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

Input:
Title: THE TALE OF SPRINGS AND STREAMS: HOW DIFFERENT AQUATIC ECOSYSTEMS IMPACTED THE MTDNA POPULATION STRUCTURE OF TWO RIFFLE BEETLES IN THE WESTERN CARPATHIANS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language can be improved with the help of a native speaker.
The data are insufficient to test the glacial refugia hypothesis. I suggest instead that the manuscript focuses on the ecological and genetic differentiation patterns among the two species in the context of different dispersal capabilities.
Experimental design: no comment
Validity of the findings: The conclusions should reflect the main findings of the study, not discuss additional topics which were not touched anywhere else in the manuscript.
Additional comments: Bozanova and colleagues compared the mitochondrial phylogeographic structure of two Elmidae species that apparently have distinct habitat preferences (one prefers springs, the other streams). The results show that the spring species exhibited a higher genetic differentiation and higher genetic diversity than the stream species. Consequently, the authors propose that springs functioned as refugia during the Pleistocene climatic fluctuations. Overall I find the study interesting, but its premise is flawed. Although the sampling is regionally very good, it is insufficient to test the glacial refugia hypothesis because the sampling outside the W Carpathians is extremely sparse (just a few locations). These two species have very broad geographical ranges. Therefore, with the data at hand it is impossible to reasonably assess the endemicity of the detected haplotypes, and when did they diverged from other haplotypes throughout the ranges of both species. Furthermore, all the analyses unambiguously indicate a rapid and recent postglacial expansion in both species, but it is not clear from where they expanded, the W Carpathians or from more southern areas? This is a critical question, but impossible to test with the current data.

To make the manuscript more coherent and stronger, the part of survival in refugia and adjacent analyses (BSP and time trees) should be discarded and the focus should be more on the comparison of springs vs. streams. In this case the data is stronger, indicating that the spring species has a higher genetic diversity and more geographically structured genetic variation. This is most likely due to different dispersal abilities and ecological tolerance. The geographical coverage is excellent for such a comparison. More focus on ecology (emphasizing more convincingly the habitat preferences of both species) and comparisons of the two species’ genetic differentiation/diversity using formal statistical tests would strengthen the manuscript considerably.

Major points:
1) Although the language is relatively clear, the text could be improved. The use of the definite article is often inappropriate. The flow of the Discussion is rather chaotic, jumping from one idea to another. I suggest that a more experienced/native English speaker should have a look at the text.

2) The formulated questions are rather clear, however, question a) (“are the spring subpopulations
genetically more variable if compared to subpopulations in the streams?”) has not been addressed in the study. Genetic variation of spring and stream populations was not tested. What was tested was genetic variation among two species that seem to have different habitat preferences.

3) The two species are considered ecologically distinct, one preferring springs and the other streams. However, there is no formal analysis which supports this. Some numbers are given in paragraph 204-211. Although a trend is visible, it is not clear whether these differences are significant or not. As such, I suggest that the authors should compare the number of spring and stream localities for each of the two species with a 2x2 Fisher’s exact test. If more ecological data is available, such as water temperature and speed, etc, it would be worthwhile to include it. It would significantly strengthen the study if, for example, it shows that the spring species prefers lower temperatures and slower water speed. Alternatively, if such data is not available, important climatic variables can be extracted for each sampling point using DIVA-GIS from the WordClim database (https://www.worldclim.org/data/index.html). Altitude, temperature and precipitation could show significant differences among species. Of course, this is just a suggestion.

4) For AMOVA, why not test the influence of drainages as well? Especially given that these are aquatic species. Also, it is not clear why AMOVA groups were split to match geological units. Is this known to affect population structure in these organisms? Considering that AMOVA indicates almost no variation among geological subunits, it would be worthwhile testing whether drainages have a bigger influence on population structure.

5) While some analyses appear to show differences between species, there is never a formal statistical comparison. For example, the authors present the number of haplotypes and haplotype diversity per species. Other important indices should also be calculated in DnaSP, such as nucleotide diversity, number of polymorphic sites and mean number of nucleotide differences. However, all these indices should be calculated per population (where more than one individual was sequenced) as this would paint a more accurate picture and would allow a statistical comparison between the two species (using a non-parametric test such as Mann-Whitney). Only then the authors can formally conclude that one species had a higher/lower molecular diversity than the other. Such results could be presented in a table format, or, for a greater effect, a figure with boxplots, for example. The same statistical test should be applied to the Fst values. Was the mean Fst value in E. aenea higher than in L. perrisi?

6) The authors could try to do a pairwise Fst comparison within species only between locations in the same habitat, i.e. only among springs or only among streams. Is the mean Fst among springs higher than among streams? Is it statistically significant? This could be a worthwhile comparison in the context of this study. The sample size seems sufficient.

7) Another analysis that could be done is isolation by distance (IBD). In this case, one would expect a higher IBD in the spring species E. aenea.

8) Regarding the BSP plots it is not clear what data was used. If the authors used all the sequences, including outside the W Carpathians, then the plots of the two species are not comparable in the focal geographical context. This is because the coalescent times will differ among species due to the inclusion of divergent haplotypes outside the focal area. For example, in the case of L. perrisi, one of the two clades (Fig 3) is not found in the W Carpathians. Including it in a BSP analysis produces misleading results if interpreted in the context of the W Carpathians. The same likely applies to the other species.

Also the interpretation of the BSP plots is ambiguous. The authors claim that E. aenea had a stable populations size throughout the LGM, but it has an obvious expansion 3000 years ago, while L. perrisi started expanding much earlier, ca. 8000 years ago. How does this support the claim that the former species survived in the W Carpathians and the latter did not? One major difference between species is the coalescence time, but like explained above, this depends on the haplotypes included in the analysis.

9) The Conclusion section should briefly conclude the main findings of the study. Yet, the authors discuss DNA barcoding in the context of conservation and taxonomy and so on. This appeared from nowhere as it was not touched upon in other parts of the manuscript.

Minor remarks:
The formulation in the title “molecular population structure” is ambiguous. It is not clear what “molecular” refers to; it can be any kind of molecule. Instead, I suggest “phylogeographic structure” or “DNA population structure” or something like that. The idea is to emphasize the use of DNA.

Abstract. “whose molecular diversity and phylogeographic patterns have not yet been explored”. Well, this is not true, there are some phylogeographic studies on spring fauna, but still the area is understudied. Thus, this sentence should be rephrased to emphasize that there is insufficient knowledge. “mtDNA barcoding fragment I” should be “mitochondrial DNA barcoding fragment representing the cytochrome c oxidase subunit I gene”.

Throughout the text both “Carpathian Arc” and “Carpathian Arch” are used. The correct one is “arc”.

Line 121. “Apuşeni” should be “Apuseni”. Please correct throughout the text.

Table 1. How many individuals were analyzed per sampling site? Why samples originating outside the W Carpathians are not included in the table? Please also provide GenBank accession numbers.

Table 2. Could be worthwhile to include herein the values for the molecular diversity indices and the number of analyzed individuals per species.

Figure 1. The inset map showing the wider geographical context is unusual. Greece, Austria and Russia are colored as if they are seas. On this map it is also not indicated where the study area is located.

Figure 4. Do the Fst analyses include only W Carpathian localities? Which values are statistically significant? What correction was applied for multiple testing to avoid type I errors? Maximum values don’t say much. What are the mean values? Are they statistically significant?

Figure 5. Indicate what the colors represent.


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

Input:
Title: THE TALE OF SPRINGS AND STREAMS: HOW DIFFERENT AQUATIC ECOSYSTEMS IMPACTED THE MTDNA POPULATION STRUCTURE OF TWO RIFFLE BEETLES IN THE WESTERN CARPATHIANS
Review round: 1
Reviewer: 3

Output:
Basic reporting: In general, the manuscript is clearly worded, well structured, well written, based on a large data set, analyzes are correct and conclusions are well-founded. It is an original primary research with well defined questions. Design, materials and methods are clear and fits with the standards. Methods chapter probvide sufficient details. The results and conclusion are important and are of interest, overall the manuscript is recommended for publication. No serious gaps or errors found; comments are mostly on formal issues than about the content. I am not a native speaker, but as far as I can judge, the English of the manuscript is appropriate and fluent, well formulated, easy to read and understand. Literature cited broadly covers the area and provide a great insight of the backround and a comparision with the results: no problems revealed here. Data depository links and permission have been checked and found accessible and fine.

Specific comments
L96-97: ’but potentially with different microhabitat preferences’: What kind of potential differences in microhabitat preferences are known? It would be interesting and useful to give more detail on this here. In the discussion it is only mentioned but also without details. It may worth to detail or delete completely.  And what about mesohabitats (riffle, pools)? If differences in microhabitat preferences occur, that is usually reflected in mesohabitat preferences too, which may explain their different habitat preference for streams and springs.
L98-100: ‘In addition, riffle beetles are considered as a good indicator of water quality and perhaps also of climate change (Elliott, 2008), so our study can also provide valuable data for biodiversity conservation.’: It would be worth considering deleting this sentence. In general, and in my opinion, it interrupts the thread. I would definitely do so, of or move it to discussion.
L110: ‘Carpathian Arch’: In the abstract the authors used ‘Arc’. Both can be fine and correct but should be unified throughout the manuscript.
L115-118: It would be useful to include at least some basic numbers here allowing the readers to have an idea about the number of sites without interrupting reading and without checking the figure caption.
L130: ‘which was permitted on the basis of the permit issued by’ please consider rephrasing this.
L250: L. perrisi should be italics

Table 1: I suggest moving this table to supplementary material, it is not essential to include it to the main part.

Figure 1 (map) It must be done again because of mistakes in the inlet map. Austria and Greece are completely missing, such as Russia at the right top corner and also the Kaliningrad region. Also suggested to indicate the area of the bigger map on the inlet using a black rectangle. It would be more informative if streams and springs can be distinguishable by two colours.

Figure 4: It seems to me that the colour shades are not the same for identical values comparing the two parts. It would be better unified with the same colour coding.

Figures, general: It would be useful to give more self-explaining captions, especially where the figure itself does not easy to understand. This would be of particular help to non-expert readers in understanding the main message if the caption pointed out what to really see. Especially true for Figure 4, 5 and 6.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Everything has been written above. No more 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: THE TALE OF SPRINGS AND STREAMS: HOW DIFFERENT AQUATIC ECOSYSTEMS IMPACTED THE MTDNA POPULATION STRUCTURE OF TWO RIFFLE BEETLES IN THE WESTERN CARPATHIANS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I congratulate the authors on the thorough revision. The manuscript has significantly improved both in terms of coherence and analyses. The ecological and genetic differentiation among the two species is much more convincing.  I recommend the manuscript for publication.

Not sure, but I believe the following paper might be useful when introducing the W Carpathian springs and their long term persistence (lines 57-64): Franko, O., Šivo, A., Richtáriková, M., Povinec, P.P., 2008. Radiocarbon ages of mineral and thermal waters of Slovakia. Acta Phys. Univ. Comen. 49, 125–132.


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

Input:
Title: THE TALE OF SPRINGS AND STREAMS: HOW DIFFERENT AQUATIC ECOSYSTEMS IMPACTED THE MTDNA POPULATION STRUCTURE OF TWO RIFFLE BEETLES IN THE WESTERN CARPATHIANS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have adressed all of my previous points raised in the first round of review. All the required information have been added, all mistakes and typos have been corrected. The text and figures have been improved significantly based on the detailed comments from all the three reviewers. Many parts have been restructured thus readability has increased. English also improved. I have no objection to acceptance of the manuscript in its current state.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No further 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: NEIGHBOURHOOD SOCIOECONOMIC CHARACTERISTICS AND BLOOD PRESSURE AMONG JAMAICAN YOUTH: A POOLED ANALYSIS OF DATA FROM OBSERVATIONAL STUDIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: This is an important finding. Neighborhood factors are still understudied and although cross-sectional, this work provides some important links. I have only minor points:
In line 88 you claim that BP ≥ 120/80 is “elevated blood pressure”. This low threshold (instead of a 140 SBP threshold for example) should be explained by studies which provide evidence for the clinical relevance and a better prognostic value than other cut-off values.
Please provide more information about missing data and the detailed multiple imputation process and also about the combining procedure.
Please provide information whether you screen for uni- and multivariate outliers which may bias result.


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: NEIGHBOURHOOD SOCIOECONOMIC CHARACTERISTICS AND BLOOD PRESSURE AMONG JAMAICAN YOUTH: A POOLED ANALYSIS OF DATA FROM OBSERVATIONAL STUDIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is an exceptionally well-written and well-analyzed paper on the association between neighborhood SES and blood pressure in Jamaican youth. The data are a bit old but this is one of the very few papers ever published on this topic from that part of the world. All things considered, my evaluation is very positive.
Experimental design: This is an observational study. Existing data were used. Two different data sets were combined.
Validity of the findings: I would like to see replication of the findings in each data set. As the two data sets are different in most characteristics , I am afraid that some of the results may be arbitrary and due to the combining two data sets. Thus, we need to see a paragraph on whether the authors could find identical results in each data set or not.
Additional comments: Overall, the paper is very strong. There are a few comments to enhance the paper:
There is a literature in the US and Europe which is above what Ana Diez roux has done. Diez Roux has done very strong work but there are also other part of the literature which is missing in this paper. Violence victimization and fear of unsafe neighborhood as well as physical and social aspects of neighborhood all correlate with exercise, BMI, and cardio-metabolic risk, which can inform the arguments made in the discussion of this paper. Another part of the literature that is not engaged here is the density of healthy food / fast-food stores and tobacco and liquor stores, all having implications for blood pressure of the individuals and populations.
The results are all based on gender/sex stratification. This should be justified well in the background and methods and also be reflected in the title of the paper. What happens to the models if you run sex/gender as interaction rather than strata?
The graphs are all one type, and may not best present the data. Currently it is difficult to see the gender differences in 1 graph. Please consider other alternatives that may better show some of the interactions between gender/sex and the associations of interest.
Finally, two distinct data sets were combined. Why a variable reflecting the data set was not controlled in the modeling? A nominal instrumental variable that reflects the study / year.


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: NEIGHBOURHOOD SOCIOECONOMIC CHARACTERISTICS AND BLOOD PRESSURE AMONG JAMAICAN YOUTH: A POOLED ANALYSIS OF DATA FROM OBSERVATIONAL STUDIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript ‘Neighbourhood socioeconomic characteristics and blood pressure among Jamaican youth: a pooled analysis of data from observational studies’ covers an interesting and relevant topic, for which there is limited evidence in Jamaica.
The manuscript is clear, well-written, and very easy to follow. Yet, there are a number of issues that should be addressed before publication:

ABSTRACT:
L44: ‘associated with higher systolic BP (β +2.6 [1.0, 4.2], p<0.01’ – Please remove the plus sign (‘+’)

INTRODUCTION
L75: The introduction lacks the rationale for the study. The authors refer that their study is needed because there is no evidence about Jamaica. Yet, it is unclear what makes Jamaica different from other contexts where this topic has been extensively addressed. Please add a few sentences about the added value and novelty of this study. Finally, the focus of the study on youth population should also be justified.
L74: I also recommend the authors to refer that neighbourhood deprivation has been associated not only with blood pressure but with a series of other biological markers. Please check the papers by Ribeiro et al (https://www.ncbi.nlm.nih.gov/pubmed/29843403, https://www.ncbi.nlm.nih.gov/pubmed/31217447)
L63: Finally, although the authors briefly describe how neighbourhood SES may influence health, this section is too brief. I strongly recommend the authors to describe into more depth the mechanisms (psychosocial, material, behavioral) neighbourhood deprivation may influence blood pressure specifically.

METHODS
L113: ‘data on the built environment…’ - since this study does not rely on build environment data, this sentence can be removed.
L130 onwards: Many details on the neighbourhood-level variables and its geographical scale are missing. Please add a supplementary table describing all the neighbourhood level variables that were used, together with information on the scale (type of administrative unit, and corresponding average area and population size), date of data collection and data source. Also, they should explain why they selected that specific set of community-level socioeconomic variables. Previous studies on deprivation index construction tend to make the first selection based on data availability and based on theoretical constructs (please see: https://jech.bmj.com/content/70/5/493)
L138: The authors mention their territorial unit of analysis is the community-level. Yet, this is not enough as the term ‘community’ means different things across different countries and regions. Please explain how many communities exist in Jamaica, provide data on their area and population size (mean and range) and refer to whether they are homogeneous or heterogeneous in terms of SES composition.
L152: The authors refer to a previous community SES classification by Mullings et al (2013). Please explain why they did not use this previous classification and how it compares the classification obtained in this study.
L181: The authors refer they tested for the presence of interactions. Please clarify how this was tested and which interactions are they referring to: multiplicative or additive? Also, since the studies are quite different, is there any interaction between the three studies? Is the effect of deprivation on blood pressure the same across these three population samples?
L198: ‘…estimate the effects…’ – The avoid using terms like ‘effect’. This implies causality, which cannot be ascertained in a cross-sectional study. Check the entire manuscript.
L203: Please clarify the concept of ‘crossed-effects models’. I believe this is not familiar for most of the readers.
L208: The authors performed multiple imputation to deal with missing data. There are some points that should be clarified. First, please explain how multiple imputation reduces potential bias (mentioned in 216); since missingness does not seem to be at-random (‘significant difference in the proportion of persons within tertiles of the second PCA SES’), this idea should be further expanded. Second, it is important to provide a table (as supplementary table) with the list of variables and corresponding percentage of missing values that were used for the imputation procedures. Finally, I highly recommend the authors to run sensitivity analyses based on the non-inputed dataset, to show that their results and conclusion are not driven by the imputation procedure. This can be in supplementary material as well.
L231-235: I do not understand the added value of this analysis. Please remove or clarify.

RESULTS
I do not understand why the authors keep showing results for the community-level variables that were merged in the SES-indexes. Since their focus is on the community SES index (at least in the abstract authors only present results for the associations with the index), I highly recommend using those two variables, instead of its components. Or, if their target is not the SES-index, then, these individual variables should be thoroughly described and the rational for their inclusion as isolated factors should be carefully described.
L289: Also, the authors describe associations between blood pressure and individual-level variables like age, BMI etc. Since this study is focused on community level SES and its influence on blood pressure, this type of description should be removed.
L308: (β +2.6 [1.0, 4.2], p<0.01 for middle vs. lower tertile) – Please remove the plus sign for the beta coefficient,

TABLES
In my point of view this manuscript has an excessive amount of tables, probably because they present the associations and comparisons for all the variables of their dataset instead of focusing on the main community-level SES determinants. If possible, I recommend the authors to reduce the number of tables.

FIGURES
I do not see the point of figure 5 and 6 and corresponding analysis. Also, from these figures (whose y-axis is not comparable), it looks like the association between SBP and SES is stronger in women.

DISCUSSION
L367: Please provide a plausible explanation on why the effect of community SES is stronger among men. There are a number of papers about gender differences in neighbourhood effects.
I miss a discussion on why no association was observed for diastolic blood pressure.
L403: Please include the % participation of each study.
Experimental design: Presented above
Validity of the findings: Presented above
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: NEIGHBOURHOOD SOCIOECONOMIC CHARACTERISTICS AND BLOOD PRESSURE AMONG JAMAICAN YOUTH: A POOLED ANALYSIS OF DATA FROM OBSERVATIONAL STUDIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: shown in General comments for the author
Experimental design: shown in General comments for the author
Validity of the findings: shown in General comments for the author
Additional comments: The manuscript has significantly improved since its last version and my concerns have been addressed. However, before publication a couple of issues (listed below) need to be considered:

PAGE 13: ‘Correlation coefficients were -1.5 for females and -1.4 for males’ – Correlation coefficients vary from -1 to 1. Thus, this sentence has to be revised/clarified.

PAGE 19: ‘…therefore used linear splines in the bivariate and multivariable analyses…’
This new version of the manuscript uses splines to categorize the 2nd component of the SES index (I am personally not familiar with this statistical technique). This method has to be fully described and justified in the methods section, otherwise, it is very difficult to understand the results section.

TABLES:
In the second row from Tables 3 and 4, the authors refer to PCA SES Component 1 (z-score) but I believe they are referring to Component 2.

In my opinion, this manuscript still has an excessive amount of tables.


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: VALIDATION AND CLINICAL APPLICATION OF A TARGETED NEXT-GENERATION SEQUENCING GENE PANEL FOR SOLID AND HEMATOLOGIC MALIGNANCIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Use of English throughout the manuscript needs improvement by the authors. The manuscript as submitted is difficult to understand in parts
e.g. Abstract section - ’The more repeated variant across GI and lung tumors were KRAS G12D/V/C.’
And
Line 19 - A crescent number of biomarkers are progressively required to characterize the molecular profile of a specific type of tumor or to administer targeted therapies (Morganti et al., 2018)
I recommend that the authors ask a native English speaker to review and re-phrase where required throughout the manuscript

Variants where described should follow HGVS guidelines for nomenclature throughout the manuscript. HGVS nomenclature is the accepted standard for variant identification - – see https://varnomen.hgvs.org/recommendations/DNA/.

I do not understand why read depth is expressed as kbp, this is not a standard measure of read depth in NGS sequence files where depth is expressed as 'N'x

The reference to Williams HL et al 2018 on line 315 is cited incorrectly using multiple author names
Experimental design: The paper is titled as a validation of a methodology. Clinical validations should include a test design specification with estimates of test sensitivity, specificity and where appropriate limit of detection arising from the validation and whether these met the design specification. There is no consideration of this in the manuscript. I feel it is essential to include these aspects in the manuscript.

The M&M section (Lines 54 – 179) are more detailed than I feel is needed given that the primary methods used are primarily manufacturer's standard protocols. I question whether this section needs to be so detailed.
Validity of the findings: I cannot agree with the authors conclusions in the Abstract (see quotation below) as the assay failure rate is unacceptably high.

‘Together, an appropriate validation of the TsT26 panel has granted a good application into the clinical routine by providing several relevant and potentially targetable variants across multiple FFPE tumors.’

The assay as described in the manuscript has a high sample inadequacy/failure rate of 1/3.  In my opinion a 30% failure/sample inadequacy rate is incompatible with an assay for clinical application.

No explanation of the discordant results from the 48 reference samples tested across all 3 sites is given, the fact that the kit gives discordant results between the gold standard test and the TST26 for several samples e.g. 1-5, 3-4 & 3-11. The discordant results should be discussed and explained. From the data given a low VAF may explain the failure to detect KRAS variants with the gold standard method in 3-4 and 3-11 but no explanation of the differences between the two different methods is given which I feel is essential.
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: VALIDATION AND CLINICAL APPLICATION OF A TARGETED NEXT-GENERATION SEQUENCING GENE PANEL FOR SOLID AND HEMATOLOGIC MALIGNANCIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I carefully read the manuscript "Validation and clinical application of a targeted next generation
sequencing gene panel for solid and hematological malignancies".
This work is focused on demonstrating the applicability of the TruSight26 panel in the clinical setting. Although using the panel in this context requires several quality checks, the Authors were able to sequence two thirds of the samples subjected to the analytical workflow detecting 372 variants, 80% of them were tightly linked to potential FDA-approved clinical actionability, such as BRAF mutations V600 in melanoma and EGFR tyrosine-kinase domain variants in NSCLC.

The manuscript is clearly written, and the literature referenced is relevant and updated. Methods are described with sufficient detail and information to replicate them.
The topic addressed in the paper is of great interest to readers, and although several authors published on the applicability of the TruSight26 panel in the clinical and diagnostic field (Swati Garg et al., 2020. J Mol Diagn. 2020; Fisher KE et al., 2016. Journal of Molecular Diagnostics 18:299-315), the paper gives an important and useful contribution.

I believe this manuscript may represent a useful study for the future diagnostic application of the TruSight26 panel in diagnostic, which deserves publication after a revision.

Minor comments

•	The English language and punctuation should be improved to ensure a clearer understanding of the text.  Some examples:lane 309-311 ” Although the TsT26 panel lacks from the study of the gene TERT, BRAF and NRAS were the more frequently mutated genes in melanoma samples, as supported by others”; lane 324-325 “Indeed, the more validated NGS studies following its application in the everyday practice, the better the way to integrate the NGS technology into the clinics”.. the current phrasing makes comprehension difficult.
•	In the Abstract, Methods section is reported “tumors types”or tumor types?
•	Page 5, lane 13. Statement “On the other hand, the cost-effectivity..”: cost-effectivity or cost-effectiveness? Please, correct it.
•	Among the supplementary files there is only the data S2 file. The data S1 file is not available.
•	Page 10, lane 125. Statement “300x or greater for a single amplicon”: “At least 400 quality reads are necessary to detect a heterozygous variant with 99.9% sensitivity in a cancer specimen containing 10% neoplastic nuclei (Lin M.Tet al., 2014. Clinical validation of KRAS, BRAF, and EGFR mutation detection using next-generation sequencing. Am J Clin Pathol. 2014;141:856–866)”. Authors should kindly add a comment on this different coverage threshold.
•	Materials and Methods section: Several articles of the Material and Methods section are not listed in the References section. Please check it.
•	Page 13, lane 185-186. Statement “Sample 1-5 variant G12A was not detected and samples 3-4 and 3-11 were identified as variant detected, respectively as G12S and G12V…”. How do you justify the differences between the centers with respect to samples 1-5, 3-4 and 3-11?  Authors introduce a comment, please?
•	Page 14, lane 214-216. Statement “Thirty-seven samples did not undergo DNA quality assessment, 5% of them resulting in a NGS fail, 3% in detected variants and 1% in not detected variant (Table 4)”. Samples that failed the quality controls and were not sequenced or were sequenced with poor results had particular characteristics? In the work of Kevin E. Fisher et al., 2016 has been reported that a delta qCT value < or = to 6.0 is a practical adequacy requirement for TST library preparation and that the most of the specimens that failed library preparation were fine-needle aspiration samples, biopsy specimens, or body fluid cytospin cell blocks, then tissue and/or nonuniform sample. I would suggest the Authors to add a comment on the samples that have not generated sequenceable libraries.
•	Page 15, lane 227-228. Statement “Thirty-seven runs were done during the clinical implementation, 17 employing v2 300-cycle and 20 using v3 600-cycle sequencing chemistries”. The Authors should comment briefly on whether or not they found differences in sequencing quality using the two chemistries.
•	Page 15, lane 238-241. Statement “The mean coverage of AKT1 exon 2, STK11 exons 1 and 6 did not satisfied the minimum coverage of 1000x required by the panel. In addition…”. How did the authors decide to analyze the exons of the genes that did not satisfy the minimum coverage of 1000X?
•	Figure S3: It is necessary to add a legend to figure S3 in order to make it legible and to better understand its meaning.


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: VALIDATION AND CLINICAL APPLICATION OF A TARGETED NEXT-GENERATION SEQUENCING GENE PANEL FOR SOLID AND HEMATOLOGIC MALIGNANCIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: This is a re-review of a manuscript which on first review amongst other things, I felt needed improvement in the use of English by the authors who I accept are non-native English speakers. Although the authors have made some improvements to phrasing of points I highlighted in my first review there continues to be tracts of text that are difficult to follow. I understand that there is a PeerJ service for English proof-reading and editing, I recommend that the authors use this service to improve the readability of the whole manuscript.

I have highlighted several English and typographical errors below to illustrate this point however there are too many to list all of these here

Lines 228/9
Regarding the varied tumor types, the most abundant consisted in gastrointestinal (GI)
I suggest should read
Regarding the varied tumor types, the most abundant consisted of gastrointestinal (GI)

Line 231
cancer types were limited in number (Table S3). Overall consisted  in biopsy specimens, surgical
I suggest should read
cancer types were limited in number (Table S3). Overall the sample set consisted  of biopsy specimens, surgical

Line 251
whereas not detected variants or a wild type genotype was found in 26% (69 samples)
I suggest should read
whereas in 26% (69 samples) variants were either not detected or a wild type genotype was found

Line 252
The major number  of detected variants was observed in TP53 (28%), KRAS (16%),
I suggest should read
The highest number of detected variants was observed in TP53 (28%), KRAS (16%),
Experimental design: The authors have taken on board my comments from the original review and included further details of the assay sensitivity and specificity. The revised manuscript benefits from this.

I am now happy with the experimental design
Validity of the findings: The authors have taken on board critical suggestions from my first review on the clinical utility of the assay considering the high failure rate of teh assay the authors have also commented and provided more explanation of genotype discordances between the TsT26 assay and the reference assays for KRAS variants.

I am now satisfied with the validity of the findings
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: VALIDATION AND CLINICAL APPLICATION OF A TARGETED NEXT-GENERATION SEQUENCING GENE PANEL FOR SOLID AND HEMATOLOGIC MALIGNANCIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: NO comment
Validity of the findings: NO comment
Additional comments: The authors responded adequately to the referees' requests, in my opinion the manuscript can be accepted in the current form.


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

Input:
Title: ATTENTION BEHAVIOURS BUT NOT PAIN-RELATED BEHAVIOURS ARE MODIFIED BY THE PRESENCE OF A TWIN IN LAMBS UNDERGOING CASTRATION BY RUBBER RING
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is concisely written, and the format and data submitted meet the standards of PeerJ. There are a few areas where clarity of the reporting could be improved.

1.	Were both members of all pairs observed? The description of treatments (lines 82-83) makes it sound as if only one individual from the heterogeneous pairs was considered as an ‘observer’ and one as an ‘actor’, but Tables 3 and 4 indicate that all 48 lambs were included in both.
2.	Some of the terminology used may not be the most appropriate. The term “social facilitation” is used in the abstract only, and the term “social transmission” elsewhere; both of these, in my experience, are used to describe an increase in performance of a behaviour due to presence of or performance by conspecifics. Since you are also looking at decreases in performance of certain behaviours through buffering, this is a little confusing. The label “pain avoidance” behaviours is also unusual – the behaviours listed are common indicators of pain, but do not necessarily help the animal avoid pain. The term “pain related behaviours” used in the title is preferable.
3.	A little more discussion to place this in context would be helpful. For example, what does this add to what was known from the Guesgen et al. study mentioned in the discussion? Is there other evidence of these phenomena in grazing animals? More information/elaboration on the ideas raised in the introduction would help clarify your aims and use of these terms. Rault’s review of social support may be useful.
4.	The stated aim also does not really cover effects in both directions. A clear statement of predictions is desirable.
Experimental design: I have a few concerns regarding the experimental design, as follows:
1.	The rationale for the choice of treatments is somewhat unclear. It appears that you could test whether social buffering OR contagion occurs, but it would be difficult to say which because there is no true control without any social effect. The degree to which these effects can be tested depends on how the partners in heterogeneous pairs were used (see question above); no explanation is given for what you intended to test by including the non-castrated actors. Was social contagion expected in non-castrated animals?
2.	If only 3 sets of each type of heterogeneous pair were used (1/cohort), is this enough to draw inferences about those situations?
3.	Is there evidence to support the use of number of ear movements for this purpose? And is 1 min of observation sufficient?
4.	Line 97 – Was this always the same time post-procedure?

Appropriate consideration was given to randomization and pen effects, and it is good to see use of blinding.
Validity of the findings: 1.	The stated aims were to see if social effects decrease distress and reduce predation risk (line 59). However, these are not directly returned to in the discussion. The use of these measures to make inferences about distress was not fully justified, and any link to predation should be explained for these specific results.
2.	The analysis does not appear to control for age (unless this is the meaning of “day”?) although there is a large range. Could any environmental factors such as weather have influenced results?

Conclusions were well stated.
Additional comments: 1.	What was the aim of using only twins, given that most received the same treatment? The Discussion suggests relatedness may be important but it is not clear if this was intentional, or whether it differs from other work.
2.	Line 68 is missing punctuation.
3.	Line 94 was duration of this manipulation similar?
4.	Was reliability of counting ear posture changes checked, given the difficulty in observing postures?


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: ATTENTION BEHAVIOURS BUT NOT PAIN-RELATED BEHAVIOURS ARE MODIFIED BY THE PRESENCE OF A TWIN IN LAMBS UNDERGOING CASTRATION BY RUBBER RING
Review round: 1
Reviewer: 2

Output:
Basic reporting: This work is original and within the aims and scope of the journal. The paper studied the effect of grouping castrated lambs either with castrated or non-castrated twins to examine the effect of social grouping on modifying the pain-related behaviors. This research adds more information about the theory of social and emotional contagion. However, observing the behavior of animals alone is not enough to answer the research questions. The paper is not well written and missing important information to judge the obtained results. For example, as it stands the materials and methods are very difficult to read and it is not clear exactly what the authors are trying to research. The conclusion needs to be more succinct and focused on the purpose of this study. The authors should be careful in their conclusion since they had insufficient data for analysis and low frequencies of some behavioral patterns. There is no discussion of the limitations of the study, although there are many, particularly with regard to the recording of behaviors and missing data. Also, no results for interactions are reported in tables.
Experimental design: The way that materials and methods are written is very confusing and hard to digest. I suggest the authors rewrite it and provide a diagram or graphical abstract describing the experimental design. It is not clear how the research will fill the knowledge gap. Please provide a clear statement regarding the identified research gap.

Here are more detailed comments.

Introduction:
L44: Please provide a reference for your statement
L49: Please provide more details about social contagion for readers who are not familiar with this theory. I suggest that you provide more detail regarding emotional contagion such as Hild et al. (2011), and social buffering (Da Costa et al. 2004)
L58: It is not clear how the research will fill the knowledge gap. Please provide a clear statement regarding the identified research gap
Materials & Methods:
L72: Please provide more detailed information about animals such as age, BW at the beginning of the experiment. What are the criteria used to identify animals for this experiment? Please clarify?
L76: You had lambs with different ages. How you adjusted for age difference in your treatment groups?
L79: What is the difference between pens and treatment pens. This is very confusing and hard to digest. Previously you mentioned that 16 lambs were housed in a pen and here you are saying 2 ewes with their twin. I suggest the authors provide a diagram or graphical abstract describing your experimental design
L83: How authors identified which lamb observing which? How did you decide which lamb will be castrated and which are not?
L91: Change the 60s to 1 minute
L92: Which industry practices, please provide the reference
L96: What do you mean by “hand-held real time recording”?
L97: Which behaviors were recorded?
L102: How the ear posture was assessed and which references where used?
L106: Which type of markers used for the lambs?
L107: How many observers recorded the behavior of animals?
L108: How is the behavior observed for 5 hours after treatment? Which recording method was used? Please provide more detailed information about behavior recording and observation
L109: Pleases move the references following “previous studies”
L110: Which husbandry procedures? Please clarify
L114-115: Where are these criteria came from? Where are your references?
L105-116: Clear description of the recording of behavior data should be provided. For example, how is the output from the cameras was recorded and how many observers recorded the behavior of each animal. How you counted the posture of animals and avoidance behaviors? Is any software used for behavior recoding or it done manually? The behavior recording recorded in this study was not accurate and is insufficient for answering your research question.
Table 1: What is “No.” stand for, I guess it the number of. What is the purpose of providing abbreviations in the table for the ethogram? Please provide references in the table for measured behavioral patterns.
L125: Please specify what kind of model used, linear what? I suggest the author explore the effect of age in the model since the studied lambs had different ages.
L127: Specify what behavior data required normalization and how you did it?
L130: Here you mentioned that you calculated the 95%CI but there are no data reported in tables
L125-131: Please specify what significance level used to report treatment differences.
Validity of the findings: Overall, the data support the research question. Some questions need to clarify for example:

How as the data treated after obtained and what "sum of time for each behavior" means, is it total duration or bouts? Was the correlation between parameters examined? if so, how was it addressed? Did the author consider confounders such as animal personality in their models?

L141: This word doesn’t make sense “at the would site”.  Did the author want to say “wound” instead of “would”?
L142: Where are the interaction data. Please add these data to tables
L146: “no significant interactions” with what?
L201: Behavior explicated by chickens may not exactly comparable to the behavior of sheep. I suggest that the author cite relevant references from the same species being studied.
L212: Provide reference, please
L226-230: This section should move to materials and methods. Regarding the handheld video recording, the general practice is to have cameras installed in the pen instead of being physically present which is interfere with the normal behavior of animals. I have a concern that the reported results could have been modified in the physical presence of observers.
Conclusions:
From the outcome of your research, it is not enough to make the current conclusion. Please rewrite.
Tables: Check the fonts for table headings. Add the results for different interactions tested in the model.
Additional comments: See above


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

Input:
Title: ATTENTION BEHAVIOURS BUT NOT PAIN-RELATED BEHAVIOURS ARE MODIFIED BY THE PRESENCE OF A TWIN IN LAMBS UNDERGOING CASTRATION BY RUBBER RING
Review round: 2
Reviewer: 1

Output:
Basic reporting: The article now meets the journal's standards.
I would suggest clarifying in the introduction (as in the response to me) that the Guesgen et al. study actually showed pain effects on number of ear posture changes, not just the more familiar measure of different postures, to better justify the method here.
Experimental design: This does address an gap in research related to social context effects on buffering and/or contagion.
Validity of the findings: Conclusions regarding social buffering could perhaps be more clearly expressed, since the effects of presence of a twin in itself could not be tested here (because all subjects had a twin present, and ewe, which was the most welfare-friendly experimental design), and that is the typical social buffering paradigm. The MS as a whole I think should discuss more explicitly whether greater buffering effects should be expected if the companion is pain free themselves, which seems to have been one of the predictions. This was partially set up in the Introduction but never made explicit that I can see.

Other than that, conclusions are now appropriately limited and data and analysis seem sound.
Additional comments: Good work on the revisions. The MS is now much clearer and more logical.

Note that although you have changed "pain avoidance behaviours" through the text, you do not appear to have done so in the Table captions.

At line 249, an increase in "postural behaviours" does not make sense. I think what you mean is postural changes?


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: ATTENTION BEHAVIOURS BUT NOT PAIN-RELATED BEHAVIOURS ARE MODIFIED BY THE PRESENCE OF A TWIN IN LAMBS UNDERGOING CASTRATION BY RUBBER RING
Review round: 2
Reviewer: 2

Output:
Basic reporting: The paper is too much improved, and authors have addressed all comments. The manuscript looks good to me and ready for publication. Just minor changes to be addressed:

1-    Consider providing more information to figure 1. The figure should stand on its own. It will be nice to have pictures of lambs in this figure.
2-    Don’t need an abbreviation column in Tables 2 and 3.
3-    Consider making table 1 supplementary material.
4-    Please consider presenting 95% CI in a separate column instead of having them in parenthesis, and use ± SE.
Experimental design: None
Validity of the findings: None
Additional comments: None


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: ELEVATION OF MPF AND MAPK GENE EXPRESSION, GSH CONTENT AND MITOCHONDRIAL DISTRIBUTION QUALITY INDUCED BY MELATONIN PROMOTES PORCINE OOCYTE MATURATION AND DEVELOPMENT IN VITRO
Review round: 1
Reviewer: 1

Output:
Basic reporting: The current study by Zhao et al. demonstrates the beneficial effect of melatonin supplementation on porcine oocyte maturation in vitro. They report biochemical changes due to melatonin treatment including changes in GSH levels and mitochondrial distribution which are known to be beneficial for oocyte quality and fertilizability and verify the beneficial effect on oocyte developmental potential. Finally, they show that melatonin (particularly at a concentration of 10-9 mol/L) treatment correlates with significant elevation in the expression of MPF and MAPK, both of which are critical for oocyte meiotic progression and maturation. The important conclusion from the study is that 10-9 mol/L Melatonin supplementation is an ideal condition for in vitro maturation of porcine oocytes, an insight that can be of relevance to the animal biotechnology industry.

The study is appropriately designed and amply supported by references to existing literature in the field. One potential area for improvement is the quality of the writing. It requires significant editing to get rid of errors and to make the article more comprehensible to the reader. Examples: the use of words such as ‘furtherly’, ‘ovary maturation’ instead of oocyte maturation in first sentence of introduction, very long single sentences (e.g. line 26-32), and multiple typos and errors all through the text (e.g. line 194: the word ‘difference’ is missing). Also, the abstract itself is very long and repetitive – it would definitely help to have a simpler and more compact abstract.
Experimental design: The research question has been suitably defined and it draws a specific conclusion about the specific concentration of Melatonin which is most beneficial for maturation of porcine oocytes.
Validity of the findings: The beneficial effects of Melatonin described are correlational and the authors rightfully state this in the text. The findings are within the scope of the study, appropriately stated and supported by the experimental results and statistical tests.
Additional comments: Major comments:
Even though the authors have extensively mentioned existing literature and context for their work, it’s important to note that they have not cited Yang et al., 2020 (Effect of Melatonin on the In Vitro Maturation of Porcine Oocytes, Development of Parthenogenetically Activated Embryos, and Expression of Genes Related to the Oocyte Developmental Capability). This recent paper appears to be from the same (or related) research group with three authors common to both studies. This is important because, the previous study and results overlaps to some degree (beneficial effect of melatonin on GSH levels, mitochondrial distribution and parthenogenetic activation) with the current manuscript. Keeping that in mind, the two main findings exclusive to the new report are the effects on MAPK and MPF expression and the recommendation of the most beneficial Melatonin concentration of 10-9 mol/L.

Minor comments:
1. The current representation of statistical significance in the histograms and figures is very unconventional, using dissimilar/similar letters to denote significance/the lack of it. While this is not incorrect and serves the purpose, it can be a bit confusing to understand which conditions are being compared. A brief key is provided in the figure legends, but it will be better if the authors can include a couple of sentences explaining this in the ‘statistics’ section of Materials and Methods.

2. It would be nice if the authors would include in the discussion their view about why a higher concentration of Melatonin (10-6 mol/L) is not necessarily the best condition supporting oocyte health and maturation. One would expect a dose-response where the beneficial effects correlate directly with the dose of Melatonin. It’s possible that excessive Melatonin could activate feedback mechanisms that interact with other pathways thereby reducing effectivity.


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: ELEVATION OF MPF AND MAPK GENE EXPRESSION, GSH CONTENT AND MITOCHONDRIAL DISTRIBUTION QUALITY INDUCED BY MELATONIN PROMOTES PORCINE OOCYTE MATURATION AND DEVELOPMENT IN VITRO
Review round: 1
Reviewer: 2

Output:
Basic reporting: MPF and MAPK pathway have many genes. The author only analyzed the expression of one gene in this pathway, so the results have·low credibility. Just verifying the related single gene by PCR does not show that melatonin could affect oocytes through MPF and MAPK pathways
Experimental design: The overall experimental design of the paper is very simple and lack of logic. The quality of the figures is poor, and the figures cannot support the results of the paper.
Validity of the findings: The results of the paper lack innovative. There are many papers published on related research results (PMID: 32012669, 31773776, 31672358). This paper just repeated the relevant experimental results, but they are relatively low. Only the cleavage rate and blastocyst rate are not enough to explain the effect of melatonin on oocyte development
Additional comments: In general, the lack of innovation is serious, and the results 1234 are just repeating the results of previous studies. At the same time, there is a lack of sufficient data to support the problem that the experiment wants to explain. In addition, the coherence and logic of the paper are poor, and no related channel issues involved in the title are raised. This paper cannot meet peerJ's publishing requirements.


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: ELEVATION OF MPF AND MAPK GENE EXPRESSION, GSH CONTENT AND MITOCHONDRIAL DISTRIBUTION QUALITY INDUCED BY MELATONIN PROMOTES PORCINE OOCYTE MATURATION AND DEVELOPMENT IN VITRO
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised version of Zhao et al has improved from the original submission in several aspects. First, it has now included a highly relevant citation from recent literature and discussed their latest findings in context. The readability of the paper is also now significantly improved from the original version, thanks to language editing.
Experimental design: N/A as no new experiments were performed for this revision.
Validity of the findings: The authors have provided the raw data based on which they performed statistical tests and prepared their figures. They have also included a sentence about the style in which significance is assessed in their assays per the previous request.

As mentioned before, the beneficial effects of melatonin described are correlational as the authors only test the expression changes of two genes in a complex cascade. This is not necessarily problematic as the data is reported and presented as correlative, focusing instead on specific phenotypic effects of melatonin stimulation in combination with the gene expression analysis.
Additional comments: Potential area of improvement: The resolution of the images is really poor and it's possible that it is a consequence of the pdf generation process during or after submission. I would certainly recommend having images of much better resolution for the publication (Figure 1 and 2).

For example, from Fig 2, it is hard to see any detail in the mitochondrial network due to excessive signal intensity and poor resolution. Also, rather than just one example each of 'good' and 'bad', I strongly recommend:
a) Showing images from multiple oocytes for each melatonin concentration
b) Showing the range of phenotypes, as can be better appreciated from the original figures shared with us but not incorporated into manuscript.

Please make sure to include scale bars in all images for proper comparison. It looks like they may not have been acquired at the same magnification. Also, please make sure that the signal intensity scaling is done identically across all conditions, while preparing the figures.


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: ELEVATION OF MPF AND MAPK GENE EXPRESSION, GSH CONTENT AND MITOCHONDRIAL DISTRIBUTION QUALITY INDUCED BY MELATONIN PROMOTES PORCINE OOCYTE MATURATION AND DEVELOPMENT IN VITRO
Review round: 3
Reviewer: 1

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: Thank you for improving the quality of the figures and adding in details for clarity.


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: COMPARISON OF PEDIATRIC SCORING SYSTEMS FOR MORTALITY IN SEPTIC PATIENTS AND THE IMPACT OF MISSING INFORMATION ON THEIR PREDICTIVE POWER: A RETROSPECTIVE ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In their study “Comparison of pediatric scoring systems for mortality in septic patients and the impact of missing information on their predictive power” Christian Niederwanger and his colleagues evaluated different scoring systems used to assess and monitor children with sepsis. In their retrospective study the authors evaluated the medical records of 398 patients under 18 years of age with sepsis and apllied the following scoring systems: PRISM, PRISM III, PRISM IV, PIM, PIM2, PIM3, PELOD, PELOD 2. They found that in particular the PIM scores are helpful in assessing the severity and that missing data do not seem to compromise the prognostic power.
The article is structured according to the guideline of the journal. The literature cited is extensive. The abstract summarizes the important results of the study. The introduction is brief and informative and the statistical methods seem appropriate. Limitations are addressed. Figures and tables are informative.
Experimental design: The research questions are well defined.  The experimental design (retrospective review of existing medical data of a single institution and application established scoring systems) is straight forward but as eluded to in the limitiation flawed by the nature of a retrospective design and in particular incomplete data sets. It is interesting that the authors tackle this problem from the start head on and included the problem of incomplete data sets in their statistical analyses.

As far as can tell most scoring systems have been evaluated in much larger studies and in a prospective fashion so the overall novelty of the findings is limited.
Validity of the findings: The authors provided all the necessary data and discussed their findings in the context of the existing literature. Open questions are addressed.
The conclusion is very lengthy and should be shortened
Additional comments: I have several further remarks:

•	The article is overall well written and to the point apart from several wording issue and should be read by a native speaker.
(see Introduction for example, line 81: However, some patients develop certain life-threatening clinical pictures- please change to conditions etc;
line 100 Please change as follows: Also, the optimal timing for determining these scores in the clinical course picture of sepsis was evaluated in addition to the influence of the lack of data on the predictive value of the different scores.

•	Methods: the definition of children with sepsis should be briefly described.

•	The discussion is lengthy and could be more concise

•	Line 248: the authors compare the finding of their study with a large prospective australien prospective cohort study (Slater and Shann, 2004) which is not entirely correct and should be rephrased.


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: COMPARISON OF PEDIATRIC SCORING SYSTEMS FOR MORTALITY IN SEPTIC PATIENTS AND THE IMPACT OF MISSING INFORMATION ON THEIR PREDICTIVE POWER: A RETROSPECTIVE ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this study, the authors evaluated and compared the prognostic ability of several common pediatric scoring systems to determine which is the most applicable score for pediatric sepsis patients from timing of disease survey and insensitivity to missing data. The main findings were:
They found that PIM scores show comparatively good performance, are stable as far as timing of the disease survey is concerned, and the system is also relatively stable in terms of missing parameters. And PELOD 2 is best suitable for monitoring clinical course.
The work in general has been well carried out, and the results give a clear hypothesis regarding the pediatric scoring systems.


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: COMPARISON OF PEDIATRIC SCORING SYSTEMS FOR MORTALITY IN SEPTIC PATIENTS AND THE IMPACT OF MISSING INFORMATION ON THEIR PREDICTIVE POWER: A RETROSPECTIVE ANALYSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: Please explain the relationship between peak CRP and disease severity.
Please provide a flow chart in the methods section.
Validity of the findings: Whether the weight of missing data affects the predicted results more than the number of missingdata?
Additional comments: Overall the quality of the article is fairly good and provides the effect of missing data on the prediction results, which has clinical practical significance.


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: ARE GIANT CLAMS (TRIDACNA MAXIMA) DISTRACTIBLE? A MULTI-MODAL STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, there appears to be a strong emphasis of distraction (caused by stimulus) linked to predation throughout the paper. Though I would differ that distraction cues could affect organisms in other ways such as altered behaviour and stress that leads to reduced physiological functions (i.e. respiration, productivity, etc…). In my opinion, these are potential risks faced by organisms – whether in the form of being eaten up, or reduced growth. Since the authors did not specifically test the effects of predation based on the stimuli offered, I feel that they should include the studies examining other impacts, on top of predation in the Introduction.

Several statements made are not so clear and needs to be addressed. For example, Lines 49-54: “Attention is limited and divisible and because it is sensitive to stimuli in different modalities (Dukas 2004; Chan et al. 2010; Blumstein 2013), external stimuli can interfere with risk assessment by both masking biologically important signals (Zhou, Radford, & Magrath 2019) and distracting individuals, thus preventing them from focusing on avoiding predation (Rabin, Coss & Owings 2006; Karp & Root 2009; Chan et al. 2010).” – the context for attention was not explained earlier, so the link to stimulus is unclear.

Lines 62, 63, 96: The term ‘palps’ alone is a terminology describing appendages found in arthropods. I think the authors are referring to the ‘labial palps’ in bivalves? Please clarify and ensure the accuracy of information between Lines 62-66.

Line 71: Authors mentioned the lack of understanding on how anthropogenic noise affects bivalves, but 5 recent papers were cited (between Lines 71, 72). Suggest the authors briefly explain the outcomes from these studies, which would add value to this section and briefly answering how marine anthropogenic noise distract bivalves. Similarly, Lines 77-80 on the lack of studies should be nuanced, and instead highlight what exactly is the knowledge gaps after knowing that some studies have already been published.

Lines 81-89: Authors broadly suggest that both sound and water flow can alter water particle motion, but there is not much information to elaborate how do sound and/or water flow change water particles movement. Given that it is a major factor influencing how the stimulus reaches the giant clam, I feel more information should be given, with respect to the two stimuli in this study. Also, I don’t think water flow and water particle motion are the same, but the section focuses only on the former point.

Several statements made need to be properly referenced to support the points made. For example, Lines 88-89: “Flow changes could also indicate changes in threat level because it is one of many factors naturally associated with the presence of a moving predator.” – should be provided with a reference.

Lines 90, 96: Is it ‘Giant clams’ and not ‘Clams’? The latter term refers to a general group.

Line 98: Suggest to add “…could modify…”.

Line 103: Suggest to add “as a potential anti-predatory response” as mantle retraction could also be attributed to clearing of irritants such as sediments, or changing light levels (i.e. shadow responses).

Lines 104-106: It is not very clear to me how latency to fully close their mantles is an indication of distraction levels – needs to be better explained here. Another point is, under most circumstances, giant clams do not necessarily extend their full mantle capacity after each retraction. How do the authors ensure full mantle emergence/re-emergence?
Experimental design: Interestingly, the experiments were carried out with wild giant clams where the species is typically embedded in the shallow waters. While the authors had attempted to address the numerous variables under natural reef conditions (such as ambient velocity flow), I think there needs more clarifications from the authors. An illustration of the experiment will be useful.

1) How did the researchers ensure that their presence did not affect the outcomes of their study? For instance, I assume that the researchers had to be in-water to introduce the extended poles and cameras, so there could be some disturbance from researchers.

2) What was the general water depths at which the giant clams were found and/or experiments were conducted? How far apart were the giant clams between each other?

3) What was the general conditions of the day (e.g. sunny, cloud cover, waves, etc…)? Related to 2), both factors can result in shadows and refraction of water ripples that causes the giant clams to become disturbed by these natural factors. My concern is that light changes under natural settings can mislead the outcomes of this study. Even if objects are placed at a distance, the giant clams can perceive light at a good distance based on previous studies.

4) Authors to clarify in text whether all 5 boat sounds were played at random, or played to all individual clams?

5) The details of equipment specifications are critical in this study, in my opinion. For example, the running voltage of the aquarium pump, the sound speakers working frequency in Hz, etc… As these parameters could affect the water particles uniquely.

6) On the stimulus presentation for water flow, can the authors clarify the position of hose facing the clam? For example, was the hose facing near one of the siphonal openings, or a general central position, or random positions every time?

7) On the velocity measurements (Lines 128-130), can the authors clarify further if the measurement was taken at the point where jet exits the nozzle of pump or 15 cm away from nozzle? The released jet will dampen in velocity with distance, hence, the velocity reported needs to account for this reduction. This is surely more difficult to handle in the field.

8) Line 156: For the no stimuli presentation (i.e. controls), were the clams introduced/shown the hand-held devices, but switched off during presentation? It is not clear based on this line, as it could just be describing the types of treatments. This is particularly critical to eliminate the effects of ‘equipment’ influencing the giant clam’s mantle behaviour.

9) Lines 158-160: Rather than ‘acclimate’, perhaps the authors can refer to the clams being subjected to the stimuli? The former suggests getting used to the conditions, but it is not the case.

10) Since the study is likely conducted in the field, did researchers account for disturbance by fishes or macroinvertebrates? I note that mantle twitches were observed, but from past observations, these twitches could be due to amphipods running across the mantle. What does the mantle twitches signify here?

11) More details needed on the post-stimulus disturbance are required, such as which part of the mantle had contact with the eraser, and was the region consistent across all the clams? From experience, not all clams will respond to being disturbed, and depending on the intensity and duration, it can affect the latency measured.

12) On the latency of re-emergence of mantle, I’m not quite sure if I understood the equation and number of measurements. How did the researchers obtain 103 measurements, if there were 32 samples (multiply by 4 treatments)?
Validity of the findings: As I still have questions regarding the experimental designs, I am unable to accurately assess the validity of the findings. My comments mainly deal with the phrasing of Results and Discussions.

Line 222: I think it is misleading to say “increased the number of retractions” as the actual measure was number of mantle twitches. Suggest to use “higher number of twitches recorded…” instead.

Lines 229-244: The results in the table presented are post-processed data. Would it be possible for the authors to state down the actual timings (i.e latency) for ease of comparisons?

Lines 254-256: Yes, but it should be noted that mantle retraction as an anti-predator response is a complete and sudden valve closure. The study here measured mantle twitches and partial retractions, which do not necessary conform to an anti-predator response.

Lines 256-259: Any reasons to explain why anthropogenic noise such as motorboats distract the invertebrates? It will be good to add 1-2 lines to explain the rationale based on previous studies.

Lines 265, 307: What could this unisensory receptor be, in this case, for the giant clam?

Lines 266-268: Does this study refer to multiple stimuli distracting prey? As the former sentence implies the additive effect of 2 stimuli, rather than 1 stimulus. Similar to an earlier comment, has there been other studies showing that multiple stimuli rather than single stimulus distract animals, and why? It will be good to add 1-2 lines to explain the rationale based on previous studies.

Lines 279-280: Suggest to include references that show giant clams filter-feeding for nutrients.

Lines 272-289: I’m not convinced that the giant clams re-emerge more quickly due to the need for filter-feeding, but rather to extend its outer mantle for photosynthesis. The latter has been said to contribute to almost 90% of nutrients for the giant clams, and the remainder derives from filter-feeding. Hence, the role of filter-feeding is minimal relative to the need to allow their photosymbionts to photosynthesise. There are several research papers that have confirmed this interaction.

Line 293: I’m not very convinced that the study looked at anti-predator behaviour, as the stimuli presented do not well-represent potential predators.

Lines 293-299: Can the authors expand on how these anthropogenic noises affects the animals, for example, give some specific examples.

Lines 306-308: Can the authors elaborate more on the mode of sensory in giant clams? Like what organs/receptors and how do they detect stimulus? Please indicate references.

Lines 314-332: While I acknowledge the lack of information on the topic in invertebrate species, but I suggest that the authors at least keep the discussion to marine organisms for relevant context. The transmission and detection of stimuli in terrestrial environments contrast greatly with the marine environments, therefore, it is best to remove the terrestrial examples.

Line 335: A potential anti-predator behaviour is more precise.
Additional comments: Thank you for this intriguing work! It is great to read new autecology work for the giant clams, given the major assumption that these animals move very little. Overall, I have great reservations on the experimental design, thus the outcomes of the study may not be representative of the actual treatments. I hope that the authors can supplement more information regarding their experimental process (e.g. to include an informative illustration on how the study was conducted) and clarifications of the steps, so that a better assessment of the results can be made. A more general comment is the mantle retractions here was definitively placed as an anti-predator behaviour, but it is not precise as the behaviour can also refer to others such as clearance of debris and sediments, or macro-fauna present on their mantles. While the study is designed with anti-predator avoidance, the context should be broadened to acknowledge the other possibilities.


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: ARE GIANT CLAMS (TRIDACNA MAXIMA) DISTRACTIBLE? A MULTI-MODAL STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Raw data (i.e., actual data of frequency of mantle retractions, latency to close, and latency to re-open) should be reported as supplementary material. Please see attachment for additional comments and suggestions.
Experimental design: Some methods should be described in more details, for instance, how long were the video recordings, what time was the video recording done, how far were the giant clam individuals from each other. Please see attachment for additional comments and suggestions.
Validity of the findings: No comment.
Additional comments: No additional comments


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

Input:
Title: ARE GIANT CLAMS (TRIDACNA MAXIMA) DISTRACTIBLE? A MULTI-MODAL STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This study explores the effect of exposure to two stimuli – sound and flow – on risk assessment in the giant clam Tridacna maxima. The authors provide evidence for distraction (i.e., increased response time measured as latency to close) in clams exposed to both stimuli simultaneously suggesting that giant clams perceive these stimuli in an additive fashion. The authors also show that exposure to sound and flow (alone or in combination) led to increased frequency of mantle retractions. Overall, the paper is extremely well-written, methodologically sound, and data are presented in clear and appropriate detail. Taken at face value, the results are important and are worth publishing. However, after careful revision, I have identified two topics that I feel require further discussion or clarification. The first is in regards to the assertion of the palps as the sole sensory modality in detection of the stimuli used in this study. The second deals with the potential role of habituation. In addition to these two general comments, there are a few other, minor, issues (e.g., a need for expanded citation of relevant literature) that I list below. I hope my comments are useful to help improve the manuscript.

General Comments:
(1) Single Sensory modality - Can the authors supply a reference for the primary role of the palps in detection of particle motion in giant clams? There is a previous reference to Nedelec et al. 2016 as the source for this assertion (line 63), but there appears to be no mention of the palps as a sensory organ in this study. Documentation of this role is important as it underpins the author’s conclusion that the examined stimuli are additive and thus distractive to the clams. In addition, several studies have shown there is a strong dependence on visual cues in giant clams to avoid predation by fish (Wilkens 1986) and that particle motion and pressure stimuli do not elicit a response when these stimuli originate below the plane of vision (Stasek 1965).

Wilkens LA (1986) The visual system of the giant clam Tridacna: behavioral adaptations. Biol Bull 170:393–408.
Stasek CR (1965) Behavioural adaptation of the giant clam Tridacna maxima to the presence of grazing fishes. Veliger 8:29–35

Further, Soo and Todd (2014) describe a ‘sight reaction’ in tridacnids in which clams sense and respond to particulate movement with their pinhole eyes. This response is independent from other ‘shadow responses’ in that it is not dependent on changes in illumination. Taken together, these data seem to suggest that mechanical stimuli may not be the primary means of sensation in giant clams. This could have important implications for the author’s assertion that giant clams uniquely discriminate the investigated stimuli through a single sensor – the palps (lines 35 – 36).

Soo P, Todd PA (2014) The behaviour of giant clams (Bivalvia: Cardiidae: Tridacninae). Mar Biol 161, 2699–2717. https://doi.org/10.1007/s00227-014-2545-0

(2) The second topic that I feel the authors should expand upon is the potential for habituation to stimuli in tridacnid clams. Giant clams have been shown to exhibit reduced responses when exposed to repetitive visual stimuli suggesting they are capable of habituation (Fankboner 1981). This is also well-documented in the aquarium hobby where giant clams will quickly cease to exhibit both the ‘shadow response’ and ‘sight reaction’ if regularly exposed to nearby movement or passing shadows. The authors also cite their own previous work which includes investigation of the potential for habituation in tridacnids (Dehaudt et al. 2019). Given the close proximity of the Gump research dock to the study site, is it possible that clams used in this study had habituated to motor noise/boat wakes? In this case habituation to frequent nearby boat traffic could manifest similarly to behavioral “distraction” – i.e., reduced (or slowed) response to the multimodal sound/flow stimuli as observed in this study.

Fankboner PV (1981) Siphonal eyes of giant clams and their relationship to adjacent zooxanthellae. Veliger 23:245–249

The authors do account for repeated measures in their statistical analyses, but did the authors observe any trends in latency data as a function of number of trials conducted on an individual? Similarly, could significant differences between individuals (as reported for most response variables) be explained by proximity to boat traffic (i.e., distance from the boat channel) or other potential sources of habitual, repeated stimuli?

Specific Comments/Suggestions:
Title: Although an issue of personal preference, it is generally considered preferable that titles be explanatory rather than interrogatory. I suggest altering the title to more explicitly state the results of the study, especially in regards to the specific stimuli examined.
Line 48: Check extraneous dashes aren’t present in final copy.
Lines 56 – 59: Although I agree that the list of literature regarding tridacnid behavior is, in general, sparse, the authors’ list of references seems incomplete. Authors should appropriately cite the works I’ve referred to above (all of which summarize a suite of anti-predator behaviors in tridacnid clams) as well as work by Neo and Todd (2011) who discuss visual responses in tridacnids.

Neo ML, Todd PA (2011) Quantification of water squirting by juvenile fluted giant clams (Tridacna squamosa L.). J Ethol 29:85–91

Lines 60 – 62: Alteration of anti-predator behavior in response to chemical cues has also been shown in tridacnids specifically. See the work of Neo and Todd (2011) in which both latent defense (i.e., shell characteristics) and behavior (i.e., vertical movement) were altered in Tridacna squamosa in response to a predator cue.

Neo ML, Todd PA (2011) Predator-induced changes in fluted giant clam (Tridacna squamosa) shell morphology. J Exp Mar Biol Ecol 397:21–26

Lines 75 – 75: Sentence fragment needs revising.
Line 82: Replace second instance of “changes” with “change”.
Lines 94 - 96: Change “while” to “whereas”. Add a “,” between multimodal and giant clams. Remove second period at line 96.
Lines 112 – 113: Although not published under peer review (and therefore potentially not relevant for citation here), the authors may be personally interested in data from a recent predation-response study in the same population of giant clams in Mo’orea:
Boville E (2020) Look out: giant clam (Tridacna maxima) defense response to visual stimuli in Mo'orea, French Polynesia


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: ARE GIANT CLAMS (TRIDACNA MAXIMA) DISTRACTIBLE? A MULTI-MODAL STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No further comments.
Experimental design: An illustration to explain how the experiment was conducted will be useful. This has not been addressed in this revision.

Line 119: Please clarify what dimension does the diameter of the shell refer to? Is it the width of the entire animal?

Lines 141-142: Are these five sounds similar in pitch, amplitude, etc? While the sounds were randomly introduced, it would be good for Authors to add this detail on what makes these sounds different, or similar?

Lines 187-196: Thank you for clarifying that researchers were in-water (>1m away from the test clams) during the experiments. I strongly recommend Authors include these details here, as well as to explain how they had added a 60s buffer to acclimate giant clams to their presence.

Linea 181-182: Please add detail that these 16 events were taken out and not analysed subsequently.
Validity of the findings: Lines 329-347: Thank you for clarifying on that multi-attribute studies on marine organisms are limited. This should be mentioned in the final paragraph. As much as terrestrial examples are useful, but it’ll be better for Authors to try and summarise these findings and not overwhelm the narrative that multi-attribute studies on marine organisms.
Additional comments: Thank you for the revisions and responses to my comments. I have a few more comments, but overall, well done on the revisions!


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: DESCRIPTION OF A NEW MEMBER OF THE FAMILY ERYSIPELOTRICHACEAE: DAKOTELLA FUSIFORME GEN. NOV., SP. NOV., ISOLATED FROM HEALTHY HUMAN FECES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript was written in clear English and the structure of the article conforms to an acceptable format of PeerJ.  However, sufficient Background/Introduction was not provided and was only within reach of some specialists.  The authors need to make a significant revision of Introduction for broad readers.
Experimental design: see below
Validity of the findings: see below
Additional comments: Ghimire et al. described the isolation and physiological characterization of a new member of the genus Erysipelatoclostridium species isolated from human feces, and they proposed it as a novel species Erysipelatoclostridium fusiforme sp. nov within the family Erysipelotrichaceae.  This is a fairly straightforward paper describing a novel species in the genera Erysipelatoclostridium within the family Erysipelotrichaceae.
Overall, experiments related to the phenotypic and chemotaxonomic analyses are well designed and well conducted. Nevertheless, there are some critical concerns that must be addressed.  Some major comments are shown as follows.

1. This manuscript is too descriptive to understand the importance of this study for broad readers, though the authors performed phenotypic and chemotaxonomic characterization according to a conventional manner of International Journal of Systematic and Evolutionary Microbiology.  The authors should add effective discussion about physiology and ecological role of the isolated microorganism in human gut.

2. The authors rarely discuss about the result of genome sequence of the isolated strain.  Moreover, the quality of the genome sequence is low (i.e., 146 contigs and 2.4Mbp), while the relative strain (Erysipelatoclostridium innocuum) consists of 4.8Mbp genome. Therefore, the authors should conduct additional genome sequencing and comparative genome analyses.

3. Cell morphology of strain SG502T is still unclear, since Figure 1 includes some different-shaped cells other than a rod-shaped cell.  Cell morphology is one of the most important indicators of taxonomy. Therefore, another micrograph such as transmission electron micrograph and phase contrast micrograph are highly required.  Does this isolate form spores?

4. The authors should submit additional figure of MALDI-ToF and discuss about the result.


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: DESCRIPTION OF A NEW MEMBER OF THE FAMILY ERYSIPELOTRICHACEAE: DAKOTELLA FUSIFORME GEN. NOV., SP. NOV., ISOLATED FROM HEALTHY HUMAN FECES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The genus name Erysipelatoclostridium has not been listed in the Approved Lists of Bacterial Names (Bergey’s Manual). (LPSN bacterio. net)
It is required to describe the novel species with a proposal of a novel genus including closely related species properly.

Expressions for the taxonomical terms should be improved.
Experimental design: The novel species is proposed based on the unvalidated genus name. Thus, the authors should check the valid names of the closely related species and consider how to propose the novel species (or genus) name validly.
Validity of the findings: Basic characterization of the novel strains was carried out almost properly.
Additional comments: The genus name Erysipelatoclostridium has not been listed in the Approved Lists of Bacterial Names (Bergey’s Manual). (LPSN bacterio. net)
It is required to describe the novel species with a proposal of a novel genus including closely related species properly.
Expressions for the taxonomical terms should be improved.

Minor comments:
Strain name: Delete ‘the’ from all strain names (i.e., strain SG502T, strains SG502T and ATCC 14501T).
(You can use the term ‘the strain’ without the strain number.)

Add the definite article ‘the’ to express taxonomic ranks (e.g., within the family Clostridiaceae, of the genus Clostridium, to the genera Clostridium and Eubacterium).

line 150, 200-201: Individual cells of strain SG502T appeared to be Gram-positive rod-shaped with 1.5×0.35 μm in
line 203: Utilizes glucose, sorbitol,
Figure 1: Add “T” to the numbers of all type strains in the figure. (e.g., ATCC 19398T, ‘T’ is a superscript.)

Table 1: Differential phenotypic features of strain SG502T. (The table includes characteristics other than ‘biochemical’ features.)
Size (μm)

Table 2: ‘contains C15:0 DMA or C14:0 3-OH; summed feature 8 contains
C17:1 cis 9 or C17:2 and summed feature contains C18:1 c11/t9/t6 or
UN17.83Q.’
Subscripts for 15:0, 14:0, 17:1, 17:2 and 18:1.


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

Input:
Title: ANALYSIS OF PEDESTRIAN ACTIVITY BEFORE AND DURING COVID-19 LOCKDOWN, USING WEBCAM TIME-LAPSE FROM CRACOW AND MACHINE LEARNING
Review round: 1
Reviewer: 1

Output:
Basic reporting: •The paper presents a direct application of pedestrians detection in the actual situation of the world. It compares the number of  pedestrians detected before and after COVID 19 lockdown. The work is very useful and shows important findings even though the contribution is not very significant.

•The paper is easily understood nevertheless we suggest that the authors improve the english used throughout the paper and correct some typos and grammatical errors such as
      -on several factors, such as, for example night lighting
      - Python scripts and jupiter notebooks
      - Croud counting requires development of new methods

•The literature review is not sufficient. We suggest to add a section devoted to literature review in which you can add paraghraph "People detection" and some other researches aiming at pedestrain detection using deep learning methods such as

-Jiang, Y., Tong, G., Yin, H. and Xiong, N., 2019. A pedestrian detection method based on genetic algorithm for optimize XGBoost training parameters. IEEE Access, 7, pp.118310-118321.
-Cheng, E.J., Prasad, M., Yang, J., Khanna, P., Chen, B.H., Tao, X., Young, K.Y. and Lin, C.T., 2020. A fast fused part-based model with new deep feature for pedestrian detection and security monitoring. Measurement, 151, p.107081.

-The author references the source code in too many places. It is enough to mention the source code in experimental results or in footnote in order to order to avoid too many hyperlinks.

•Please correct the way you reference tables, figures and sub figures (Fig. 8A).
Experimental design: •Please add more details explaining why the YOLOtiled method gives better results compared to YOLO.

•The author did not mention the ground thruth, regarding the true count of pedestrains provided by human observations, to assess the proposed method.

•Please add a table in which you compare YOLOtiled and YOLO in terms of computational time
Validity of the findings: •The results provided by the proposed method compared to YOLOv3 are satisfactory. But it is highly recommended to assess the performance of the proposed approach with robust scientific metrics. Moreover, comparison with state-of-the-art approaches, in the same data, will push forward the paper.

•The conclusion contains unnecessary details especially those taking about source code.
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: ANALYSIS OF PEDESTRIAN ACTIVITY BEFORE AND DURING COVID-19 LOCKDOWN, USING WEBCAM TIME-LAPSE FROM CRACOW AND MACHINE LEARNING
Review round: 1
Reviewer: 2

Output:
Basic reporting: This research applied the YOLO machine learning algorithm for pedestrian detection and track the changes in pedestrian activity before and during the COVID-19 lockdown in Cracow, Poland.
Experimental design: 1) This manuscript is just a case study of using YOLO. Each webcam image was simply divided into six smaller tiles for YOLO input. I think the authors did not improve or modify the original algorithm.

2) Please clarify why the similar dimensions/proportions between the input image and the training image can improve the accuracy of pedestrian detection. The readers expect to understand the intrinsic nature of this outcome. In Fig4a, will the accuracy be improved if the original image is cropped to remove buildings on top before dividing it into two tiles (720x720 px)?

3) The conclusion is that pedestrian activity decreased by 78-85% during the lockdown. What are the new things here? I heard similar statistics on media many times.
Validity of the findings: How was the detection accuracy of the methods validated and compared?
What is the novelty of the research? I don't see significant contributions from the manuscript.
Additional comments: - It is strange when the number of pedestrians is described in decimals, for example, 0.14 or 16.86 people. Instead of statistics in hourly, pedestrians can be counted per day for ignoring decimal usage.
- The principles of the YOLO algorithm should be introduced in more detail. A workflow should be added.