal’ to ‘are generally unimodal’. Suggest changing ‘trait-value’ to ‘biological rate’

34: Suggest changing ‘data’ to ‘relationships’.

39-41: In my opinion, the introduction would benefit from a broader discussion of how the parameters are used in comparative physiology (not just MCA), with an emphasis that detection of MCA is an example of where inaccurate parameterisation of models can lead to false-positive results (I’m sure however there are many others too, but obviously MCA is useful to mention as the analysis investigates this effect later).

42: “the traits value” sounds odd. Which trait? ‘a cellular, organismal or population rate’s value’?

58: Could the ending of this sentence please be more explicit by defining ‘to data’. (e.g. to thermal performance rates).

42-56: In my opinion, this paragraph could benefit from a brief sentence describing the explicit consequences of overestimating B0 and how overestimation could alter current understanding of metabolic cold adaptation.

60: rates

79-82: Is this list of references is necessary given Table A1?

96-97: This statement on first reading appears contradictory to the result presented in figure 1A this is because the y axis on figure 1 is very non-intuitive and could be improved. Based on this statement, I initially thought why at the minimum difference between Th and Tref is the deviation of B0 from B(Tref) at a minimum too, if I misinterpreted this with I’m sure others will too. Consider rescaling such that the difference between B0 and B(Tref) is minimal at 0 on the y-axis.

104-105: Ensure the number of rejected vs. potential TPCs is recorded in the manuscript based on these cut-offs.

105: I would be interested to know that the results do not depend on the R2 cut off.

111-114: Please be specific about the machine learning approach used on first mention.

116-119: I do not follow the logic of using a Tref that = 0°C to obtain “reliable estimates of B0” when the argument put forward in the article is that “when non-negligible loss of enzyme activity occurs at Tref – e.g., due to denaturation or inactivation of some other component of the metabolic pathway – B0 overestimates the real value of the trait at that temperature (B(Tref))”. I may be wrong but I cannot imagine that >50% enzymes would be active at 0°C, I think this would be valid if the aim of this is to artificially inflate B0? It isn’t clear to me if this is the aim here. See ‘Considerations’.

122-123: I’m not completely convinced this cut off couldn’t bias your results. See ‘Considerations’.

124-136: In my opinion, the precise aim of this analysis should be introduced in more detail prior to describing the modelling process with a conditional inference tree. It is not clear in this paragraph what the ‘predictor’ variables are, and found it difficult to follow the paragraph and its relevance as a consequence.

134: ‘assess overfitting’

164: Your data are larger than your simulation of 1,000 TPCs, so this isn’t a valid justification (although I support the use of a simulation here).

164: consider rephrasing difficult to read.

167-168: How was ‘negative skew’ was assessed.

175-176: Is there a reference which justifies that species <15°C Tpk are ‘cold’ adapted?

201-203: The low value of the correlation coefficient should be emphasised here as it is in the legend of Figure 4.

210-211: This sentence would benefit from emphasising whether this is a novel finding of the study.

212-213: The first sentence here could be more clearly articulated. The word ‘this’ is used twice and thus the meaning of the sentence is lost, consider rephrasing. For example, “We determined that the discrepancy between real trait performance and estimated trait performance at B0 arises under the conditions that…”

216-217: This paragraph would benefit from some assessment as to whether most of the literature would suffer from this error, I would assume this is the case in a few studies of cold adapted species.

223-225: Is there a way to build the ML model such that the inappropriate use of Tref can be assessed by the parameters available in the literature?

232: ‘ones’ sounds informal.

233-234: Consider rephrasing as meaning is not initially clear to me. Is this sentence saying there may still be a small amount of bias in B0?

235: Unsure if this sentence is necessary?

238: A further useful suggestion could be to use a Tref appropriate based on the metabolic group such that a Tref of 25°C is not used for stenothermic polar species (for example).

261: This feels like it should be in the ‘recommendations’ section rather than a stand-alone header.

265-266: This sentence suggests there would only be a single temperature at which enzyme activity is at 100%, is this the case?

277-279: In my opinion, this sentence slightly overstates the implications of the results. I don’t think the patterns demonstrated in this analysis justify a ‘strong exaggeration’ of temperature-normalised trait-estimates and the correlation coefficient in figure 4 is quite low and, as such, the consequences of this rate estimate exaggeration appear to be relatively minimal.

284-285: Is there a NERC funding grant no. attached to each DTP?


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: USE AND MISUSE OF TEMPERATURE NORMALISATION IN META-ANALYSES OF THERMAL RESPONSES OF BIOLOGICAL TRAITS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The basic reporting meets most of the criteria. However, they seem to be missing some key citations (see specific comments) from the literature.
Experimental design: The authors achieved their research goal and provided an answer to their question. However, they left out a few key talking points (see specific comments).
Validity of the findings: The authors demonstrated some problems with the Sharpe-Schoolfield model, but need to consider enzyme and whole-organism performance separately. Thus, I don't find the results particularly interesting and even a little misleading at times.
Additional comments: General comments:

Here the authors evaluate the use of the Sharpe-Schoolfield equation to normalize data for making comparisons of organismal performance. Overall, the authors make a sound argument that the Sharpe-Schoolfield model generates biased estimates of temperature normalized performance when key assumptions are violated. However, the results are underwhelming and I have reservations as to why anyone would use such a model for whole-organism or population data. See papers (below) by Andy Clarke which explain why such models should never be confused with a description of the mechanisms underlying performance, which are undoubtedly fare more complex than a rate-limiting enzyme or even enzymes alone. Thus, the model’s parameters can only be interpreted at the enzyme level, rather than at the organismal level. At the very least the authors should address this issue in their discussion. Furthermore, the authors discuss and seem to promote the use of the Arrhenius equation as an alternative method. However, Andy Clarke (2004; 2006) provides good arguments against molecular interpretations of the Arrhenius equation when fit to the metabolic rates of organisms. This leads me to question the relevance of the study in general. Organismal biologists will likely not find this paper very useful as one should not draw conclusions about enzyme performance from whole-organism performance.

Perhaps a more specialized journal (e.g., comparative and evolutionary biochemistry) would be more appropriate than PeerJ.

Clarke, A. (2004) Is there a Universal Temperature Dependence of metabolism? Functional Ecology, 18, 252-256.

Clarke, A. (2006) Temperature and the metabolic theory of ecology. Functional Ecology, 20, 405-412.

Specific comments:

Lines 35-37: This is an unconventional way of describing a thermal performance curve and I’m not aware of any ecologists that actually quantify these four values. The only citation provided for use of these values is a self-citation, which makes me even more skeptical. For example, optimal temperature (To) is the common term here, not “the temperature where the performance peaks (Tpk)”. I don’t much care for acronyms, and trying to introduce a new version of an existing acronym is unnecessary and confusing to the field. Ecologists are also concerned with the more common terms “performance breadth” and “critical thermal limits” (e.g., CTmin and CTmax).

Lines 218-220: It seems odd that this point (a single sentence) needs to be its own paragraph. Either elaborate on the point or work it into another paragraph.

Lines 242-244: Why should these other models be considered? Provide a sentence or two describing the validity of their application here.

Lines 247-249: I don’t agree with this statement as numerous studies (almost all?) that measure performance curves measure performance below and above optimal temperatures. After all, that is how optimal temperature is determined. See:

Angilletta (2006) Estimating and comparing thermal performance curves.

Vickers et al. (2011) Extending the cost-benefit model of thermoregulation: high-temperature environments.

Williams et al. (2016) Biological impacts of thermal extremesL mechanisms and costs of functional responses matter.

Lines 261-273: This is the most common, and most appropriate, approach researchers use when studying whole-organism performance.


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: USE AND MISUSE OF TEMPERATURE NORMALISATION IN META-ANALYSES OF THERMAL RESPONSES OF BIOLOGICAL TRAITS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I thank the authors for including MCA in the introduction, but feel it's definition is too vague and little introductory information is provided on MCA. At least a specific definition of MCA would improve the introduction, particularly now that the paper is more focussed on this topic.

In my opinion the “Theoretical Context” section hangs awkwardly between the introduction and the methods, moving to the methods may improve the flow of the article.

The discussion does a good job in suggesting solutions to help compare temperature normalised rates, but would benefit from some specific examples of MCA 'false positives' based on incorrect parameterisation of TPCs, there is a broad literature, emphasised in Appendix A. The discussion would be more thorough and constructive if these references were used to place the results relating to MCA false detection in a richer context.
Experimental design: Including an equation of how the beta-distribution is parameterised would be necessary to understand how the ‘final curve height’ and ‘final curve width’ of the Table 1 are used. I cannot see how these are used in the parameterisation of the beta distribution. Subscripts i, j, and k, are not explained in the text or table 1.
Validity of the findings: No comment.
Additional comments: Thank you for your thoughtful and detailed responses to each of my comments. I think the updated manuscript is much improved and have only minor comments in the PeerJ review, and a few detailed points below.

Line by line considerations:
69: Reword to contain example in parenthesis within sentence for clarity, “aforementioned and other analyses” sounds vague.

134: Is the text for this subheading intentionally smaller?

140: unintentional double space

141: Unnecessary - “again using a large empirical dataset”

143: What is the total sample size of individual TPCs including training and test sets?

148: Would be beneficial to see a summary table of the taxonomic coverage/trait coverage in the SOM. Bacteria, macroalgae and terrestrial plants seems an odd choice of organismal diversity to choose to emphasise Biotraits scope.

169: Was this a subset of the Biotraits/literature. The sentence sounds like this was a separate dataset at the moment? Data subset?

184: Unnecessary

189: Please specify that the alpha and beta parameters are parameters of the Beta distribution.

200: Consider rephrasing this paragraph as I find it surprisingly difficult to understand despite the relative simplicity of the procedure.

209: The results start with a statement to direct the reader to a figure rather than a statement of the result with the relevant figure in parenthesis.

210: Could this be stated in terms of interpretation of the parameter differences rather than the parameters themselves? The reader currently has to juggle how the parameter equations relate to concepts and then to results in one go.

Figure 2. Could the Figure 2 axis y label be phrased in words rather than equations, with equations in brackets perhaps? (i.e., Deviation of B0 from B(Tref), Deviation of optimum performance from B(Tref)). I feel like this figures requires a lot of work from the reader and axis simplification would remove on component of the complexity.


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: USE AND MISUSE OF TEMPERATURE NORMALISATION IN META-ANALYSES OF THERMAL RESPONSES OF BIOLOGICAL TRAITS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No new comments
Experimental design: No new comments
Validity of the findings: No new comments
Additional comments: I appreciate the authors’ responses to my comments and the addition of some additional references to strengthen their arguments. This is a much improved version of the manuscript.

The only concern I have at this point is the author’s interpretation of optimal temperature. I think they are oversimplifying the measure and actually just describing it with their new proposed acronym (point at which the performance curve peaks). I feel that this is unnecessary and confusing to new readers in the field of thermal biology, but shouldn’t prevent the paper from being published. Readers can decide to follow this new acronym or not.

Specifically, I’m not sure how the authors are interpreting “optimal temperature”, but my understanding is that it is the temperature at which “optimal performance” is experienced produces the “highest peak” of a performance curve for that given trait. They could use their modified definition to simply describe what optimal temperature (a much better known term) is. I agree that where some performances are optimal (i.e., highest peak) does not automatically mean the “organism’s fitness is maximal”. In fact, the only times that is possibly correct is when the performance curve is specifically measuring fitness or a given trait’s optimal temperature overlaps with the temperature that produces maximal fitness. However, this is rarely the cased as most performance curves are more specific than “fitness” (or measure different proxies for fitness) and measure a single trait such as sprint speed, digestion rate, or enzyme reaction rates.

Yes, organisms often experience temperatures below optimal temperatures as these temperatures are energetically costly and unnecessary at all times. For example, an animal has no need to be at optimal temperature for digestion when it has an empty stomach. It makes ecological sense to be below the optimal temperature for digestion when without food in order to conserve energy. Furthermore, this is why there are often different optimal temperatures (or performance peaks) for different traits (e.g., sprint speed vs assimilation rate).

And finally, according to a brief literature search through Google Scholar, “the temperature where the curve peaks” did not produce any direct hits whereas “optimal performance” produced hundreds if not thousands of hits.


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: ANTITUMOR ACTIVITY OF CHLORELLA SOROKINIANA AND SCENEDESMUS SP. MICROALGAE NATIVE OF NUEVO LEÓN STATE, MÉXICO
Review round: 1
Reviewer: 1

Output:
Basic reporting: The introduction is too brief.

The results for DNA degradation in 2% agarose gel electrophoresis are not found in the text or Figure.
Experimental design: In the abstract the authors reported that
 The extracts were shown to induce tumor cell death by the mechanism of apoptosis.
However, only one experiment was conducted (AOPI staining) to prove apoptosis (a cell death pathway). There were no experiments done to show the mechanism of apoptosis such as caspase activity and gene expression study.
Validity of the findings: Not enough data to prove the cytotoxic activity of the  C. sorokiniana and Scenedesmus sp. methanol extracts. The results for DNA fragmentation is missing. Apoptosis should be supported by other assays such as cell cycle, Annexin 5, Mitochondrial membrane potential, caspase activity and apoptotic gene expression using qpcr.

The IC50 values of the extracts were not reported.
Additional comments: Not enough data to support the conclusion from the study. Hence, the results are inconclusive.
The experimental designs should be expanded to provide supporting results to justify the research question.


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: ANTITUMOR ACTIVITY OF CHLORELLA SOROKINIANA AND SCENEDESMUS SP. MICROALGAE NATIVE OF NUEVO LEÓN STATE, MÉXICO
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1.  English writing needs improvements.
2.  In the discussion, need to cite and comment on recent paper showing that C. sorokiniana extract inhibits lung cancer in vitro and in vivo (BMC Complement Altern Med. 2017 Feb 1;17(1):88).
3.  Should provide a representative image of cells stained with AO/EB and indicate apoptotic and necrotic examples in Fig. 3.
4.  The methods mention DNA laddering/smear but this figure is not presented. This is very important to provide further confidence that the extracts are working through apoptosis (laddering) more than necrosis (smear), as suggested by AO/EB results in Fig. 3. In methods line 163, should state DNA smear not scan.
Experimental design: 1.  Appears to be original in that they obtained organisms from local river, However, there is one very recent but more complete paper mentioned above that  uses C. sorokiniana extract in lung cancer.
2.  Methods for isolation, growth, and preparation of extracts is well described. There are some issues in methods described in general comments.
Validity of the findings: 1.  AO/EB results would benefit from a representative image.
2.  DNA laddering result is not shown and is essential before acceptance.
Additional comments: The authors obtained water samples from a local river in Nuevo Leon Mexico and isolated two strains of micoalgae, Chlorella sorokiniana and Scenedesmus. They present details on the methods of growing and confirming the identity of these organisms by 18S PCR.  Methanol extracts (250-500 ug/ml) of dried mass obtained from bioreactors was used for testing anti-cancer efficacy in mouse lymphoma L5178Y-R cells. An acridine orange/ethidium bromide (AO/EB) staining assay was used to determine effects on apoptosis and necrosis. These extracts had less cytotoxic effects on non-cancer mouse thymocyes.

In general, this paper provides some interesting information on utilizing a local micoalgae organism for testing anti-cancer activity. However, there are several issues that need to be addressed.
1.	Should provide a representative image of cells stained with AO/EB and indicate apoptotic and necrotic examples in Fig. 3.
2.	The methods mention DNA laddering/smear but this figure is not presented. This is very important to provide further confidence that the extracts are working through apoptosis (laddering) more than necrosis (smear), as suggested by AO/EB results in Fig. 3. In methods line 163, should state DNA smear not scan.
3.	In the discussion, need to cite and comment on recent paper showing that C. sorokiniana extract inhibits lung cancer in vitro and in vivo (BMC Complement Altern Med. 2017 Feb 1;17(1):88).
4.	Sentence in lines 247-249 needs to be revised. It is assumed what is meant is that extracts have low cytotoxicity in non-cancer cells but higher in cancer.
5.	English writing needs improvements.
6.	Fig. 1, why after 18d Scenedesmus biomass much greater vs S. sorokiniana? Does not correspond to numbers given.
7.	Several issues in methods section: a) more information of 18S PCR to identify strains; b) “Tumor cytotoxicity and apoptosis assay” subheading is misplaced and should be moved to line 120; c) how is the concentration of the extract measured? It is given as 1 mg/ml; d) more information on microscope source, wavelength used for analysis; e) there is mention of vincristine as positive anti-cancer drug but actinomycin D is used in Fig. 3.


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: ANTITUMOR ACTIVITY OF CHLORELLA SOROKINIANA AND SCENEDESMUS SP. MICROALGAE NATIVE OF NUEVO LEÓN STATE, MÉXICO
Review round: 4
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Some modifications have been made in the revised manuscript. I have attached the pdf file of the edited manuscript.


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

Input:
Title: ANTITUMOR ACTIVITY OF CHLORELLA SOROKINIANA AND SCENEDESMUS SP. MICROALGAE NATIVE OF NUEVO LEÓN STATE, MÉXICO
Review round: 4
Reviewer: 2

Output:
Basic reporting: 1.	Line 282--- misspelled ladder (“latter”).
2.	Line 290-291---revise to read “…resulting in up to 26% and 19% toxicity with the highest extract concentration (500 g/ml) (Fig. 4).  In L5178Y-R tumor cells, 500 g/ml of extract resulted in 62-75% toxicity (Fig. 2)."
Experimental design: Acceptable.
Validity of the findings: Acceptable.
Additional comments: Minor writing changes. Paper is improved and is now acceptable.


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

Input:
Title: EVOLUTION OF THE SCHOLARLY MEGA-JOURNAL, 2006–2017
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well written and meets all journal standards for clarity etc.
Some minor points:
Lines 224-225. “In a separate on-going study together with Mikael Laakso, we’ve estimated that there were 327,000 such articles in Scopus in 2016.” It’s not clear to me from the preceding paragraph what “such articles” refers to. The number seems too high to be mega-journal articles. Please clarify.

On line 181 the reference is a number, rather than the author name.

Lines 230-232. “Taking that as a rather conservative estimate for the current APC-funded article share, the estimate for articles for which APCs were paid is around 160,000 articles. These estimates are presented in table 4. Around 2,9 % of articles were published in mega-journals.”
It took me a couple of reads to realise that the "2.9% of articles" referred to ALL articles published, and not of articles for which an APC was paid (which is what the previous sentence refers to). I think this paragraph could be restructured to make it clearer.

I think all of the Tables would benefit from some additional thought regarding layout:

In Table 1, for completeness the SUM row should include the data from 2006-2008.

I think Table 2 would be clearer if it showed the increases as percentages rather than factors.

In Table 3, the Chinese share of all mega-journal articles (%) is shown in the far right hand columns, under the raw numbers – why not put them in the left hand columns under the other percentages?

I find the layout of Table 4 a little strange – I’m not sure why different (untitled) columns are used for the various article counts. I think this could helpfully be compacted.
Experimental design: I have two significant concerns.

The first is the decision to class RSC Advances and Palgrave Communication as mega-journals. RSC Advances has the following criteria for publication on their website (http://www.rsc.org/journals-books-databases/about-journals/rsc-advances/):
“The criteria for publication are that the work must be high quality, well conducted and advance the development of the field. Articles submitted to the journal are evaluated by international referees for the overall quality and accuracy of the science presented.”

Similarly, Palgrave Communications state the following as their aims and scope (https://www.nature.com/palcomms/about):
“The journal editors are dedicated to publishing high-quality original scholarship. Actively welcomed for submission is research on agenda-setting issues, grand societal challenges and emerging areas of thinking, irrespective of the field of study. This also includes research that reflects on, or seeks to inform, policymaking of all types.
Palgrave Communications additionally welcomes interdisciplinary research that makes an explicit and valuable contribution to the advancement of the humanities and/or social sciences.”

While I would agree that in both cases the term “quality” leaves some room for interpretation, neither journal explicitly states (as all the other journals on your mega-journal list do) that they review solely for scientific soundness. I therefore see no difference between RSC Advances and other large, broad scope, OA journals such as Nature Communications, Science Advances, or eLife.

My view is that either these two journals should be excluded from the analysis (which I think is preferable), or instead explicit discussion of their peer review processes should be included in the paper, along with clear justification for their being considered mega-journals.

My second issue is with the method used to obtain data relating to the proportion of Chinese authors.

The method states that “The share of Chinese authors in some of the journals was estimated by picking 100 sequentially ordered articles published in the summer of 2017 or 2013, and by visually identifying articles were [sic] all the leading authors were Chinese in the tables of contents.”

I think this needs clarification, as there seem to be a number of questions left unanswered. Why was summer chosen as the sampling period?  Was only the nationality of the lead author considered? How was the nationality of the author determined (just based on name? Institutional affiliation?).

I also have an issue with the sample size, particularly in the case of PLOS ONE and Scientific Reports. Given the publishing volume of these journals, the sample required to estimate a proportion with a reasonable degree of confidence is significantly higher than 100.

Given this it’s unclear to me why this sampling method was favoured over the use of a bibliometric database (e.g. Scopus, which was used for data collection later in the paper, and was used by Wakeling et al. to generate the 2015 figures you include in the table). Using Scopus would have allowed you to obtain true figures rather than estimates.

Out of curiosity I ran several such searches in Scopus, and in some cases found quite different results to the ones presented in the paper.
e.g.
For 2013, Scopus shows 18.5% of PLOS ONE articles having an author affiliated with a Chinese institution (paper suggests 12%). For Scientific Reports the figure is 29% (compared to 25%). For AIP Advances Scopus shows 32% (compared to 44%).

To be clear I suspect that were the full analysis done in Scopus, the conclusions would be broadly similar. But the Scopus approach is much more technically sound.
Validity of the findings: I am confused by some of the data presented in Table 1. The outputs of RSC Advances and Medicine prior to their conversion are shown as 99 each year. I suspect these figures may be place-holders that have not been updated – RSC Advances published many thousands of articles in those years, while Medicine published fewer than 99 each year prior to 2014.

The potential link between JIF and submission rates is interesting, but as the author notes, establishing cause and effect here is difficult. Almost all mega-journals (PLOS ONE being the notable exception) show year-on-year growth between 2011 and 2016. I think therefore that if the paper wishes to provide evidence of a potential link between Impact Factor and submission rates, it needs to put post-JIF submission increases in context (i.e. identify whether post-JIF growth is at a faster rate to pre-JIF growth).

To illustrate this it is interesting to note that the data presented in Table 1 shows the one and two year increases in PLOS ONE articles following their receiving a JIF in 2010 (2.05 & 3.48) and almost identical to the increases in the two years following 2007 (2.16 & 3.50).  Indeed PeerJ actually grew more slowly in the years after it got an Impact Factor (1.67 & 1.82) than it in the two years after 2013 (2.03 & 3.34). I suspect that if post-JIF increases are viewed in context it may be possible to identify more clearly those journals which were most effected by the JIF.

I was also left wondering whether the author might have drilled deeper into the geographic factors he alludes to on line 181. We know that in some countries (China being the most obvious, Spain another example) publication in journals with JIFs is formally incentivised. I wonder if analysing submission rates for these countries pre- and post-JIF might reveal something?

Given the peer review instructions I feel obliged to point out that the second half of the following sentence in the conclusion is not really supported by evidence in the paper: "its also evident from the numbers, that mega-journals have established a definite niche for themselves, based on benefits to authors in combination with the reasonable brand recognition they provide in CVs"
Since the paper does not examine why authors submit to mega-journals, it is probably necessary to make it clear that the proposed reasons are based on the literature or speculation.
Additional comments: It is helpful to see updated mega-journal publication data, and there are some interesting findings in the paper. I do feel though that some changes to the data collection are necessary to make this paper methodologically sound.


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: EVOLUTION OF THE SCHOLARLY MEGA-JOURNAL, 2006–2017
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: Identification of Chinese authors needs more detail. What is leading author – first author, corresponding author? And is this the only author looked at in order to identify the article as Chinese one? And what is “visually identifying”? Is that checking the relevant author’s affiliation, or whether the author name looks Chinese? – In the latter case, Chinese working in non-Chinese institutions will be lumped with authors working in China, which is quite another matter. Author behaviour will be influenced by institutional surroundings, not by nationality or ethnicity per se.
A sample of 100 seems to me, intuitively, to be a bit small for the large-volume journals – could this number be expanded to 200 for some journals and years, to make the numbers more reliable?

The 2017 numbers in Table 1 are 2 times the actual numbers end of June. Finding numbers by end of September and calculating on that basis could (should?) give more reliable numbers. If it could be without delaying publication much, I would advise this be done.

No comments on other aspects.
Validity of the findings: No comment
Additional comments: Some comments on minor points, referring to line numbers in brackets:
[12] [which authors pay for the dissemination services] I think you should enlarge on this - as it stands, it could be read as that you are of the opinion there is nothing done in the pre-dissemination phase, that authors need pay for. Which I cannot think is your opinion, based on your previous publications. (Might be I misinterpret your use of the term “dissemination” here?)

[17] Can any comparable number for Chinese authors in general in OA or TA journals be found?

[51] A tentative percentage would make this a better read.

[65] No Björk 2016 in the literature list?

[87] [5] looks like a literature reference, but according to another standard. Should it be [2017]?

[133-134] a. for [as], substitute [a]
b. No, no different font in Table 1, but  suspicious-looking rows of 99’s for both converted journals.

[158] For [of], substitute [or]

[228 ff] The percentage of OA articles published with APC payment is problematic. Crawford (who, alas, publishes himself and does not submit his works to peer scrutiny) found that for 2014 that 57 per cent of articles in OA journals were paid for through APC. (See https://scholarlykitchen.sspnet.org/2015/08/26/do-most-oa-journals-not-charge-an-apc-sort-of-it-depends/). Despite lack of peer review, Crawford’s numbers generally can be trusted. Crawford analysed the whole set of DOAJ journals, while you limit your analysis to Scopus. I take for granted that what is missing in Scopus generally is small OA journals which tend to be non-commercial. That means the APC payment rate in your data should be even higher than Crawford suggest, at least 60 per cent. This is, however, not a major point of your manuscript.

I hope you follow up later with some analysis of the background for, and possible consequences, of the large influx of Chinese authors in mega-journals, and compare this to the more standard journals. Also, why only to some of the journals?


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: EVOLUTION OF THE SCHOLARLY MEGA-JOURNAL, 2006–2017
Review round: 2
Reviewer: 1

Output:
Basic reporting: Good. There are a few typos (e.g. missing space in "PLOSONE" on L97, an extra word "that share of to be" on L154 etc).
Experimental design: The changes definitely make the paper more robust. I have only a few very minor points

L92-93 - A very small issue but for clarity you might report (perhaps in the table) which journal outputs were sourced from Scopus, and which from the journal website, and explain why (I'm aware that some journals are not indexed on Scopus, but some readers may not be). It is also usual to report whether you filtered Scopus results by "Document Type" - most studies like this limit results to "Article" and sometimes "Review" documents (to exclude corrections, letters etc). I don't think it's a major problem if you didn't do this, but should be clarified either way.

On lines 95-96 you write "...multiplying by a factor taking into account both scaling up to a full year and the time lag in Scopus for indexing...". For the sake of transparency and replicability I think you should say a little more about how this factor was calculated, and report the factors used in the final calculation. I may be being a little slow, but it's not obvious to me how comparing Scopus figures and journal website figures on the same day translates to an estimate of lag - wouldn't you need to look at the date of the last Scopus indexed article to calculate this?

L98-100 - Scopus "country/territory" data are determined by the country in which the author's affiliated institution is based (rather than on the actual nationality of the author). Reviewers always ask me to make this clear in the text, so I am passing that on!
Validity of the findings: All now seems sound.
Additional comments: I am very glad you found my comments helpful, and note that all of the issues have been addressed. I think the use of Scopus data make the results much more robust. I have selected "minor revisions" only because of the few small points that might need looking at in the method section.


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

Input:
Title: EVOLUTION OF THE SCHOLARLY MEGA-JOURNAL, 2006–2017
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: The points I raised have been well answered by the author.
Validity of the findings: No comments
Additional comments: I find that the points I pointed out as problematic have been well answered by the author, and find the article well publishable.