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: SMALL MOLECULE THERAPEUTICS FOR COVID-19: REPURPOSING OF INHALED FUROSEMIDE
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: In the present manuscript, Wang and coll. report an interesting in silico / in vitro drug screening strategy for the identification of molecules with multi-target anti-inflammatory effect that could eventually constitute interesting candidates for the treatment of the immune-pathogenic phase of COVID-19. As a result of their screening and in vitro validation approach, they propose furosemide as a possible therapeutic.
The manuscript is very well written, with clear and relevant concepts. The context is well explained and provides the necessary background information for the interpretation of the study and results. The study design is straightforward and the different levels of validation follow a logical sequence. However, I believe that certain points need to be addressed before considering the manuscript for publication in PeerJ.

Major issues:
1)	The most important issue to be addressed is related to statistical analysis and the criteria used for data interpretation. On one side, differences observed in Fig 1A-B and 5A-C seem a priori rather minor to support P-values below 0.05 or 0.01, mostly considering error bars. On the other side, the results shown in Fig 4B and do not seem to support categoric statements such as “the amount of secreted IL-1b slightly decreased…” (line 242). I suggest the authors revise the analysis and potentially temperate their conclusions, notably in the case of the putative effect of furosemide on NO production and TNF-a. Including in the supplementary material the dataset from which the analysis was performed would also be desirable.

2)	For clarity purposes, I find important to include in Figure 1 a schematic representation of the overall screening strategy prior to the in vitro evaluation, from the +1000 molecules in the library to the identification of the 4 candidate “hits”. This would greatly help the readers to better understand the experimental approach.

Minor issues:
Figures 4, 5, 6: Please consider merging these figures in one to ease analysis/comparison.
Figures 7, 8: Please consider merging these figures in one to ease analysis/comparison. Please provide more information on the methodology in the figure legend.
Figures 9, 10: Please consider merging these figures in one to ease analysis/comparison. Please provide more information on the methodology in the figure legend.
Lines 60-62: I find that the inclusion of the reference “Xu X et al” is rather premature. Although the authors clearly warned on “preliminary data”, this is so far an abstract (the rest of the manuscript is in Mandarin) in a non-peer-reviewed preprint server. I would probably remove this part of the text or ideally find another reference.
Lines 331-333: The authors state that furosemide has “ideal” pk properties for targeting circulating macrophages. Please briefly discuss the potential role of respiratory tissue resident macrophages.
Lines 346-348: “…nebulized furosemide… demonstrating improved efficacy…”. Please explain the context of the trial; i.e. “improved efficacy” against which pathology?
Lines 366-368: The authors propose to use furosemide in the early course of infection. Although I agree that the advanced ICU state would be too late, the early clinical phases of COVID19 are mostly driven by high viral replication, for which the combination with an antiviral seems mandatory.
Discussion (in general): one important limit of the study is that the potential effect of furosemide could not be evaluated in the context of SARS-CoV-2 infection. I do understand the manipulation of the virus is very restricted and of course I do not expect the authors to include this kind of experiments. However, I suggest the authors discuss the potential differences between the LPS-induced inflammatory response model used in this study and those induced by infection.


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: SMALL MOLECULE THERAPEUTICS FOR COVID-19: REPURPOSING OF INHALED FUROSEMIDE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The main idea of this work was to use both human endogenous substances and a drug dataset, in order to screen for some that could be active against TNF-α and IL-6 cytokines, using computational and in vitro methods. The English language is clear and used the professional terms in all the text. The figures and literature are well-represented in most of them. The authors used suitable literature and background in all sections of the article. The results confirmed the author's hypothesis but, on the other hand, the work needs complementary data in the text results and discussion to be fully considered for publishing.  There are other previous articles that used furosemide as an anti-inflammatory agent and combined with other drugs, as can be checked out in my suggestions in the next sections of the review process. On the other hand, the authors bring new insights for furosemide acting in IL-6 and TNF-a. Some improvements are needed in computational methods and results section to become the manuscript acceptable for publication.
Experimental design: The experimental design was well constructed and organized. The methodology was original in using endogenous substances to search for possible compounds with anti-inflammatory action. The authors used the in vitro methods with rigor and ethics, but the computational methods must be better described. See my considerations below:

Lines 78 - 80: Here the authors don’t explain were these endogenous substances and the drug dataset was obtained. Is it from any curated database (PubChem, Drugbank, ZINC)?  Please indicate this in the methods section.

Lines 83 - 84: The authors don’t explain how they selected the crystallographic structures for docking.  Please include this in the paper.

Lines 92 - 95: Explain why you selected pH 7.4. Do you used it just for the ligands or included the receptors?

Lines: 138 - 139: Please include the concentration of the substrate.

Line 146: Please include polyacrylamide concentration.
Validity of the findings: The work brings new aspects of the immunological action of furosemide, applying to the treatment of COVID-19. In my point of view, these results can be applied to other types of treatments where the patient's inflammatory burden increases suddenly. In this case, a viral infection is just another treatable disease with the help of this medication. The work is innovative in the sense of using computational tools in order to filter endogenous substances with important actions for the treatment of COVID-19, combined with confirmatory in vitro methods. On the other hand, other authors have already used this drug for the same purpose in other diseases. An important point in this work is that the computational results are confirmed by the in vitro tests. My considerations about the findings are described below:

Lines 176 - 178: please indicate from where you obtained these small molecules.

Lines 273 - 277: Please include re-docking for both crystallographic ligands from IL-6 and TNF-a, for validation of your docking findings with 3-HAA.

Lines 287 - 289: What parameters do you have to say that furosemide inhibits TNF-a based on pose energy? I think here you need to include a re-docking with the crystallographic ligand of 2AZ5 (6,7-DIMETHYL-3-[(METHYL{2-[METHYL({1-[3-(TRIFLUOROMETHYL)PHENYL]-1H-INDOL-3-YL}METHYL)AMINO]ETHYL}AMINO)METHYL]-4H-CHROMEN-4-ONE), in order to validate your docking results.

Lines 294 - 296: I think here you need to include a re-docking with the crystallographic ligand of 1ALU (tartaric acid), in order to validate your docking results. Other authors have found anti-inflammatory activity for furosemide, such as Pandota (2002) - 		 DOI: 10.1097/00045391-200207000-00009 ; Berti et al. (1995) - https://pubmed.ncbi.nlm.nih.gov/8595068/. Then, in this line, the authors do not provide significant new findings without completely validate the biochemical mechanism of action of furosemide in this case. Please, include re-docking for validating your computational findings.
Additional comments: It is an original and well-organized work but lacks some computational methods information and validations which will improve the quality of the work.


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

Input:
Title: SMALL MOLECULE THERAPEUTICS FOR COVID-19: REPURPOSING OF INHALED FUROSEMIDE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors satisfactorily addressed my major concerns. I would like to thank them for the effort. I therefore consider this new version of the manuscript acceptable for publication.


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

Input:
Title: SMALL MOLECULE THERAPEUTICS FOR COVID-19: REPURPOSING OF INHALED FUROSEMIDE
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Thank you for all changes in the paper and for following the suggestions.


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: INTERMITTENT THETA BURST STIMULATION FACILITATES FUNCTIONAL CONNECTIVITY FROM THE DORSAL PREMOTOR CORTEX TO PRIMARY MOTOR CORTEX
Review round: 1
Reviewer: 1

Output:
Basic reporting: The topic of the manuscript is of sufficient interest, the article is well structured but the figures are of poor quality. Results are correctly reported and sufficiently well discussed from a physiological point of view. The main problem of the manuscript is the language, which presents several mistakes and is not fluently. I strongly recommend an english revision from a native speaker.
Experimental design: The aim of the study is well defined and quite relevant, although the novelty of the study is low. The methods are well described with sufficient details to reproduce the experiment.

A main limitation of the study is the absence of a neuronavigator system to localize the target areas. This is a weak point especially as regards the localization of PMd
Validity of the findings: The experimental designed is well constructed with a sham condition of sufficient validity. Statistics are well planned. The conclusions are well stated and sufficiently support the results of the study.
Additional comments: The manuscript is well designed and the topic is of sufficient interest, although the novelty is not high. The main limitation of the work is the language writing. I strongly recommend a revision by a native english speaker. In addition there are some sentences throughout the manuscript that need revision, for instance:

line 91-12 "TMS applied...M1 regions". This sentence does not have a scientific validity. What kind of TMS should strength M1 connectivity?

line 246-247 "decrease in SICI...connections decreased". The physiological meaning of this sentence is not clear to me.

line 267-268 "PMd rTMS...learning". What kind of rTMS are the authors talking about? Please be more precise.


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: INTERMITTENT THETA BURST STIMULATION FACILITATES FUNCTIONAL CONNECTIVITY FROM THE DORSAL PREMOTOR CORTEX TO PRIMARY MOTOR CORTEX
Review round: 1
Reviewer: 2

Output:
Basic reporting: In my opinion this manuscript suffers of some critical points. I have several suggestions that the authors may want to take into consideration.
In first instance, the main concern regards the small number of participants, that allows to judge the results, included the performed correlation, only as very preliminary. At this regard, I suggest to collect additional data for a better validation of the findings. Regarding the introduction, it suffers from too general statements regarding the TMS protocols and the cortical changes induced in terms of plasticity changes, lacking of any specific explanation of the neurophysiological mechanisms for which TMS approach could be useful to evaluate the PMd-M1circuitry.
Additionally, it lacks of any relevant reference about the relationship between premotor and motor cortices (for example, Koch G, et al. J Physiol 2007. Interactions between pairs of transcranial magnetic stimuli over the human left dorsal premotor cortex differ from those seen in primary motor cortex).
Experimental design: From a methodological point of view, the manuscript lacks of a clear hypothesis. What was the rationale for the choice of a specific interstimulus interval (i.e., 2 ms) for SICI protocol? Why the authors did not consider to assess both inhibitory and facilitatory mechanisms, by means of a short intracortical inhibition/facilitation (SICI-ICF) protocol? Did the authors used a neuronavigation system, for a correct targeting of TMS pulses during the different experimental sessions (before and after both experimental interventions, i.e. iTBS600 and sham)?
Validity of the findings: The discussion did not report a clear explanation about the possible neurophysiological mechanisms underlying the cortico-cortical interaction between PMd and M1. Could the authors explain in more detail their results, also regarding the time-points in which the main findings were observed?
Additional comments: In this study, Meng and colleagues aimed to investigate the influence of dorsal premotor cortex on motor cortical activity, by applying a theta burst stimulation protocol (intermittent TBS600 vs sham) over PMd and by assessing motor cortical excitability and intracortical circuits over M1. The results highlighted an increase of motor evoked potentials and a decrease in SICI at specific time-points after intermittent TBS as compared with sham.
In my opinion this manuscript suffers of some critical points. I have several suggestions that the authors may want to take into consideration.
In first instance, the main concern regards the small number of participants, that allows to judge the results, included the performed correlation, only as very preliminary. At this regard, I suggest to collect additional data for a better validation of the findings.
Regarding the introduction, it suffers from too general statements regarding the TMS protocols and the cortical changes induced in terms of plasticity changes, lacking of any specific explanation of the neurophysiological mechanisms for which TMS approach could be useful to evaluate the PMd-M1circuitry.
Additionally, it lacks of any relevant reference about the relationship between premotor and motor cortices (for example, Koch G, et al. J Physiol 2007. Interactions between pairs of transcranial magnetic stimuli over the human left dorsal premotor cortex differ from those seen in primary motor cortex).
From a methodological point of view, the manuscript lacks of a clear hypothesis. What was the rationale for the choice of a specific interstimulus interval (i.e., 2 ms) for SICI protocol? Why the authors did not consider to assess both inhibitory and facilitatory mechanisms, by means of a short intracortical inhibition/facilitation (SICI-ICF) protocol? Did the authors used a neuronavigation system, for a correct targeting of TMS pulses during the different experimental sessions (before and after both experimental interventions, i.e. iTBS600 and sham)?

The discussion did not report a clear explanation about the possible neurophysiological mechanisms underlying the cortico-cortical interaction between PMd and M1. Could the authors explain in more detail their results, also regarding the time-points in which the main findings were observed?


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: INTERMITTENT THETA BURST STIMULATION FACILITATES FUNCTIONAL CONNECTIVITY FROM THE DORSAL PREMOTOR CORTEX TO PRIMARY MOTOR CORTEX
Review round: 2
Reviewer: 1

Output:
Basic reporting: The introduction is well written and provide a sufficiently clear explanation of the rationale. However, it would be appropriate to mention new TMS-EEG study that demonstrated that TBS affects not only the site of stimulaton but also interconnected motor and non-motor areas.
Other minor points:

line 58-59: this sentence is too general since the authors should be more clear on which kind of "stimulation" are they referring to, especially when they refer to structural changes of the cortex.

line 79-80: this is inaccurate, since TMS stimulate not only facilitatory interneurons but also inhibitory
Experimental design: The experimental design presents a main point of weakness, namely the authors did not use any neuronavigation system to monitor coil position nor to identify the PMd site of stimulation.
In addition I have several concernes about the experimental procedures:
1. How did the authors establish the number of experimental participants? Did they perform a power analysis?

2. As far as I have understood, the authors re-tested 1mV intensity at each time point. To me, this procedure is not accurate and could lead to some bias. Can the authors better explain this procedure providing some references to justify this choice?

3. I find not convincing the choice to use only one ISI for SICI and ICF. The authors justify this choice referring to some preliminary test however they do not report this data.

4. The statistical section is poorly described. Which factors were included in the ANOVAs? Were the data tested for normality and sphericity?
Validity of the findings: Corticospinal M1 excitability results:
1. As a preliminary analysis, did the authors tested for difference in baseline between the two conditions? This should be explicited.

2. The authors reported a significant time*protocol interaction. However, I do not completely understand which post-hoc tests were detected as significant. The authors reported only one significant difference on MEPs tested at 15 minutes between the two protocols. However, it is not clear whether MEPs testeat at 15 min in the TBS condition were different also compared to the other time points of the same condition. This is important to understand if iTBS effectively induce an LTP-like effect. If not, this should be reported in the results and discussed.

3. Generally speaking, by looking at the results figures, I do not find easy to understand which differences are significant.

4. The correlation analysis is not convincing. First, it seems that the significant correlation is led by a few cases. Second, it is not clear how many correlations did the authors run and if a correction for multiple correlations was applied.
Additional comments: The study is well-written and the physiological interpretation of the findings is convincing. However, the experimental design and the results suffer from several methodological limitation that I explained in detail in the previous section.


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

Input:
Title: INTERMITTENT THETA BURST STIMULATION FACILITATES FUNCTIONAL CONNECTIVITY FROM THE DORSAL PREMOTOR CORTEX TO PRIMARY MOTOR CORTEX
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 satisfactorily to all my comments.
Please correct "faciliatory" with "facilitatory" (lines 53, 59, 124,215, 238, 306, 356)


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: MELATONIN IMPROVES THE GERMINATION RATE OF COTTON SEEDS UNDER DROUGHT STRESS BY OPENING PORES IN THE SEED COAT
Review round: 1
Reviewer: 1

Output:
Basic reporting: It is okay.
Experimental design: It is okay.
Validity of the findings: It contains new findings on roles of melaotnin in plants.
Additional comments: This paper described the functional role of melatonin on cotton seed germination in response to drought stress. The data were similar to previous report of Simlat et al (2018), but contained advanced data. I just pointed out a couple of minor points prior to publication.

1. Title was somewhat misleading. Melatonin does not improve cotton germination, but improves germination under drought stress. Thus, add under drought stress in title.

2. line 146: delete an Inhibition and produce.


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: MELATONIN IMPROVES THE GERMINATION RATE OF COTTON SEEDS UNDER DROUGHT STRESS BY OPENING PORES IN THE SEED COAT
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is an interesting study on the use of melatonin for enhancing seed germination under drought stress in cotton. However, the introduction, methods and discussion need more detail. More recent literature should be cited. The English language should be improved. Some examples where the texts could be improved are listed below

Line 38-41: I would suggest to extend this section by detailing the global impacts of drought on plant physiology and crop production. More recent references (see below) should be cited.

Tomato WRKY81 acts as a negative regulator for drought tolerance by modulating guard cell H2O2–mediated stomatal closure. 2020. Environmental and Experimental Botany 171. doi:10.1016/j.envexpbot.2019.103960

Line 58: Antagonistic interaction between ABA and GA in regulating seed germination under stress conditions should be discussed in view of recent literature

Abscisic Acid and Gibberellins Act Antagonistically to Mediate Epigallocatechin-3-Gallate-Retarded Seed Germination and Early Seedling Growth in Tomato. 2020. Journal of Plant Growth Regulation. doi:10.1007/s00344-020-10089-1

Line 68-69: please do not generalize neurohormones and plant melatonin in terms of stress tolerance. This is misleading. I would suggest the authors to provide a general but specific introduction to melatonin in plants and animals. Also, describe in detail that plant melatonin or phytomelatonin plays crucial roles in both biotic and abiotic stress tolerance in plants in view of following literature

Melatonin alleviates iron stress by improving iron homeostasis, antioxidant defense and secondary metabolism in cucumber. 2020. Scientia Horticulturae 265. doi:10.1016/j.scienta.2020.109205

Alkanes (C29 and C31)-Mediated Intracuticular Wax Accumulation Contributes to Melatonin- and ABA-Induced Drought Tolerance in Watermelon. 2020. Journal of Plant Growth Regulation. doi:10.1007/s00344-020-10099-z

Role of melatonin in arbuscular mycorrhizal fungi-induced resistance to Fusarium wilt in cucumber. 2020. Phytopathology. doi:10.1094/phyto-11-19-0435-r

Line 135-141: Please describe the standards that you used to consider a seed germinated or not.  I would suggest to provide more detail on the assessment of seed germination

Line 187: under the subheading “Determination of MT concentration”, it seems that authors would like to describe melatonin content in plants, but I do not find any description regarding endogenous melatonin content. This will mislead the readers. Please replace it with ‘Selection of MT concentrations for seed treatment’
Line 366-395: Discussion relating to ROS, oxidative stress and antioxidant potential as well as the role of plant growth regulators in improving stress tolerance could be further improved in view of the following literature. Authors are suggested to discuss and cite the following literature.

Abscisic Acid and Gibberellins Act Antagonistically to Mediate Epigallocatechin-3-Gallate-Retarded Seed Germination and Early Seedling Growth in Tomato. 2020. Journal of Plant Growth Regulation. doi:10.1007/s00344-020-10089-1

Dopamine alleviates bisphenol A-induced phytotoxicity by enhancing antioxidant and detoxification potential in cucumber. Environmental Pollution 259. doi:10.1016/j.envpol.2020.113957

Tomato WRKY81 acts as a negative regulator for drought tolerance by modulating guard cell H2O2–mediated stomatal closure. Environmental and Experimental Botany 171. doi:10.1016/j.envexpbot.2019.103960

Hasan MK, Ahammed GJ, Sun S, Li M, Yin H, Zhou J (2019) Melatonin Inhibits Cadmium Translocation and Enhances Plant Tolerance by Regulating Sulfur Uptake and Assimilation in Solanum lycopersicum L. Journal of Agricultural and Food Chemistry 67 (38):10563-10576. doi:10.1021/acs.jafc.9b02404

The English is understandable, but the quality of writing and technical construction of the narrative needs attention. The quality is almost good enough, but there are some atypical word choices, misplaced modifiers, vague language choices, and phrases. e.g. Line 426-: ‘pre-treating cotton seeds with MT’! There are many such examples throughout the manuscript.
Experimental design: Line 108-109; 168-171: Experiments were said to be conducted in 3-5 replicates for each experiment, but no information is presented for each of the repeats or how the experimental repeats where handled in the context of presented data.

Line 116: Please explain the basis for choosing 24 h duration as time-span of seed treatment.

Line 119-, 127-, 142-, 149-, 155-: Many important details need to be specified in “Materials and Methods”, such as (1) how the germination experiments were done (conditions, 7 days in dark?);(2) how the various samples were collected (including number of samples, sample units, replicates, tissue type (specify leaves/shoots/roots) detailed step-by-step protocol and more) for multiple tests, and ;(3) how exactly statistical analyses were performed.
Validity of the findings: Melatonin is a new and multifunctional molecule that confers tolerance to a number of biotic and abiotic stresses in plants. In the present manuscript, the authors studied the effects of seed treatment with melatonin on seed germination under drought stress in cotton.
Additional comments: This is an interesting study on the use of melatonin for enhancing seed germination under drought stress in cotton. However, the introduction, methods and discussion need more detail. More recent literature should be cited. The English language should be improved. Some examples where the texts could be improved are listed below

Line 38-41: I would suggest to extend this section by detailing the global impacts of drought on plant physiology and crop production. More recent references (see below) should be cited.

Tomato WRKY81 acts as a negative regulator for drought tolerance by modulating guard cell H2O2–mediated stomatal closure. 2020. Environmental and Experimental Botany 171. doi:10.1016/j.envexpbot.2019.103960

Line 58: Antagonistic interaction between ABA and GA in regulating seed germination under stress conditions should be discussed in view of recent literature

Abscisic Acid and Gibberellins Act Antagonistically to Mediate Epigallocatechin-3-Gallate-Retarded Seed Germination and Early Seedling Growth in Tomato. 2020. Journal of Plant Growth Regulation. doi:10.1007/s00344-020-10089-1

Line 68-69: please do not generalize neurohormones and plant melatonin in terms of stress tolerance. This is misleading. I would suggest the authors to provide a general but specific introduction to melatonin in plants and animals. Also, describe in detail that plant melatonin or phytomelatonin plays crucial roles in both biotic and abiotic stress tolerance in plants in view of following literature

Melatonin alleviates iron stress by improving iron homeostasis, antioxidant defense and secondary metabolism in cucumber. 2020. Scientia Horticulturae 265. doi:10.1016/j.scienta.2020.109205

Alkanes (C29 and C31)-Mediated Intracuticular Wax Accumulation Contributes to Melatonin- and ABA-Induced Drought Tolerance in Watermelon. 2020. Journal of Plant Growth Regulation. doi:10.1007/s00344-020-10099-z

Role of melatonin in arbuscular mycorrhizal fungi-induced resistance to Fusarium wilt in cucumber. 2020. Phytopathology. doi:10.1094/phyto-11-19-0435-r

Line 108-109; 168-171: Experiments were said to be conducted in 3-5 replicates for each experiment, but no information is presented for each of the repeats or how the experimental repeats where handled in the context of presented data.

Line 116: Please explain the basis for choosing 24 h duration as time-span of seed treatment.

Line 119-, 127-, 142-, 149-, 155-: Many important details need to be specified in “Materials and Methods”, such as (1) how the germination experiments were done (conditions, 7 days in dark?);(2) how the various samples were collected (including number of samples, sample units, replicates, tissue type (specify leaves/shoots/roots) detailed step-by-step protocol and more) for multiple tests, and ;(3) how exactly statistical analyses were performed.

Line 135-141: Please describe the standards that you used to consider a seed germinated or not.  I would suggest to provide more detail on the assessment of seed germination

Line 187: under the subheading “Determination of MT concentration”, it seems that authors would like to describe melatonin content in plants, but I do not find any description regarding endogenous melatonin content. This will mislead the readers. Please replace it with ‘Selection of MT concentrations for seed treatment’
Line 366-395: Discussion relating to ROS, oxidative stress and antioxidant potential as well as the role of plant growth regulators in improving stress tolerance could be further improved in view of the following literature. Authors are suggested to discuss and cite the following literature.

Abscisic Acid and Gibberellins Act Antagonistically to Mediate Epigallocatechin-3-Gallate-Retarded Seed Germination and Early Seedling Growth in Tomato. 2020. Journal of Plant Growth Regulation. doi:10.1007/s00344-020-10089-1

Dopamine alleviates bisphenol A-induced phytotoxicity by enhancing antioxidant and detoxification potential in cucumber. Environmental Pollution 259. doi:10.1016/j.envpol.2020.113957

Tomato WRKY81 acts as a negative regulator for drought tolerance by modulating guard cell H2O2–mediated stomatal closure. Environmental and Experimental Botany 171. doi:10.1016/j.envexpbot.2019.103960

Hasan MK, Ahammed GJ, Sun S, Li M, Yin H, Zhou J (2019) Melatonin Inhibits Cadmium Translocation and Enhances Plant Tolerance by Regulating Sulfur Uptake and Assimilation in Solanum lycopersicum L. Journal of Agricultural and Food Chemistry 67 (38):10563-10576. doi:10.1021/acs.jafc.9b02404

The English is understandable, but the quality of writing and technical construction of the narrative needs attention. The quality is almost good enough, but there are some atypical word choices, misplaced modifiers, vague language choices, and phrases. e.g. Line 426-: ‘pre-treating cotton seeds with MT’! There are many such examples throughout the manuscript.

You need a little work on improving the coherency of the narrative as well as the English language so that it will be suitable to publish.


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: MELATONIN IMPROVES THE GERMINATION RATE OF COTTON SEEDS UNDER DROUGHT STRESS BY OPENING PORES IN THE SEED COAT
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Abstract
•	Information regarding PEG should be given.
•	Abbreviations for  hydrogen peroxide, superoxide, superoxide dismutase, and peroxidase should be given.
•	Which osmo-protectants were affected positively? It is unclear.
•	The authors mentioned “Starch metabolism” in abstract, but there is no expression about amylase activity, GP, GR, etc.
•	The abstract section should be re-written based on all parameters studies.

Introduction
•	There is no information regarding amylase.
•	The information regarding the other parameters studied should be extended.
•	Line 43 .. Correct ref

Mat met
•	Line 149: Soluble sugar, protein, amylase methods are not adequate. A detailed explanation should be given.
•	The methods of ABA and GA contents must be given in detailed

Results
•	Line 180 (PEG concentration) results must be checked. The values (%) are faulty.
•	Line 219: The value of SOD is faulty.
•	Similarly,
Line 225 (POD activity),
Line 236 (O2- content), Line 243
Line 251 (MDA) content
Line 261 (amylase content) values have been miscalculated.

•	Line 269-270: The authors expressed that all treatments increased proline content; however, as seen from the figure, MT treatment did not statistically increased proline content on 2, 4, and 6th days.
•	The names of treatments groups should be given as only abbreviation. The full names must be removed in this section.
•	Fig 3 A: The unit of SOD activity must be given U.mg protein. U/g FW is not correct to discuss the results.
•	Fig 4A : Change the unit of H2O2 content. gprotein expression is not correct.
Discussion
•	The names of treatments groups should be given as only abbreviation. The full names must be removed in this section.
•	The authors published a different study regarding effect of melatonin on  germination of cotton seeds. In this study, they investigated amylase activity, proline, protein, sugar, H2O2, O2- contents and SEM different from prior study.
•	The discussion section is not satisfactory. The results are interconnected and not fluent.
•	The results are not well discussed, but simply passed over.
•	Very little information is given about the pore opening.


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: MELATONIN IMPROVES THE GERMINATION RATE OF COTTON SEEDS UNDER DROUGHT STRESS BY OPENING PORES IN THE SEED COAT
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revisions look fine. Professional article structure, figures, tables.
Experimental design: The revisions look fine. Research question well defined, relevant & meaningful.
Validity of the findings: All underlying data have been provided
Additional comments: I found that the authors adequately addressed my queries, although there are still some minor language issues in the revised texts. Perhaps the authors are still confused between Gibberellins and Gibberellic acid. Anyway, these minor issues could be solved during proof-correction, therefore, I would like to endorse the revised manuscript for publication.


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

Input:
Title: PREDICTING THE EFFECT OF VARIANTS ON SPLICING USING CONVOLUTIONAL NEURAL NETWORKS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: The conversion of sequence dataset into CNN input format should be described more clearly. For details refer my comments.
Validity of the findings: Comparative analysis with existing literature is required. Kindly refer my comments.
Additional comments: In this study, authors applied convolution neural network (CNN) for predicting splice sites as well as the effect of single nucleotide variants on splicing using benchmark data sets. This study is interesting. However, following points should be addressed before accepting for publication.

1.	The input format for CNN model is of image type. Can the author explain how they convert the splice site sequences into images?  To my knowledge, the binary transformation of sequences only yields a matrix. So it is necessary to know how this matrix is converted into images (kindly explain if any software is used). If there is other way of feeding the numerical data set into CNN, this should be explained in details.

2.	The authors should compare the prediction accuracy with existing deep learning based methods with regard to prediction of splice sites.

3.	Also, comparative analysis with existing literature should be performed in respect of predicting the effects of variants on splicing.

4.	The size of the splice site data set is very large. Hence, time taken by CNN and other machine learning methods for training model must be mentioned.

5.	Ready made source code of the methods should be provided for reproducibility of the work.

6.	Authors should share the processed splice variants data set for reference in future study.


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: PREDICTING THE EFFECT OF VARIANTS ON SPLICING USING CONVOLUTIONAL NEURAL NETWORKS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Little improvement is required in the language like proper use of articles, grammatical corrections. More citations to the splice site prediction tools at least in last five years should be given with adequate discussions. Result and discussion section has to be more descriptive.
Experimental design: Research is original. The research question is well defined, relevant & meaningful but comparison with existing state of the art tools  using an independent test set is missing.
Validity of the findings: Findings are valid
Additional comments: Review report
Thanapattheerakul et al.,  attempted to develop a statistical model for the prediction of splice sites and estimated the effect of variants on the splice motif. There work seems to be interesting and can be used in the field of genome annotation. Few revisions and concerns are to addressed before its publication in the PeerJ.
Major Concerns
There are many splice site prediction tools available in the public domain, but authors have not compared there tool with any other state of the art tools for splice site prediction using an independent test data set. Based on machine learning techniques various splice site prediction tools are available like MalDoss, DSSPred, HSplice etc. which are neither compared using an independent test data nor cited in the introduction. Though authors cited SpliceRover, they have not compared its performance with the proposed approach.
Have the authors made an comparison in terms of performance for different window sizes of splice sites with the best model before selecting the window size of 40. If not, either they should compare or refer appropriate citations based on window sizes for splice site prediction to justify their selection of 40 bp widow size.
In the model validation part, the data division for cross validation is not clear, probably the authors wanted to say 80% of the data set they have used for training and 20% for validation for each cross validation alternatively. But from there description it seems that they have used 100% of the data set for training and 20% of their training data has been used for validation each time. If the latter one is the case, then performance of their model is over estimated.
Authors should use Mathews Correlation Coefficient as an additional performance metric for the evaluation which is generally regarded as a balanced measure and can be used even if the classes are of very different sizes(imbalanced; see Boughorbel, S.B (2017)).
Overall  the Results and Discussion section has to be more elaborated.
Minor Concerns
The authors mainly focused on mRNAs, hence they should specifically use mRNA instead of RNA wherever necessary.
In the abstract, "Several models were trained ...." authors should specify the exact number of models they have used. They should also mention the source of existing datasets in the abstract.
The authors missed a citation in the line no 164 and also missed the year of citation in the line no 197.
Line no 198; non-linearity relationship should be changed to non linear relationship.
Line no 235; the word splice site is missing after "donor and acceptor".
The authors should read the manuscript thoroughly for minor grammatical corrections throughout the manuscript.


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

Input:
Title: PREDICTING THE EFFECT OF VARIANTS ON SPLICING USING CONVOLUTIONAL NEURAL NETWORKS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors responded to most of my concerns properly. However, some more clarification/revisions are needed before its publication.
Experimental design: Well defined
Validity of the findings: Findings are valid
Additional comments: I am happy that the authors responded to most of my concerns properly. However, some more clarification/revisions are needed before its publication.
The authors mentioned that they could not compare the performance of their model with the suggested tools. As they have reported the accuracies for donor and acceptor splice sites separately, they could have compared the performance of the model with the existing tools in terms of donor splice sites separately.
The effect of the performance of the model based on different window sizes is concerned, in spite of lower accuracy with the window size 40 the authors have considered this window size for predicting the effect of variants. The prediction of the variant effect is dependent on the accuracy of the prediction of splice sites in the previous stage. Thus, my concern is won’t reliability of the prediction of variant effect be reduced with a low accuracy window size? Further, I can observe the window size of 240 has an equivalent accuracy with the window size of 398. Thus, this window size could have been explored for the prediction of the effect of variants.

Minor comments

Sonnenberg et al. proposed the SVM with weighted degree kernel to recognize splice sites (Sonnenburg et al., 2007). Meher et al. proposed SVM- and RF-based tools, named HSplice (Meher et al., 2016) and MaLDoSS (Meher, Sahu & Rao, 2016), to predict splice sites in many species, including Homo sapiens, Bos taurus, Danio rario and Caenorhabditis elegans; however, both tools can predict only donor sites.

Can be rewritten as

Sonnenberg et al. (2007) proposed the SVM with weighted degree kernel to recognize splice sites. Various SVM- and RF-based tools like HSplice (Meher et al., 2016) and MaLDoSS (Meher, Sahu & Rao, 2016), are available in the public domain for the prediction of donor splice sites in many species, including Homo sapiens, Bos taurus, Danio rario and Caenorhabditis elegans etc.


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: PREDICTING THE EFFECT OF VARIANTS ON SPLICING USING CONVOLUTIONAL NEURAL NETWORKS
Review round: 3
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Authors have responded well to all my queries, however still some minor corrections are required.I suggest the senior authors to re-read the manuscript once again for spellings, definitions and grammar. Some of the minor comments are mentioned below:

Line no 83:
Sonnenberg et al. proposed the SVM with weighted degree kernel to recognize splice sites (Sonnenburg et al., 2007).
it should be written as "Sonnenberg et al. (2007) proposed the SVM with weighted degree kernel to recognize splice sites." as per journal format. The citation (Sonnenburg et al., 2007) is not required at the end of the sentence.

Line no 84-87:
Various SVM- and RF-based tools, for example, HSplice (Meher et al., 2016) and MaLDoSS (Meher, Sahu & Rao, 2016), have been made available in the public domain for the prediction of donor splice sites in many species, including Homo sapiens, Bos taurus, Danio rerio, and Caenorhabditis elegans
The species names in last sentence must be in italics.

Methodology, Line 264
“Model Comparison... As an additional comparison of the developed CNN models to the traditional machine approach, an existing web-based tool termed HSplice (Meher et al., 2016) was used.
in the above sentence "traditional machine approach" should be change to "traditional machine learning approach"

Line 462
"......GitHub for open access; however, note that domain knowledge is needed to finalize a validated dataset and it is also a time-consuming process.”
In the above sentence "however, note that domain knowledge" should be changed to "however, the domain knowledge".


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: EVALUATION OF PSYCHOLOGICAL STRESS IN SCIENTIFIC RESEARCHERS DURING THE 2019–2020 COVID-19 OUTBREAK IN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript generally is clear but there are some lapses in the English. Occasionally these make it hard to work out the intended meaning. This needs to be tightened up but mostly this cosmetic (annoyed pdf attached to this review).

The literature is a little sparse and confined to recent work. There is however older work on stress in academia and among researchers. There are also some recent work that is probably relevant:

Some suggested additional context:

https://wellcome.ac.uk/sites/default/files/what-researchers-think-about-the-culture-they-work-in.pdf

https://www.thelancet.com/journals/lancet/article/PIIS0140-6736(20)30460-8/fulltext

https://www.tandfonline.com/doi/abs/10.1080/01443410120090849

https://www.tandfonline.com/doi/abs/10.1080/0144341960160104

Overall the structure is mostly fine, but I think the specific hypotheses and links to the analyses reported lack clarity. To the extend that there is a confirmatory element to the research I'd like clear hypotheses stated and linked to specific analyses. There is also clearly an exploratory element and I'd like to see that facilitated by reporting: a table of means and SDs of the measures and a correlation between the key variables. I'll go through analysis in turn and make some suggestions for improving clarity of reporting below.
Experimental design: The sampling strategy is not adequately described. This needs to be stated (i.e., how were email addresses targeted). I'm not sure how participants were randomly distributed - so I suspect this was an opportunity sample. Even if randomly distributed the responses are not random so the sample is probably best described as an opportunity sample.

As stated earlier the primary research question and hypotheses need to be clearer.

Making the survey Qs available to readers (if necessary stripping out copyrighted scales) would be helpful.
Validity of the findings: The data are provided and look reasonable - however I have not reproduced any analyses.

The analyses are a bit confusing in places - partly because I don't know what the main research Qs are. I'll go through the main analyses table by table.

To interpret these it would help to have the means and SDs (maybe skew and kurtosis) and in the scale descriptions the min and max of the scales should be reported. It would also be useful to report internal consistency reliability for the scales (coefficient omega or coefficient alpha - especially the scales that are modified.

Table 2a. The reporting is a little non-standard but is equivalent to separate analyses of the four outcomes with whether the researchers agree that research been delayed as a predictor. I'd consider correcting for multiple testing (though as it happens a Hochberg adjustment gives the same pattern of statistical significance).

Table 2b. I don't think this is a sensible way to analyse the data. First some categories are too small (e.g., the relaxed category has n = 1 and should be collapsed into one of the others). Second the categories aren't obviously ordered and seem to mix outcome with predictor variables (i.e., whether the project was impacted and the state of the researcher). I'm not sure what is the best way to sort this out. Possibly there is a clear ordering here and it could be handled more neatly by correlating the ordinal response with the continuous outcome. I think a Spearman or Pearson correlation would suffice here as there is a single predictor.

Table 3. I'm not a huge fan of analysing subgroups like this. It is easy to detect spurious patterns via multiple testing. It is also described in the table as a stepwise regression. Stepwise regression biases tests and estimates. I'd recommend a single regression with simultaneous entry of predictors. I'd do this in stages with demographics entered as a block and then the predictors of interest. Instead of subgroup analyses include large subgroups as dummy coded predictors and include interactions with key predictors.

Table 4. These sorts of tables are hard to interpret. Collapse the small categories into similar groups (all PhD students for instance). To aid detection of patterns I'd consider looking at the standardised residuals or adjusted standardised residuals (the former are a bit conservative - but that tends to make them useful in situations like this as it is less important to correct for multiple testing). The standardised residuals have an approximate z distribution and thus if exceed +/- 1.96 are statistically significant at p < .05.

Table 5a. Collapse social science and others (small n and similar patterns). More importantly I think the irrelevant category needs to be excluded from the analysis in the bottom analysis (mention this in the notes to the table). Including it makes no sense.

Table 5b. Here and the top analysis in table 5a you have an ordinal outcome - however the title variable, while arguably ordinal, is showing a non-monotonic pattern. There is a case then I think for an ordinal regression with research progress as an outcome and title dummy coded. This would allow other predictors to be included - but that might not be sensible if you have no specific hypotheses about them. Gender might be worth including. So I can see case for keeping the original chi-square analysis (and maybe also looking at the standardised residuals).
Additional comments: This is a potentially useful data set that could be important in highlighting how the present pandemic is impacting on research. The sampling strategy, research question and analyses could be better described and the presentation strengthened. The literature is also focused a bit narrowly on recent work without linking to prior research on researcher burn-out or stress (which would probably provide additional support for their main conclusions).

Although the research questions need to be clarified and and specific hypotheses flagged I'd also ask the authors to highlight the largely exploratory nature of the research where appropriate.


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: EVALUATION OF PSYCHOLOGICAL STRESS IN SCIENTIFIC RESEARCHERS DURING THE 2019–2020 COVID-19 OUTBREAK IN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1.	The language used could be clearer throughout the manuscript. I note several instances in my comments below. In some cases it is merely that very long sentences could be split into separate ones, e.g. “Due to the severe epidemic situation and in order to avoid further transmission, most industries had been forced to shut down temporarily and science and education activities were paused in China, which had caused people much inconvenience(ScienceMag.org 2020b).” (page 6). Similarly, the following sentence is very hard to follow “Animal centers and practical labs were borne the brunt not to be admitted, and many scientific and social congresses and symposiums were cancelled, and postgraduates and scientific workers were confined to be back to their workplaces”. In particular the “confined to be back to their workplaces” is very hard to follow.
2.	There are instances of unnecessary repetition throughout the manuscript. E.g. the 23 questions of the perceived stress scale. Stating this twice made the section difficult to follow – at first I thought these were different scales. Please revise the wording for clarity
3.	While I appreciate more colloquial language in manuscripts, this manuscript at times does not read like a research article. E.g. “it can be roughly seen from this question…” The writing should be revised to be clearer and more precise.
4.	Please report very small p values as < .001, rather than p=.000

In sum, I do not feel that this manuscript meets the standards of the journal in this section.
Experimental design: My comments on the experimental design largely fall into the general comments under "methods"
1.     Given that the measures used are novel, all items should be provided in the report, e.g. as an appendix. It came as a complete surprise that one of the possible responses was “about to collapse”. As the measures are adapted/new it is particularly important that the reader is provided with this information. When checking the raw data I noticed items that were not discussed in the manuscript, perhaps ones that were removed in the stepwise regression analyses. I suggest that a table is included with summary statistics for all items in the surveys – perhaps merely a summary score for the standardised measure.
2.	Please include details on how the questionnaire randomly distributed. The authors should provide more information on this and the recruitment process.
3.	How did the authors check that respondents understood the meaning of the question?

Much work would be needed for this manuscript to meet the journal standards for this section
Validity of the findings: 1.	As exemplified in specific comments in the general comments header, the paper would be clearer if results and speculation of the results were more firmly distinguished throughout the manuscript. Similarly, the authors should be careful to not make inferences of the results that the analyses did not test, e.g. specific differences between two groups in the Chi Squared tests.
Additional comments: The authors present a survey study asking what impact the COVID-19 pandemic (and social isolation measures) has on researchers work capacity mental health. The abstract supports many of the shared feelings among researchers during the COVID-19 outbreak. I was excited to read a paper examining the impact of research disruptions on researcher mental health; we need data on this in order to understand how to best support researchers. Even simple survey statistics – as I expected from this paper – would be useful to use in future appeals to improving working conditions and support for researchers.

I empathise with the intentions of this research and sympathise with the author’s desire to have their work published. But, I am not clear what this paper offers above e.g. the blogpost referenced throughout the paper (Sciencemag.org, 2020a). The authors comment reads “This is a clinical investigation of COVID-19 epidemic, which will help others around the world during this outbreak. We hope you could consider it for a rapid reviewing and editing process. Many thanks.” This gave me some enthusiasm for the paper. Yet, the paper is not a clinical investigation, nor do I feel the results would help others during the outbreak. The authors received rapid review for this paper, yet I cannot see why this paper needs urgent publication. I cannot help but think that other papers would be more deserving of reviewer efforts at this time.

Core to my comments below is that this paper requires substantial revision and proof-reading to be able to review in its entirety.

Abstract:
1.	I suggest stating “Chinese government” for additional clarity
2.	The sentence beginning “the pressure on colleagues…” reads oddly with the word “researches”.
3.	I am not clear what is meant by “a great influence on the experiment” in the final sentence.

Introduction:
4.	The abbreviation “COVID-19” is introduced twice in the first paragraph. No need for the second.
5.	The majority of the literature discussed in this manuscript are papers from 2020 focused on COVID-19. Much work has been already conducted to investigate researcher and student mental health (e.g. to name two https://wellcome.ac.uk/reports/what-researchers-think-about-research-culture and https://www.nature.com/articles/d41586-019-03459-7) in relation to the issues raised in this paper. This limits some of my enthusiasm for this study as it does not situate it within known issues within researcher and student mental health, including work-related stresses. So, while I am concerned with the same issues raised by this paper the introduction will need to be reworked to situate the paper within the already existing literature.
6.	In the final paragraph, the authors could describe the present study with more clarity. E.g. what diverse populations? How was the study conducted? As it stands, most of the paragraph actually appears to discuss the results and indicate points in the discussion section.

Methods:
Note: Other comments appear under the “experimental design” subheading above.
7.	The questionnaires section also somewhat describes the analysis plan, making it difficult to follow. I suggest reconfiguring the methods section to more clearly differentiate these aspects.

Results:
8.	The results section would be clearer if discussion of the results were moved to the discussion section. E.g. most of the ‘basic information of the participants’ paragraph is discussion related, and the sample summary is already in table 1.
9.	The results section reads more as a qualitative analysis, rather than a quantitative analysis of data collected. I suggest revising the results to more specifically describe the statistics performed, and move any discussion of implications/speculation to the discussion section.
10.	At first glance, I was concerned that the authors were selectively reporting significant results in the regression analyses. Then table 3 made it clear that a stepwise approach was used. First, relevant details such as this should be presented in the data analysis description. Secondly, there are several strong arguments against a stepwise approach (e.g. https://journalofbigdata.springeropen.com/articles/10.1186/s40537-018-0143-6 and https://towardsdatascience.com/stopping-stepwise-why-stepwise-selection-is-bad-and-what-you-should-use-instead-90818b3f52df). I suggest reporting all predictors, and report any corrections for multiple comparisons applied, or not.
11.	The description of the three researcher appeals is hard to follow. Several appeals are discussed in the same sentence. The wording suggests that groups differed in their rate of appeal. Yet, none of the Chi squared tests would be significant if multiple comparisons were considered. Nor were tests conducted between individual groups.
12.	In the section “The research progress affected by COVID-19 differs from researcher’s identities”: It would be helpful to know what analyses were conducted before saying that there were statistical differences. This would allow the reader to understand the meaning of the analyses conducted.  The statistics reported do not correspond to the description of results. The Chi squared test does not tell us that one individual group scores differently to another specific group, additional tests would be needed to address this.
13.	The authors reference tables 2a and 2b at the end of the results section, I assume that they mean 5a and 5b?

Discussion:
14.	As mentioned earlier on the discussion section, the literature discussed here is limited. For this work to have more utility it must be situated well in the existing literature – this would provide much more support to
15.	An aspect that makes the manuscript difficult to follow throughout is a lack of clarity between discussion of results and implications. Discussion of results is intertwined with potential implications that were not examined within the survey and analysis.
16.	The limitations section exemplifies my previous two points. No literature is referenced to support the statements, and it is not entirely clear what the suggestions would add other than a cursory observation that other work could be done.
17.	Additionally, the authors should add more detail to the statement about power of this study. Was a power analysis conducted? Why not collect data for longer if this is the case? What is meant by underpowered in this case?

Tables and Figures:
18.	Please indicate what the +/- indicates in table 2 – I assume standard deviation?
19.	Please also note what the numbers in parentheses are in table 4.

Data:
20.	I want to thank the authors for providing the raw data - this is something I stand firmly behind. Could the authors provide a copy of the raw data with the numeric values instead of the worded item responses?
21.	Perhaps the authors would be willing to also share their analyses syntax? Of course this is not a condition of publication in PeerJ, but it would be a nice example of open practices.

In the interest of openness, I always sign my reviews,
Sam Parsons


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: EVALUATION OF PSYCHOLOGICAL STRESS IN SCIENTIFIC RESEARCHERS DURING THE 2019–2020 COVID-19 OUTBREAK IN CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised MS is much clearer and the findings are related appropriately to the wider literature on researcher stress. There are still a few areas where the English could be improved - though this is mostly very minor or to make key points clearer. I have edited the word document* with track changes to pick up most of the required changes - with a few queries/comments. In particular the term "appeals" might be easier to understand as "proposed solutions" (throughout the MS including tables).

*It appears I can not upload the word version I have edited - I have converted this to a pdf, but can provide the word version if required.
Experimental design: The survey is explained much more clearly.
Validity of the findings: The conclusions are more measured and better supported by the evidence presented. In particular collapsing categories and reporting slightly simpler analyses has improved the MS.

While it isn't directly relevant to the revisions I note that I didn't explain my recommendation about using standardised residuals of the chi-square analysis clearly. It is no longer relevant to the MS, but this is a paper describing the approach I was suggesting:

MacDonald PL, Gardner RC. Type I Error Rate Comparisons of Post Hoc Procedures for I j Chi-Square Tables. Educational and Psychological Measurement. 2000;60(5):735–754.
Additional comments: I am recommending minor revisions only to tidy up the minor issues with the MS that remain. (Apologies for the autocorrect error on my previous review - it was indeed "annotated" rather than "annoyed".)


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: ASSOCIATION BETWEEN THE NUMBER AND SIZE OF INTRAPULMONARY LYMPH NODES AND CHRONIC OBSTRUCTIVE PULMONARY DISEASE SEVERITY
Review round: 1
Reviewer: 1

Output:
Basic reporting: professional English was used, only some minor mistakes are present, also compare minor issues
Experimental design: see below
Validity of the findings: see below
Additional comments: In the present manuscript, Schreuder et al report on the impact of perifissural lymphatic nodule (PFN) characteristics on COPD severity. The manuscript is based on a large clinical study (COPDGene) and 50 patients per COPD group were randomly recruited from this big database resulting in 350 analyzed study subjects.
In the end, no association of the number of PFN and COPD severity was found, however, a tendency towards lymph node size (in short diameter) and more advanced disease was suggested with regard to PFNs.
In summary, this study is about a relevant and interesting topic and also the study design involving the above mentioned large clinical trial data is a promising approach. However, some major issues have to be addressed before the present manuscript can be recommended for publication.

1)	When studying the (complex) impact of inflammation on COPD severity one has to take into account that not a single marker like e.g. radiological characteristic of only one lymph node subpopulation/station is representative for such a complex disease involving the whole lung and its associated thoracic structures and furthermore the whole immune system.

2)	Thus one might be interested in:

A)	Systemic inflammatory parameters (blood parameters)
B)	The whole lymphatic system including mediastinal as well as hilar lymph nodes
C)	Local (in the lung and adjacent tissue) inflammation

3)	Since the COPDGene database should offer the possibility not to only study PFNs but also the aforementioned local and systemic inflammatory parameters, a more comprehensive analysis with regard to inflammation would be of interest and worth to be published. One – very special – single marker without a well-documented rational behind it might not be representative for the whole pathogenesis behind a – heterogeneous and complex chronic – disease like COPD.

4)	Was really no ethical approval required?

5)	Is it valid to summarize PRISm together with GOLD 1 & 2 in the mild group?

6)	What about the follow up? Was the dynamic of the lymphadenopathy relevant for the clinical curse? Was enlargement of lymph nodes associated with progression of disease over the 5 year period? You have this 5 year follow up and should use it, would be a clear strength of the study to use the 5 year data to test your marker(s) also as follow up markers!

 Minor Issues:
Abstract line 45 should be associated with lymphadenopathy
Methods line 102: two times “to compensate for this” in one sentence

In summary the study design and rational behind this study are strong, however, the authors could get out significantly more of their own data and hypothesis. Thus, major revision is recommended from my side.


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: ASSOCIATION BETWEEN THE NUMBER AND SIZE OF INTRAPULMONARY LYMPH NODES AND CHRONIC OBSTRUCTIVE PULMONARY DISEASE SEVERITY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Acceptable
Experimental design: acceptable

no issue here
Validity of the findings: acceptable
Additional comments: In this study , author describes association between IPN (size and number) and COPD severity. Author COPD severity as assessed by GOLD stage classification based on FEV1 correlates with the inflammation which may be associated with enlargement of IPN size and numbers .

Study is well designed and well presented . Figures and tables are clear. However , there is major concern;
-Older GOLD stage classification is based on FEV1 which is not the sole contributor of the COPD severity , 3 years ago new dimensions (rate of exacerbation and dyspnea index ) were added to the new GOLD classification . It will be very useful if authors of this paper has clinical data such as rate of exacerbation , hospitalization or dyspnea score for the correlation. If not then this should be mentioned as a limitation and in addition title should reflect that COPD severity was based on spirometric criteria.


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: ASSOCIATION BETWEEN THE NUMBER AND SIZE OF INTRAPULMONARY LYMPH NODES AND CHRONIC OBSTRUCTIVE PULMONARY DISEASE SEVERITY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Re-Review 4 Dec. 2019

The authors have not really addressed my concerns at all, as they also stated in their rebuttal letter. However, I can accept the manuscript in its present form since it is about an interesting topic and I agree with the authors, that some of my concerns would be too much for this kind of manuscript.
Nevertheless, at least the following points should be clarified:
•	A statement from your local ethic committee that the study is fine should be no big problem and would give the official approval to perform your study, which is in the interest of the analyzed patients, you as the authors and the journal you are planning to publish in
•	Was a statistician involved in your analyses? It sounds strange that the normality was not tested, this is also a simple test and should be performed anyway before further analyzing the data, there is no good reason for me not to do so
•	Why don’t you exclude PRISm from this GOLD 1 & 2 summery and let us know what happens than to the data?
In the end, I leave the decision to the editor. Unfortunately, my reviewers comment were not able to rise the quality of the present manuscript since not a single comment led to a change/improvement.
However, at least the above mentioned major concerns should be addressed in an adequate way.


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: ASSOCIATION BETWEEN THE NUMBER AND SIZE OF INTRAPULMONARY LYMPH NODES AND CHRONIC OBSTRUCTIVE PULMONARY DISEASE SEVERITY
Review round: 3
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have in part adequately addressed my issues. From my point of view, I would still give PRISM as own category, so I would prefer the in the rebuttal letter given figure.
EC issue is still not solved. I only know that an amendment to the already approved study should be no big problem. Maybe a call to your IRB would be helpful to ask for a written statement (which is no major issue and should grant to you that everything is fine). Otherwise, I can also accept the granted EC approval for the big study if the editor and Journal do so AND if this is the usual way to handle sub-studies derived from a bigger project in your country. Nevertheless, I know that our IRB would definitely ask for an amendment if a specific side-project is planned out of a bigger study to be published, but this might be different and less strict in another country.
Otherwise, everything is fine to me now.


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: ASSOCIATION BETWEEN THE NUMBER AND SIZE OF INTRAPULMONARY LYMPH NODES AND CHRONIC OBSTRUCTIVE PULMONARY DISEASE SEVERITY
Review round: 3
Reviewer: 2

Output:
Basic reporting: please see below
Experimental design: please see below
Validity of the findings: please see below
Additional comments: please see below


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: ASSOCIATION BETWEEN THE NUMBER AND SIZE OF INTRAPULMONARY LYMPH NODES AND CHRONIC OBSTRUCTIVE PULMONARY DISEASE SEVERITY
Review round: 4
Reviewer: 1

Output:
Basic reporting: na for this round
Experimental design: na for this round
Validity of the findings: na for this round
Additional comments: for me it is fine now, thank you and all the best


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: GENOME-WIDE ANALYSIS OF BASIC HELIX-LOOP-HELIX TRANSCRIPTION FACTORS IN PAPAYA (CARICA PAPAYA L.)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article should include sufficient introduction and background to demonstrate how the work fits into the broader field of knowledge. Relevant prior literature should be appropriately referenced.
Experimental design: Methods described with sufficient detail & information to replicate.
Validity of the findings: The data on which the conclusions are based must be provided or made available in an acceptable discipline-specific repository. The data should be robust, statistically sound, and controlled.
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: GENOME-WIDE ANALYSIS OF BASIC HELIX-LOOP-HELIX TRANSCRIPTION FACTORS IN PAPAYA (CARICA PAPAYA L.)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript entitled ‘Genome-wide analysis of basic helix-loop-helix transcription
factors in papaya ( Carica papaya L. )’ describes genome-wide identification of Carica papaya bHLH transcription factors downloaded from the Plant TFDB V4.0 database. The bHLH transcription factors were then analyzed bioimformatically, and their expression patterns after abiotic stress treatment by qRT-PCR. Together, the authors draw to conclusion that some important candidate CpbHLHs are be responsible for abiotic stress responses in papaya.

In general, the manuscript is well written, contains some fairly-novel results, and is appropriate for PeerJ.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript entitled ‘Genome-wide analysis of basic helix-loop-helix transcription
factors in papaya ( Carica papaya L. )’ describes genome-wide identification of Carica papaya bHLH transcription factors downloaded from the Plant TFDB V4.0 database. The bHLH transcription factors were then analyzed bioimformatically, and their expression patterns after abiotic stress treatment by qRT-PCR. Together, the authors draw to conclusion that some important candidate CpbHLHs are be responsible for abiotic stress responses in papaya.

In general, the manuscript is well written, contains some fairly-novel results, and is appropriate for PeerJ. I have only a few minor comments:

a.In the Background section, the authors introduced the background of papaya and gene family analysis in papaya only in two sentences. The authors should rewritten this part and cite more references such as below for reference citation.

Pan LJ and Jiang L. Identification and Expression of the WRKY Transcription Factors of Carica Papaya in Response to Abiotic and Biotic Stresses. Mol Biol Rep, 41 (3), 1215-1225.
Liu KD, Yuan CC, Feng SX, et al. Genome-wide analysis and characterization of Aux/IAA family genes related to fruit ripening in papaya (Carica papaya L.). BMC Genomics, 2017, 18:351.
Liu KD, Yuan CC, Li HL, et al. Genome-wide identification and characterization of auxin response factor (ARF) family genes related to flower and fruit development in papaya (Carica papaya L.). BMC Genomics, 2015, 16: 901.

b.Moreover, the authors should also show the cis-motifs in the promoter regions of putative orthologs in Arabidopsis genes to provide comparative aspects in the promoter regions as well as gene expression in response to abiotic stress treatments in the Figure 5 and 7.

c.The resolution in figure 4 is very lower, should be revised.


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: GENOME-WIDE ANALYSIS OF BASIC HELIX-LOOP-HELIX TRANSCRIPTION FACTORS IN PAPAYA (CARICA PAPAYA L.)
Review round: 1
Reviewer: 3

Output:
Basic reporting: Author used clear and unambiguous, professional English used throughout. They cited appropriate previous studies.
Experimental design: Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap. They performed detailed analysis in terms of bHLH in papaya genome.
Validity of the findings: They discussed most of the important findings in their results. Conclusions are well stated, linked to original research question & limited to supporting results.
Additional comments: Revise page 8, line 156.

Please use same style for gene and protein name.

How did you select stress conditions? Do you have any reference study?

How did you determine the genes studied in gene expression analysis with qRT-PCR?

Please discuss why most of bHLH genes gave responses to the all stress conditions?


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

Input:
Title: GENOME-WIDE ANALYSIS OF BASIC HELIX-LOOP-HELIX TRANSCRIPTION FACTORS IN PAPAYA (CARICA PAPAYA L.)
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The revised manuscript has been much improved and answered all my concerns. I have no more comments. I think the revised manuscript is suitable for publication in PeerJ.


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

Input:
Title: ADDRESSING INCOMPLETE LINEAGE SORTING AND PARALOGY IN THE INFERENCE OF UNCERTAIN SALMONID PHYLOGENETIC RELATIONSHIPS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript was well written and provided proficient review of relevant literature to support the claims. It has informative figures and appropriate associated supplemental data. Additionally it includes tables that help to follow the results of the abundant analyses conducted.

The authors make clear the purpose of their study, the history of the problems associated with Salmonidae and relevant taxon information, and provide an concise conclusion to their study supported by the data and results of there numerous analyses.

I only have very minor suggestions for Lines 228-229: I would simply add "under the assumption the subfamilies are truly monophyletic" in addition something along the lines of "which appears to be a sound assumption (citations)".
Experimental design: The authors have done an excellent job of providing rigorous phylogenetic analyses including coalescent-based methodology as well can concatenation-based. They have also experimented with data-matrix completely and tested different ways of partitioning the data used in analysis. Furthermore they have conducted phylogenetic topology testing. The level of phylogenetic, data set, and topology support testing is exceptional.

The only minor comment I have on methodology is on line 187: it is unclear how partitioning was accomplished for StarBEAST2 multispecies coalescent analyses. It is stated that substitution models were assigned using ModelGenerator, but was each locus treated as single partition? Or the entire alignment treated as a single partition.

This is certainly not required give the current rigor of the methods, but the authors may consider making use of the new UCE specific partitioning scheme, the Sliding-Window Site Characteristics, developed by Tagliacolo & Lanfear. Here is the reference: Tagliacollo, V.A. & Lanfear, R. (2018) Estimating improved partitioning schemes for ultraconserved elements. Molecular Biology and Evolution, 35, 1798–1811.
Validity of the findings: Given the extensive testing conducting, the authors conclusions are well-founded. The conclusions are concisely stated and are all well-supported by the analyses conducted.
Additional comments: The methodological rigor of this manuscript is above and beyond what I have seen exhibited in many recent phylogenomic studies. Additionally, the manuscript was well-written and includes highly informative figures that help make clear the necessity for such rigor. It was a pleasure reviewing your manuscript and your work is highly commendable.


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: ADDRESSING INCOMPLETE LINEAGE SORTING AND PARALOGY IN THE INFERENCE OF UNCERTAIN SALMONID PHYLOGENETIC RELATIONSHIPS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Addressing incomplete lineage sorting….salmonids

The ms is applies a set of UCE loci to selection of salmonid species with the aim of resolving several higher order phylogenetic questions.  Much attention is given to identifying problems related to incomplete lineage sorting, paralogy and tetrasomic inheritance.  The manuscript is very well written, and analysis carried out at a very professional level. The conclusions are mostly sound and well formulated, but their relevance to the body of literature as well as future studies is not clarified.
Additionally, the importance of both the questions and the conclusions, considering that similar or identical results have been already obtained, when sufficiently large data sets have been used is marginal.  In reality, the conclusions that the authors reached are based on a very small set (N = 6) of loci due to their stringent filtering and this raises the question of whether the applied loci set are more broadly applicable outside of this data set?  Additionally, the overall structural style and emphases outlined in the introduction could be improved.  The authors could perhaps balance the marginal importance of the data or conclusions by moving the analytical aspects of the ms more into the foreground, and address the potential applications of their analysis for other studies or study groups (see also comments below).  I also have a few minor questions concerning methodology, which I pose below.

Introduction
The ms poses at first very large questions (concerning e.g. the tree of life), and then discusses at length teleost duplication events, and above all gene-tree – species tree conflicts.  However, the study is rather focused on high-level relationships (sub-families or genera) of salmonid fishes, examined with a somewhat unique (UCE) set of loci.  In my view the abstract and introduction should more quickly prepare the reader for the focus of the article, and spend some time arguing precisely why this set of loci, and the accompanying analytical approaches may or may not be appropriate for the questions and problems at hand.  For example, the authors do not spend any time presenting the advantages or disadvantages of UCE loci?  Some background on why these markers were chosen and what their characteristics are, is required. What potential does this set of loci have for addressing similar questions in other groups?

At the end of the introduction the authors pose three phylogenetic questions concerning salmonid fishes, the relationships among sub-families, the monophyly of Coregonus, and the placement of Parahucho.  However, a major emphasis of the analysis, relates to theoretical and/or analytical hurdles concerning incomplete lineage sorting and genome duplication, and not the problem of resolving these relationships, which have been addressed in numerous publications.  Additionally, a major dilemma with the conflicting reports concerning these relationships relates to marker choice, which is slowly being overcome with NGS based data sets.  The authors should more specifically address this.  Another problem is taxon sampling, which the authors ignore somewhat (except for discussing one specific example, C. huntsman).  I do not get the feeling at the end of the ms, that the reader is well informed as to why these conflicts in results have occurred, and to what extent has this data set resolved the issue, as opposed to larger genome-wide sampling?  For example, has the application of mtDNA-based phylogenies for these questions led to misleading or congruent results? Has the application of nuclear markers to these questions led to misleading or congruent results?  Does (or would) the application of a large number (1000s) of nuclear markers overcome the problems that the authors outline, or is it necessary to consider incomplete lineage sorting and duplicated regions in all attempts at phylogenetic analysis of salmonid fishes, regardless of the number of markers applied?  How does use of UCEs help in resolving these problems?  The authors also mention “lineage-specific rediploidization” at the last sentence of the introduction (and again in the conclusions) with no explanation of what that is and its potential influence on phylogenetic analysis.  It is doubtful that most readers understand this concept, and whether or not it is being specifically addressed in the manuscript?  If this is one of the major hurdles posed for correct phylogenetic inference in salmonids (as the authors state), it would seem very important to know if they have successfully overcome this problem?

Methods
Authors correctly identify the problem with tetrasomic loci in salmonids, and attempt to address this problem by identifying a sub-set of their UCE loci in Atlantic salmon and rainbow trout that presumably lie in duplicated regions.  Are these regions specifically the so-called LORe regions discussed in Robertson et al 2017?  Please specify.  For the uninformed reader, it would appear that this problem only relates to duplication, but it is more complicated than that.  The authors should explain the lineage-specific nature of these events and how it relates to the WGD, and specifically how this then causes a problem for phylogenetic inference.  Lastly, the question of whether or not the identification of these regions in Atlantic salmon is sufficient for identifying such loci throughout the family is saved for comments in the discussion, but the problem is known beforehand and not a result of this analysis. Thus the authors should comment on this in the methods.

Conclusions
Here the authors mention “lineage-specific rediploidization” as a potential problem in their own data set (or at least with the number of loci increased beyond 6?).  This relates then to my comment on the sentence at the end of the discussion – elsewhere in the ms, this term does not appear.
The authors state that tetrasomic regions exist on 8 pairs of chromosome arms in salmonids.  Can they really say this?  Has this been explicitly shown outside of Atlantic salmon?  Perhaps for rainbow trout as well, but in other salmonids?  Considering the wide range in karyotype between both general and species, should this statement not be more narrowly defined to those groups where these regions have been specifically identified?
Experimental design: all comments contained under basic reporting.
Validity of the findings: all comments contained under basic reporting.
Additional comments: all comments contained under basic reporting.