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: FUNCTIONAL DRUG–TARGET–DISEASE NETWORK ANALYSIS OF GENE–PHENOTYPE CONNECTIVITY FOR CURCUMIN IN HEPATOCELLULAR CARCINOMA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article titled “Functional drug–target–disease network analysis of gene–phenotype connectivity for curcumin in hepatocellular carcinoma” (#61606) by Zhao Y et al., emphasizes on identification of FAN analysis underlying the connectivity between curcumin and HCC using Drugbank, STRING, CDC, and cBioPortal databases and we discovered the 360 connectivity between curcumin and HCC. They have identified five genes as curcumin targets using this network analysis.
Experimental design: The Methodology and the study design justifies the rationale of this work.
Validity of the findings: Overall, the findings were of interest to the peers working in HCC and other related cancers but there were several areas that need authors attention to detail.
Additional comments: As a reviewer from a reader’s point of view the below comments were made to improve the overall reach of this work.
Major concerns:
1.	The introduction is very short, and it is not adequately providing the background of the disease and the significance of the work. The authors may think of providing more information on several aspects relevant to this work like about HCC itself, statistics of this disease (# of deaths), which age groups are affected, gender differences if exist, factors leading to or effecting the disease, current interventions etc.
2.	Line 271: The RNA expression levels are highly significant in Figure 7C, but this did not translate to protein levels Figure 7D and 7E. Although the authors discussed a bit (Line 350) about this in discussion it is not satisfactory as the differences are huge.
3.	Line 271: Why did the authors exclude GSTP1 in checking protein expression levels like they have done for TGFb? In the RTqPCR data (Figure 7C) GSTP1 is also significantly low like TGFb? This need to be verified at protein levels.
4.	Line 271: Figure 7: The data that was shown here is for 20 µM concentration of Curcumin but in the original data/raw data in Supplementary Figures S2 they have shown data of 30 µM concentration. This is misleading and confusing and raises doubt on the quality of the data and results presented.
5.	Figure 7 and Supplementary Figure S2: The raw western blot image shown in Figure S2 and the Western blot image shown in Figure 7D are very different. This is a serious concern regarding the trustworthiness of the data presented.
6.	Figure 7A: The authors have seen a significant reduction in cell viability at 30 µM concentration and as early as 24 h in both Hep3B and HepG2 cells. In that case, it would be ideal to use these conditions for the further RTqPCR and protein expression levels. Testing at these conditions would provide an accurate answer for the differences they have seen at RNA and protein levels of TGFb.
7.	Figure 1B: What is the reason that all the other 4 genes are connected to GSTP1 and it is down regulated in Figure 7C? It would be interesting to investigate this gene at protein level
8.	Suggestion: It would be very helpful for the reader if the authors can provide a workflow of the different analysis they have performed as a flow chart with identification of genes at each step
Minor:
1.	Line 48: Correct “was” to “were”
2.	Line 53: Elaborate “MTT” in the first appearance in the manuscript text
3.	Line 60: Elaborate “OS” in the first appearance in the manuscript text
4.	Line 59: Replace special characters in the parentheses to commas
5.	Line 125: Elaborate FDR in the first appearance in the manuscript text
6.	Line 150: Cell Cook (Provide company details in parentheses)
7.	Line 155: Elaborate MTT in the first appearance in the manuscript text
8.	Line 159: CCK-8, what is this solution, provide details and elaborate CCK
9.	Line 160: Delete space between 4 h.
10.	Line 161: Delete space between 450 nm
11.	Line 173: Change “an” to “a”
12.	Line 177: Write ingredients in RIPA buffer
13.	Line 181 and 182: Delete space before and after parentheses
14.	Line 184: Which HRP-IgG secondary antibody is used from which company?
15.	Line 186: write company name of chemiluminescence system that was used?
16.	Line 195: Provide references for each activity like anti-tumor, antibacterial etc
17.	Line 196: Provide clinical trial number here.
18.	Line 234: Based on the Figure 3A the authors have identified 504 target genes by CTD but in the text they have mentioned 505. Correct the same.
19.	Line 244: The alterations of gene sets from 0-29% were not clear from the figure 4
20.	Line 254: Delete comma after GSTM1
21.	Line 258: 364 patients were involved. Please mention about the patient details in the materials and methods sections and include relevant approvals. Is this a clinical study performed by the authors?
22.	Line 265: The authors has mentioned that “For Hep3B cells, curcumin (10 μM) can significantly decrease cell viability after 24, 48, and 72 h” but in the data Figure 7A it is not significant for 24 h time point. Correct the same.
23.	Line 272: Change Rb1 to RB1
24.	Line 282: Change the font to italics to in vitro and in vivo
25.	Figures S1 and S2 and Tables S5-9 were not cited in the manuscript text. Cite them at relevant locations
26.	Line 315: Change the font to italics to in vitro
27.	Line 330: The font and size of the citation (Moreno-Caceres et al., 2017) need to be changed to match the test of the text
28.	Line 331: Change “Was” to “Were”
29.	Line 359: Correct the spelling of DrugBank
30.	Table 1: The gene functions are not correctly annotated to the genes. Please verify and correct
31.	Table 2: Either write Gene or Gene name. Maintain uniformity
32.	Table 3: Last row: add space between “and atherosclerosis”
33.	Figure 1B: There is only one type of blue line. No other type blue line is seen. Please change to contrasting colors rather than similar ones.


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: FUNCTIONAL DRUG–TARGET–DISEASE NETWORK ANALYSIS OF GENE–PHENOTYPE CONNECTIVITY FOR CURCUMIN IN HEPATOCELLULAR CARCINOMA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is well written and it has a good flow throughout. The article is easy to comprehend, with all the sections (abstract, introduction, experimental data and inferences) carefully planned and clearly described. The figures, raw data and supplementary material are in line with the journal standards. The citations are current and relevant to the study.  One suggestion that the authors could look into addressing would be in terms of reducing the words in the discussion section. It would be helpful if the discussion were made more succinct with less repetition from what has been described in the introduction/results sections of the article.
Experimental design: I commend the authors for the careful design and well-executed experiments, both in terms of the bioinformatics data as well as the in vitro experiments. The in vitro cell viability experiments lend proof of concept of the hypothesis and conclusions from the FAN analysis.
The study is supported by thorough analysis, explanation of the techniques used, their relevance and the inferences are sound. The FAN analysis described will be useful in further studies addressing effects of curcumin or other therapeutic agents in the context of multiple disease states.
Validity of the findings: The rationale for the inferences from the experimental data is very clear and practical. The inclusion of the Kaplan-Meier analysis and the in vitro experiments (cell viability and gene expression) certainly corroborate to strengthen the findings and pave way for future studies of effects curcumin in cancer.  One point I would like to raise with regard to the in vitro experiments are the protein expression levels of TGFB1. The gel images are not very convincing of the fact that curcumin has an effect on this particular protein expression, although curcumin does appear to have an effect on cell viability. The question I would like for the authors to address is if the protein expression was carried out at 72h timepoint wherein there is a significant decrease in cell viability. If the gel image is a representation of the experiments at 72h timepoint, I would suggest that the authors refrain from commenting/inferring much on the levels of protein expression modulated by curcumin. As the authors have rightly suggested, it may also be modulated due to factors/pathways independent of the curcumin related pathways.
The supplementary materials are very informative and provide sound justifications for the authors’ choice of following up on cancer-related pathways and HCC to dissect the therapeutic potentials of curcumin.
Additional comments: The study is relevant in terms of the experiments and the inferences made. The findings of the study do indeed provide valuable insights into the potential anti-tumorigenic properties of curcumin, especially in the context of HCC.
The study results are promising in terms of potential future studies related to the therapeutic effects of curcumin not only in HCC but also in other cancers, in lieu of the list that the authors have reported (supplementary materials) pertaining to cancer-related genes and biomarkers.


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: FUNCTIONAL DRUG–TARGET–DISEASE NETWORK ANALYSIS OF GENE–PHENOTYPE CONNECTIVITY FOR CURCUMIN IN HEPATOCELLULAR CARCINOMA
Review round: 1
Reviewer: 3

Output:
Basic reporting: In the manuscript (#61606) entitled, “Functional drug–target–disease network analysis of gene–phenotype connectivity for curcumin in hepatocellular carcinoma”, the authors have have aimed to explore the underlying mechanisms of curcumin and broaden the perspective of targeted therapies. They have used an extensive data-driven approach to support their experimental findings.
Experimental design: The reporting of the methods in the manuscript is robust and the overall manuscript and study  design is comprehensive and well thought through. The data presented/experiments performed are rigorous enough and does justify the conclusions.
Validity of the findings: The authors have performed rigorous scientific analyses with the help of multiple online modalities and databases and have performed various validation assays. The experimental findings are conclusive and very well supported by data. Enough experimental evidences have been given to support the results.
Additional comments: The authors have used a well-planned and comprehensive approach to come up with a logical conclusion and the manuscript is well written and can be published in its present form in this journal with some minor changes as detailed below.
The authors need to address the issue just one main issue about this manuscript and it is the language used. I could find many grammatical errors, typographical errors, punctuation mistakes, confusing sentences and a peculiar choice of words in many instances making the comprehension of data difficult. Thus the manuscript needs to be edited and prrof-read thoroughly.
Introduction needs citations to new articles especially with regard to the chemopreventive effects of curcumin.
Line 183 The samples were washed is incorrect, it should be membrane was washed.


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: FUNCTIONAL DRUG–TARGET–DISEASE NETWORK ANALYSIS OF GENE–PHENOTYPE CONNECTIVITY FOR CURCUMIN IN HEPATOCELLULAR CARCINOMA
Review round: 2
Reviewer: 1

Output:
Basic reporting: In the manuscript (#61606) entitled, “Functional drug–target–disease network analysis of gene–phenotype connectivity for curcumin in hepatocellular carcinoma”, the authors have have aimed to explore the underlying mechanisms of curcumin and broaden the perspective of targeted therapies. They have used an extensive data-driven approach to support their experimental findings.
Experimental design: The reporting of the methods in the manuscript is robust and the overall manuscript and study  design is comprehensive and well thought through. The data presented/experiments performed are rigorous enough and does justify the conclusions.
Validity of the findings: The authors have performed rigorous scientific analyses with the help of multiple online modalities and databases and have performed various validation assays. The experimental findings are conclusive and very well supported by data. Enough experimental evidences have been given to support the results.
Additional comments: The changes made as per the peer review have made the manuscript better and more understandable to the reader. Although, Line 200 The samples were washed is still incorrect, it should be membrane was washed. Please correct.


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

Input:
Title: IDENTIFICATION AND VALIDATION OF CANDIDATE GENES DYSREGULATED IN ALVEOLAR MACROPHAGES OF ACUTE RESPIRATORY DISTRESS SYNDROME
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, the authors identified several HUB genes thought to be related to the pathogenesis of ARDS. The chemokine receptor CCR2 and a formylpeptide receptor FPR3 were chosen because of their relatively higher level expression by macrophages as defined by data base search. The authors subsequently performed some in vitro tests using LPS-stimulated THP-1 monocytic cell line as a model of “ARDS macrophages”. The found increased expression of CCR2 and FPR3 by LPS stimulated THP-1 cells and siRNA silencing of FPR3 unexpectedly suppressed cell responses to the CCR2 ligand CCL2. Overall, this study contains potentially interesting contents, but there are some serious concerns.
Major concerns
1.	The data base mining is interesting and well performed. But the manuscript is in short of experiments for validation of established theories. A major problem is the authors did not use primary macrophages from patients and control subjects to measure gene expression levels, cell surface receptor density and signaling pathways that may confirm the existence of HUB networks to govern the progression of the disease. Use only THP-1 cell line as “ARDS macrophages” is inadequate.
2.	There is no mention of neutrophils, which are also one major cell component in the pathogenesis of ARDS, recruited by chemokines and cause tissue damage.
3.	The role of FPR3 is not well addressed. How FPR3 controls macrophage responses to chemokine CCL2 remains unknown, for instance, whether FPR3 in the context of ARDS may encounter any “endogenous” agonist(s) that may stimulate the receptor to transduce signals that cross-talk directly with CCR2 or indirectly through yet to be identified pathways.

Minor concerns
1.	It is conceptually erroneous to name fMLP(F) as a “chemokine”. Its receptors belong to a non-chemokine GPCR subfamily.
2.	There are a number of typographical and grammatical errors to be rigorous corrected in future forms of the manuscript.
Experimental design: The data base mining is interesting and well performed. But the manuscript is in short of experiments for validation of established theories. A major problem is the authors did not use primary macrophages from patients and control subjects to measure gene expression levels, cell surface receptor density and signaling pathways that may confirm the existence of HUB networks to govern the progression of the disease. Use only THP-1 cell line as “ARDS macrophages” is inadequate.
Validity of the findings: Doubtful, although potentially interesting.
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: IDENTIFICATION AND VALIDATION OF CANDIDATE GENES DYSREGULATED IN ALVEOLAR MACROPHAGES OF ACUTE RESPIRATORY DISTRESS SYNDROME
Review round: 1
Reviewer: 2

Output:
Basic reporting: Attention to language would benefit the manuscript. There is an overuse of the word “nowadays”; this term is not specific and not used properly.
Sentence structure and word usage is sometime not correct.
One example: “Despite the occurrence of several therapeutic strategies, the nowadays therapy for ARDS is disappointing” is a sentence that could be improved by giving specific details on current therapeutic strategies and rather than use the word “disappointing” use something like “ineffective” or “inadequate”.
Line 115: “By now” should be deleted/replaced… “Currently”

While there are some issues with certain parts of the manuscript as noted above, the Introduction contains good content, with an appropriate level of detail and background information.

The last section of the Results (lines 400-406) are written in a very confusing way and lack a summary statement.
Experimental design: This manuscript described a study using previously collected data from ARDS patients. These data sets examined lung alveolar macrophages and peripheral blood, with one data set being collected early during disease (day 1) and used as a prognostic metric by examining outcomes in the ICU. Overall, the details were described and referenced in sufficient detail.

The research question is focused on defining predictors of poor outcomes in ARDS patients and uses appropriate datasets.

To validate their findings using human gene expression datasets, they perform chemotaxis assays using THP-1 differentiated macrophages.
Validity of the findings: The authors merge to prior datasets to attempt to identify novel signaling networks that may be targeted to treat ARDS. Overall, data are accurately presented. The authors clearly qualify the findings where statistical significance is lacking, and appropriately temper conclusions.

The studies nicely build on human datasets and examine the biological consequence of CCR2 and FPR2 on chemotaxis.

The authors should provide more clear information on how their study goes beyond what was published using the previously published dataset and what was concluded and revealed in that manuscript.
Additional comments: The poor outcomes in ARDS patients is important and warrants investigation. The authors leverage datasets to examine predictors of poor outcomes and then attempt to validate their findings using in vitro assays and a monocyte cell line. Overall, the study is well-described and presented in the figures. There are several comments that should be addressed:

1.	There are a number of gene networks that were described as being increased that are somewhat confusing, such as B cell receptor signaling, and raise questions about the purity of the monocyte/macrophage cells collected. This should be commented on.
2.	G-protein coupled receptors emerged as a key potential player, though no significant differences were obtained in terms of outcomes (Figure 3E). It is not clear why/how these genes were chosen for follow-up. The networks depicted in panels A and B are not terribly easy to interpret and one suggestion is to show the expression data for all CCL13 receptors and CCR2 ligands.
3.	Authors include CXCL16 data in Figure 4. This should be evaluated in the human datasets presented in Figure 3.
4.	One of the key findings from the THP1 experiments is that silencing FPR3 seems to reduce CCR2 expression, though it is poorly summarized in the text. In general the authors do not provide much information or context to their interpretations of FPR3 and its role in ARDS.
5.	The authors should clearly articulate how this analysis/re-analysis moves beyond what was published in PMID: 30990758


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

Input:
Title: IDENTIFICATION AND VALIDATION OF CANDIDATE GENES DYSREGULATED IN ALVEOLAR MACROPHAGES OF ACUTE RESPIRATORY DISTRESS SYNDROME
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors made substantial effort to address the concerns expressed by this reviewer. The current version is now considered acceptable.
Experimental design: The approaches used by the authors to address the questions are reasonable.
Validity of the findings: The hypothesis and conclusions are reasonably made.
Additional comments: The authors have reasonably revised 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: IDENTIFICATION AND VALIDATION OF CANDIDATE GENES DYSREGULATED IN ALVEOLAR MACROPHAGES OF ACUTE RESPIRATORY DISTRESS SYNDROME
Review round: 2
Reviewer: 2

Output:
Basic reporting: Though the writing is much clearer in the revised submission, there are still issues with the manuscript in terms of language usage. There are spelling errors and incorrect grammar and punctuation.
Experimental design: The study builds upon a deposited gene expression data set. The deeper analysis was aimed at understanding the responses to acute respiratory distress syndrome and revealed the potential role for chemotactic signals. Overall, the research goal and the data analysis was described clearly.
Validity of the findings: The findings are clearly stated and presented. One concern is that the conclusions that CCR2 is important for pathogenesis is based on a correlation of it's expression and macrophage migration, and there is no evidence provided to conclude that CCR2 drives disease.
Additional comments: This resubmission addresses some of the original questions and criticisms, though there are still some concerns that should be addressed:
1. Writing and language usage needs editing.
2. The entire study provides correlative data only. The observation that CCR2 would mediate chemotaxis towards a CCL2 gradient is expected. There is no evidence that Ccr2 expression is actually "over-expressed" as stated on line 133, it's simply the expression after LPS challenge.
3. Data in Figure 4 are not convincing regarding the increase in CCR2 expression in ARDS patients. The MFI for CCR2 should be shown as the major difference really appears to be an increase in CD68+ cells. This should be discussed and is not clearly stated or summarized.


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: REMOVAL OR COMPONENT REVERSAL OF LOCAL GEOMAGNETIC FIELD AFFECTS FORAGING ORIENTATION PREFERENCE IN MIGRATORY INSECT BROWN PLANTHOPPER NILAPARVATA LUGENS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript titled "Removal or component reversal of local geomagnetic field affects foraging orientation preference in migratory insect brown planthopper Nilaparvata lugens" is a very interesting study about the effect of IscA1 gene on magnetoreception and deserves to be published in PeerJ. However, there are some errors and shortcomings, which are following as:
    Q1: Abstract: Methods: L23: “in magnetic field” should be changed as “under the controlled magnetic fields”.
    Q2: Abstract: Results: L23: L27-28: “...also affected the foraging orientation preference of N.
Lugens”  What about the magnetic fields?
    Q3: Fig.2: In the center of the cross-tube, no individuals of N. lugens remained (i.e., nonmoving individuals”? e.g., L148-150: The percentage of insects orienting to the north was 39.06%, which was significantly higher than that in south 14%, west 25.40% and east 21.39% (Fig. 3A). Total 99.85% individuals moved, and 0.15% individuals non-moved!
    Q4: Fig.3, Fig.4 and Fig.6: Why did you supply food source located in the north direction of the cross-tube, not S, W or E?
    Q5: There were some errors of languages and writing etc., e.g., in L16, "return" (returns);in L21, "reversing" (reversal); in L37, delete “which”. Other corrections were revised and marked directly in the PDF file.
    Q6: The result about the foraging orientation under reversal of the vertical component is quite interesting and distinguishable from previous study of planthopper N. lugens. Also please supplement the references by the newly published paper about altered migratory traits under changed GMF in the insect Ni. lugens by Wan et al. (2020a, 2020b).
Wan GJ et al. 2020a. Geomagnetic field absence reduces adult body weight of a migratory insect by disrupting feeding behavior and appetite regulation. Insect Science (https://doi.org/10.1111/1744-7917.12765)
Wan GJ, et al. 2020b. Geomagnetic field intensity as a cue for the regulation of insect migration. Biological Letter (http://dx.doi.org/10.1098/rsbl.2019.0940)


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: REMOVAL OR COMPONENT REVERSAL OF LOCAL GEOMAGNETIC FIELD AFFECTS FORAGING ORIENTATION PREFERENCE IN MIGRATORY INSECT BROWN PLANTHOPPER NILAPARVATA LUGENS
Review round: 1
Reviewer: 2

Output:
Basic reporting: First, overall the writing and figure presentation is quite well. In the following, I will propose some suggestions to improve the manuscript. The formatting of the manuscript is not uniform. I would suggest using uniform justified as style.
1. In page 3, add some transitional phrases between 1st and 2nd paragraph for a better smooth context.
2. In page 3, line 54: use full scientific names for the first time, and use abbreviations for the rest of generic names.
3. In page 3, line 54-55: list literature in the order of publication, and sic passim.
4. In page 3, line 58: change the word to either singular or plural form.
5. In page3, line 64-65: the phrase “since other mechanisms of navigation, foraging or homing are unavailable” is a bit arbitrary and should be modified appropriately.
6. In page4, line 83: check the publication date of literature.
7. In page5, line 98: change “27±1°C/26±1°C” to “(27±1) °C/(26±1)°C”.
8. In page5, line 102: should it be described as length or height for the rice seedings?
9. In page5, line 107-108: check whether the latitude and longitude symbols are correct.
10. In page6, line 123: indicate lumination intensity at the cross tube.
11. In page6, line 132: indicate detailed information of test insects such as age, sex or mating status.
12. In page6, line 140: indicate environmental conditions at experiments.
13.In page6, line 143: check the literature.
14. In page7, line 160: describe how the One-way ANOVA was used.
15. In page7, line 166, 170: mark the Chi-square value and P-value even it is not significant.
16. In page8, line 181: change the phrase “The foraging orientation preference of insects as influenced by the IscA1 gene knockdown” to “The IscA1 gene knockdown affected the foraging orientation preference of insects”.
17.In page9, line 197: add the literature.
18. In page9, line 203-209: the phrase should be reorganized.
19. In page11, line 251: the conclusion should better be reorganized for concision.
20. In page12, line 290: check all the references for a uniform style, and a correct citation for the literature “Cheng HN, Chen JC, His H, Yang LM, Chu TL, Wu CT, Chen JK, Yang CS. 1979. Studies on the migrations of brown planthopper Nilaparvata lugens Stal. Dialogue, 33, 164-167. DOI:10.1017/S012217300038932.”
Experimental design: 1. In the behavioral test, the physiological state of the tested insect should be described in detail, such as gender, age, mating experience, etc.
2. The q-PCR experiments has not been carried out following the highest standards (see the MIQE rules). And also add the reference gene for the q-PCR experiment and the calculation formula.
Validity of the findings: This manuscript  demonstrated that the near-zero magnetic field (NZMF)or vertical reversal of geomagnetic field (GMF) could lead to brown planthopper Nilaparvata lugens losing the foraging orientation preference, suggesting that a normal level of GMF was essential for the foraging orientation of N. lugens. Also, the authors silenced N. lugens IscA1 resulted in affected orientation preference of N. lugens, pointing out a potential role of IscA1 in the insects’ sensing the varying GMF. This observation suggests that a foraging orientation preference is associated with the GMF, and reveals new insights into the relationship between the IscA1 and magnetosensitivity mechanism in N. lugens. This result is very interesting, and the study seems to be well executed.
Additional comments: The authors should comment a little more about the experimental setup in the discussion as to connect the results with a possible interpretation involved in the individual test design.


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: REMOVAL OR COMPONENT REVERSAL OF LOCAL GEOMAGNETIC FIELD AFFECTS FORAGING ORIENTATION PREFERENCE IN MIGRATORY INSECT BROWN PLANTHOPPER NILAPARVATA LUGENS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The English was understandable, but could use some additional final proofreading to avoid confusion and improve clarity. I did not do a detailed proofreading of the text, but rather tried to focus on the scientific content.

Structure of the article and the flow of the information presented was appropriate.

Table 1 providing the q-PCR primer information was not cited in the text of the article.

Figures 3, 4 and 6 – The use of patterns/shading in the bar graphs is unnecessary. The bars are distinguished by the labels on the X-axis. The shading does not provide any additional information needed to interpret the graph.

Line 53. I think something is missing here. Did you instead intend to say altering the GMF causes misdirection?
Experimental design: The research question was well-defined. The experimental outcomes contribute to the understanding of responses of insects to magnetic stimuli and their use as environmental ques for movement, along with the underlying mechanisms involved in magnetoreception.

The protocols used to impose modifications of the geomagnetic field as treatments are well-developed and have been used to study insect physiological and behavioral responses to magnetic stimuli in several prior studies.

In several cases, more methodological detail is needed to better describe how the experiments were conducted and properly interpret the results.

Line 118. Please provide more detail about how the insects were introduced into the center of the cross-tube arena. Where they placed in individually? On an infested plant? Or perhaps collected from the rearing colony into a vial or cup that was then place in the center of the arena?

Lines 116-118. It is not clear where the food (rice seedlings) was placed during the initial choice trials. After reading the Results, it seems as though the plants were placed ONLY at the end of the north tube?  If so, then I assumed that the purpose of this first part of the trial was to provide food as a stimulus that the insects might associate with magnetic cues under the normal GMF, and the purpose of the second part of the trial was to test for a disruption of their ability to exhibit this learned directional preference when the GMF was altered. In addition to clarifying the position of the rice seedlings during the first trial, I suggest that you also briefly explain why there were two steps involved in the assays.

Line 134. Were the cross-tube behavioral trials for the RNAi insects conducted in the same manner as described in section 2.3 as part of a two-step trial?  Please clarify or explain how the assay was modified for the RNAi insects.

Lines 135-139. The description of the qPCR methods is incomplete. What were the housekeeping gene(s)? Has the expression level of the housekeeping genes been tested to be sure the expression level is constant when exposed to different GMF treatments? How was RNA extracted? Table 1 containing the primer information was not cited in the text.
Validity of the findings: The interpretation of the data seems to be confusing the use of magnetic stimuli as a cue involved in local foraging movements versus long distance migratory flights. The relevance of the study results to local foraging movements versus long distance migratory movements needs to be clarified in the text on lines 184-185 and 190-191.

Strictly speaking, the data shown in Figures 3 and 4 are most relevant to local scale movements associated with foraging for food. Related to my comment above about the behavioral assay methods (lines 116-118), I interpreted the intent of the first part of the assay with food to the north to provide the opportunity for the insects to associate magnetic field information under the normal GMF with the presence of food in a particular direction, and the second part was intended to test whether changing the magnetic field either by reducing it (NZMF, Figure 3) or altering it (component reversal, Figure 4) affected their ability to exhibit this learned directional foraging preference. Provided I did not misunderstand how and why the experiment was conducted, then interpretation of these results is directly related to the use of GMF stimuli in local scale foraging, not longer distance migratory flight. It doesn’t rule out the use of GMF in long distance flight, and indicates that the insects are able to detect and respond to GMF changes as imposed by your treatments, but your data better address GMF as a cue involved in local movement - which is nonetheless still very interesting.
Additional comments: All my comments are included in the other sections,


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: REMOVAL OR COMPONENT REVERSAL OF LOCAL GEOMAGNETIC FIELD AFFECTS FORAGING ORIENTATION PREFERENCE IN MIGRATORY INSECT BROWN PLANTHOPPER NILAPARVATA LUGENS
Review round: 2
Reviewer: 1

Output:
Basic reporting: As it is shown, the manuscript titled "Removal or component reversal of local geomagnetic field affects foraging orientation preference in migratory insect brown planthopper Nilaparvata lugens" has been addressed substantially for content and clarity by the authors, and this version has been revised based on the comments of the reviewers. I am pleased to recommend its publication in PeerJ.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: REMOVAL OR COMPONENT REVERSAL OF LOCAL GEOMAGNETIC FIELD AFFECTS FORAGING ORIENTATION PREFERENCE IN MIGRATORY INSECT BROWN PLANTHOPPER NILAPARVATA LUGENS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors addressed the points raised in my previous review.
Experimental design: The authors addressed the points raised in my previous review.
Validity of the findings: The authors addressed the points raised in my previous review.
Additional comments: I have attached an edited version of the manuscript with suggested grammatical corrections that I hope will be helpful in preparing the final version.


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

Input:
Title: IDENTIFICATION OF HUB GENES AND TRANSCRIPTION FACTOR-MIRNA-MRNA PATHWAYS IN MICE AND HUMAN RENAL ISCHEMIA-REPERFUSION INJURY
Review round: 1
Reviewer: 1

Output:
Basic reporting: This report uses published data sets to examine possible transcription factor-miRNA-mRNA interactions or roles in renal ischemia repercussion injury.  Overall, the presentation of the data us within the standards of the literature.
Experimental design: Published data sets were analyzed using a variety of on-line tools to examine how IR alters gene expression and its regulation.  The data analysis are straight forward.
Validity of the findings: The major issue with the paper is the lack of data showing experiment based independent validation of the differential expression patterns observed.  No data validating the importance of identified hubs are presented.
Additional comments: I don't think this report contributes much.  The authors should provide a more in-depth analysis to address whether the changes observed are IR specific.


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

Input:
Title: IDENTIFICATION OF HUB GENES AND TRANSCRIPTION FACTOR-MIRNA-MRNA PATHWAYS IN MICE AND HUMAN RENAL ISCHEMIA-REPERFUSION INJURY
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are not enough descriptions in figure legends in all figures. And some of them are not correct. Therefore, it’s very difficult to understand the results. The authors need to add more detailed descriptions in all figure legends.

Fig2A is not clear because the legends don’t have enough description. One sample per lane with data set number (at the bottom) is shown? One half is ISI samples and the other half controls in this heatmap? Legends say 32 DEMs but I see only 21 DEMs in this figure.

Fig.3C. In this study, RNA levels were examined. Therefore, protein-protein interaction doesn’t provide much information. It is better to search genes by initial genes in the pathways (as hub genes?).

Fig.3D. Because the details of MCODE module analysis is not clear, it is not sure if these genes are hub genes. Definition of “hub gene” should be described.  This study may just pick the proteins which interact with many proteins. Fig.3A suggests more TNF related genes but the identified hub genes here don’t match with them and even the genes identified in Fig.2A. It may suggest that the critical genes are not regulated by miRNAs. It is better to change the strategy to identify critical genes. Again, it is better to search genes by initial genes (as hub genes) in the pathways.

Fig.4. Did they analyzed all DEMs or only increased DEMs in IRI cases? According to Fig.4C, all miRNAs are increased DEMs in IRI. If so, decreased DEMs should be examined in the same way.
It is difficult to understand why they are in loop. They are simply pathways. Does it mean negative feedback regulation of same family TF mediated by miRNAs? Are there any examples of “positive” feedback? Positive feedback loops mediated by miRNAs were reported in kidney diseases not only IRI.

Fig.5. Because it is not sure if these genes are hub genes, the study doesn’t sound meaningful.
Fig.5A. If those TFs upregulates miRNAs, targets of miRNAs should be down regulated (negatively correlated). But all of them (TFs and targets) are positively correlated. This is another unclear part of this study.  Identified TFs and targets may be directly related and miRNAs may not be involved in the signaling.
Fig.5B is not clear, either. What is the meaning of “diagnostic” here? Is it related to IRI?

Fig.6. Why was the RNA-seq results used as confirmation? DEGs identified in this dataset (RNA-seq) may be analyzed like former analysis and get more targets? Again, same as Fig.5, these results may just show positive correlation of TFs and targets genes and miRNAs may not be involved (because no miRNA results are in this dataset (RNA-seq).
Experimental design: Definition of “hub gene” should be described. In this study, RNA levels were examined. Therefore, protein-protein interaction doesn’t provide much information. This study may just pick the proteins which interact with many proteins. It is better to change the strategy to identify critical genes. It is better to search genes by initial genes (as hub genes) in the pathways.

Methods
MCODE module analysis should be explained more.

Diagnostic value of genes and COR curve should be described more. Because Method is not clear, results are not so informative.

This study is based on mouse IRI model. Because human patient data (microarray or RNA-seq) should be available, comparison of the results the authors obtained with mouse data in this study with human data is encouraged.

The authors collected datasets of mRNA and miRNAs studied in mouse IRI models from publicly available databases and analyzed DEGs and DEMs and made connections from TF to miRNAs and mRNA (targets), and found some possible pathways involved in IRI. But all of them are correlative and not proved well by experiments. Testing some of the most important pathways by the experiments (in cultured cells) is encouraged.
Validity of the findings: As mentioned above, it is not sure if the genes the authors identified are hub genes. Reconsider the definition of hub gene and search for real hub genes (such as initial genes of the pathways but not based on protein-protein interaction).

Reconsider the definition of loop. They identified some signaling pathways but they are not in loop. If TF activate miRNA which targets the "same TF", it may be called loop. But miRNA targets TF but not exactly same TF.

In those pathways, TF activates miRNA which targets (downregulates) target. In this situation, TFs and targets should show negative correlation. But in this study, all of them showed positive correlation. It could be just direct regulation of targets by TFs and miRNAs may not be involved.
Additional comments: Title is misleading.
They identified pathways of TF-miRNA-mRNA but not TF-miRNA-mRNA. “Pathway” should be included.
They used mouse IRI models but not human patients. It is better to include “mouse models” of IRI.


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

Input:
Title: IDENTIFICATION OF HUB GENES AND TRANSCRIPTION FACTOR-MIRNA-MRNA PATHWAYS IN MICE AND HUMAN RENAL ISCHEMIA-REPERFUSION INJURY
Review round: 2
Reviewer: 1

Output:
Basic reporting: Revised manuscript has more descriptions and is easier to understand for readers. But because of that, more concerns have been raised up. I am not sure if continued transcription factor miRNA-mRNA pathways exist or not.

Several papers reported that miR-155 is upregulated in kidney injury and miR-155KO mice are protected. It is totally opposite of the authors’ conclusion.
Authors also discussed that miR-155 induces kidney injury in discussion. Such discrepancy should be discussed.
miR-192 and miR-200 family are upregulated in this study and also in previous reports of kidney injury. Those upregulated miRNAs should be discussed.

Many of Hub genes identified in this study and Fos/Jun family proteins are already known to be upregulated in IRI.

Overall, this manuscript doesn’t have much novelty but is just confirmation of known biomarkers identified by rescreening of publicly available RNA datasets (without any experiments using kidney cells). (confirming Fos, Fosl2, miR-155 and other RNAs as markers for IRI but no proof of regulation or pathways.)
Experimental design: The authors reanalyzed (correlation of the expression of DEM and DEG or TFs) the publicly available RNA datasets in human and mouse IRI (without any experiments using kidney cells).

Authors searched hub genes based on protein-protein interaction of predicted proteins from DEG in IRI and tested correlations of hub genes and IRI.
Validity of the findings: As also mentioned by authors, all of DEMs identified in this screening are down-regulated. It is quite surprising. Authors mentioned among 21 DEMs, only 7 miRNAs were up-regulated. But 7 out 21 is quite significant number. I don’t understand why they lost those 7 miRNAs in the analysis. TFs identified in this study are activators of transcription. But miRNAs DEMs in this study are down in IRI. It doesn’t make sense. Supplementary file 5 is not appropriate and not the evidence. Figures of correlation between TFs and DEMs (like TFs and targets) should be provided.

Authors used two databases, FunRich (http://funrich.org) and TransmiR v2.0 database. They need to explain how those databases identified TF for miRNAs. Simply expression or location of TF sites around miRNAs or experimentally proved?

As commented in the first review, this is a totally correlative study but no guarantee of regulation. Even if TF and DEM pair is found, that doesn’t mean TF regulates DEM. DEM may regulate TF identified in this study, too. It could also be just coincidence (no regulation for each other). Figures of correlation between targets and DEMs (like TFs and targets) should be provided.

Fig.5 & 6 just show positive correlation of TFs and target genes, but miRNAs may not be involved. Because same family TFs are both in TFs and targets, simply TFs increase target RNAs (same family). Again, it is difficult to understand why miRNAs are downregulated by those TFs (activating transcription).

Initial downregulation of miRNAs may regulate TFs (which could upregulate target mRNAs). It could be simply miRNA-TF (target) but not TF-miRNA-mRNA. Upregulated Fos and fosl2 and downregulated miR-155 can be markers for IRI. However I doubt if TF-miRNA- target pathway is real. It could be simply miRNA-target or TFs-targets (no miRNA involved).

Hub genes are identified by potential protein-protein interaction using RNA datasets (as translated proteins). Since the same family proteins are interacting each other, such proteins can be preferentially picked. It is difficult to be combined with microRNAs data although the expression of hub genes is correlated with IRI.

To make those concerns addressed, in vitro experiments are necessary, as also suggested by another reviewer. Especially Fos and JunB are positive TFs and upregulate gene expression. It is difficult to believe that Fos and Junb downregulate miRNAs. Again, figures of correlation between targets and DEMs should be provided. Fos or Junb may simply (directly) upregulate Fosl2 (without miR-155). Analyzing other RNA datasets doesn’t help at all.

I think experiments using cultured kidney cells should be done to solve this puzzle. Overexpression of Fos or Junb down (or maybe up) regulates miR-155 in cultured cells? miR-155 decreases Fosl2 and miR-155 inhibitor increases Fosl2 in in vitro culture experiments? Overexpression of hub genes changes the expression of those miRNAs and targets? Overexpression or inhibition of TFs or miRNAs changes the expression of hub genes?

Or (without in vitro experiments), tone down “hub genes and pathways” (should be excluded from title and abstract).
Authors should discuss at least four possibilities (not only the first one).
TF-miRNAs-Targets (very weak evidence)
miRNAs-TFs (can also upregulate targets)
miRNAs-Targets (can also be TFs)
TFs-Targets (without miRNAs)
(hub genes can be TFs or targets)

Therefore, the major conclusion and the title (pathways and hub genes) of this study are not supported by their results. This is just a reanalysis of publicly available RNA datasets confirming known facts (biomarkers of IRI).
Additional comments: It may be better to test (emphasize) interactions (or positive or negative correlation) of previously unknown DEM and DEG by experiments rather than confirming known DEM and DEG in IRI.

Based on the authors' current results, Title may be
"in silico confirmation of biomarker RNAs of human and mouse IRI by reanalyzing publicly available RNA datasets."

Typo in abstract
Fosl2 is correct but not "Fols2".


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

Input:
Title: IDENTIFICATION OF GENES AND GENE EXPRESSION ASSOCIATED WITH DISPERSAL CAPACITY IN THE MOUNTAIN PINE BEETLE, DENDROCTONUS PONDEROSAE HOPKINS (COLEOPTERA: CURCULIONIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper, “Identification of genes and gene expression…,” describes a study  that uses transcriptomic and genomic methods to identify differential gene expression and SNPs associated with flight behavior in mountain pine beetle. Overall, the methods are robust and appropriate, and the paper provides valuable baseline information to guide future, more targeted studies, and perhaps will have applications for understanding beetle spread in response to the warming climate. I see no major flaws in the paper, and I commend the authors on their rigor and clear explanation of the study.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I have just a few suggestions that might improve the text, and some other comments, below.

Abstract:
Consider changing the wording of the second sentence. “Transcriptomics” and “genomics” are the methods, not the biological basis for dispersal. Maybe “gene expression” and “genetics,” or something similar, would fit better here. Also, in the second to last sentence, your study did not test whether beetles are conserving energy before host colonization, so this could be stated less conclusively.

Line 22: Do all of the papers in the block starting with “Robert et al.” address host defenses AND reproduction? Or should some be placed after “host defenses” and some after “reproduction”?

Line 72: Thank you for making sure the study organisms is documented with physical vouchers.

Line 268: Could delete “relatively.”

Line 289, and elsewhere: Some of the differentially expressed genes, like in this section, are not necessarily a trait of a “strong flier” or “weak flier”, but more likely a consequence of the activity of flight. It is a subtle difference, and probably splitting hairs, but I wonder if some slight wording changes could help make this distinction. As worded, I could see that future studies might cite your paper, portraying this incorrectly.

Line 305-308. The first sentence here and the last phrase in the second sentence seem redundant.

Conclusion:
The concluding paragraph is well-written, and accurately describes the value of the study.

Figures 3, 4 captions:
Please define “GO” and “KEGG” here again for readers who might not see them in the text.


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

Input:
Title: IDENTIFICATION OF GENES AND GENE EXPRESSION ASSOCIATED WITH DISPERSAL CAPACITY IN THE MOUNTAIN PINE BEETLE, DENDROCTONUS PONDEROSAE HOPKINS (COLEOPTERA: CURCULIONIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: English is unambiguous and professional. The writing is perfectly clear.

References are well presented. Maybe I would like to see a bit more detail on what the evidence is based that provides a possible functional link of a gene to dispersal capacity and in what organism.

Figures are clear.

ddRAD and raw expression data should be submitted to a public repository as well.
Experimental design: Very elegant experimental design with well discussed findings.
Validity of the findings: Some additional context and discussion could be helpful (see below).
Additional comments: Shegelski and colleagues present a study on genes and their expression associated with dispersal capacity in the mountain pine beetle D. ponderosae. They do this by first collecting beetles and testing their dispersal capacity (distance) and propensity (frequency of initiating flight). Next, they identified low and high dispersing individuals and used these for a gene expression and association study. They find a set of roughly 3,000 genes differentially expressed between dispersal phenotypes of which many present strong candidates for a functional link with dispersal metabolism or morphology. Using ddRAD for variant calling, they also identified 3 SNPs close to 3 genes that strongly associate with dispersal capacity and may be useful in the future to identify flight capacity at a population level.

I found the experimental setup of this study very elegant and the result interesting and well discussed. My main questions relate to elaborating some discussion. I think the analysis and interpretation are mostly strong.

First, I was wondering what the degree of phenotypic plasticity is of dispersal capacity and whether anything is known about the heritability of dispersal capacity. If heritability is low, few associations may be expected. It is mentioned that dispersal capacity may change after colonization, but I think it would be helpful to elaborate on this. If little is known, it would be interesting to the reader to mention this.

Second, in insects, cohorts with different dispersal capacity are often described as dispersal syndromes with discrete difference, because so many genes and traits are generally involved. Is this also the case for the mountain pine beetle, or is a continuum of phenotypes observed? This also raises the question if there might be key regulatory factors that give rise to the development of these phenotypes. For example, JH expression could be a key factor resulting in the development of a high or low dispersal morph, with downstream affects on thousands of genes. I think this would also be interesting to elaborate on, as it could be an eventual goal to identify these developmental switches or triggers.

Third, I felt a little confused about not presenting the RAD data for all loci. L240-253: What happens if you run this analysis on all SNPs in the genome? Adaptation in gene regulation may happen at a respectable distance from the actual genes and if the reference genome is highly fragmented, you might be losing many true positives.

Minor questions:

L92: Is the difference in genes because of the sex chromosome being absent in females?

L136-145: Does this methodology compare to a strategy followed by GEMMA (https://github.com/genetics-statistics/GEMMA), which allows for accounting for relatedness between individuals (which might be important if beetles come from the same tree)?

Figure1: might be more striking to present both A and B with the same y-scale. My first impression was that they don’t differ much. This is not crucial, but the results from L147-167 could maybe also be presented here (as box plots?)

L168-217: I like the summary of these result, but I am maybe somewhat lacking details on how these genes have been demonstrated to affect flight functions in other species. Also in the discussion, it would be interesting to know from what organisms this evidence comes.

L218: Please check consistency of writing e.g., 1,000 or 1000.

L240-241: How do you go from 714 to 367 scaffolds. Did the others not include any SNPs?

L241: How many ddRAD loci do these contain?

L300: “believed to be adaptive” Can you give a little more info on why this is?


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: ASSESSMENT OF ANTIMYCOBACTERIAL ACTIVITIES OF PURE COMPOUNDS EXTRACTED FROM THAI MEDICINAL PLANTS AGAINST CLARITHROMYCIN-RESISTANT MYCOBACTERIUM ABSCESSUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, the research is carried out in a good way and the methods used are correct to achieve the stated objectives.
Experimental design: I consider that research has scientific contributions, especially in the treatment of microorganisms that are constantly acquiring resistance to conventional antibiotics.

Some considerations:

1.- Briefly explain why the toxicity tests of the compounds were performed on RBC and WBC and not on some other tissue.

2.- Is there any explanation or reference to why the compounds have a higher percentage of toxicity in WBC compared to RBC?
Validity of the findings: Line 269-272.
I suggest you discuss a little more about this topic and the results obtained that are shown in figure 1. And with that to reinforce whether or not there is a relationship between the morphology of the isolates and the susceptibility to the compounds and clarithromicin.

Line 284.
Why this reaction happens with the WBC and not with the RBC; is there any explanation or is there something in the literature about it?

This is important because of its role in the immune response.

Fig. 3. Place the measuring bar.

Line. 280. ...human RBCsThe plant  --> human RBCs. The...

LIne 68.
 Complete the medicinal effects of these plants. Is it known in the literature against which organisms they act?
Additional comments: Consider the suggestions displayed.


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: ASSESSMENT OF ANTIMYCOBACTERIAL ACTIVITIES OF PURE COMPOUNDS EXTRACTED FROM THAI MEDICINAL PLANTS AGAINST CLARITHROMYCIN-RESISTANT MYCOBACTERIUM ABSCESSUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors have investigated the antibacterial activity of several plant compounds and their effect cytotoxic effect. The compounds have a strong effect on various clarithromycin susceptible and resistant strains of M. abscessus. The study is well designed.  However, the introduction needs to be elaborated to put forth a clear and detailed literature review and its development in the field. The role of these plants in folk or cultural medicine and the previous research developments about them should be written with a conclusion of the significance of this study at the end of the introduction.  There are technical mistakes in presenting the data. The figures need editing and error bars to be depicted with clarity. The literature references are lacking appropriateness with methodology and findings. Other than that the work is divided into appropriate sub-sections of coherent linkages. The discussion part needs to be more coherent with results, the discussion of the findings with respect to already findings in the literature would broaden its standing and scope.
Experimental design: The experimental design is OK, methods need to be presented in detail to clearly understand the steps performed in a particular method. For statistical analysis, biological or technical replicates are a must, which needs to be incorporated in the methodology section. There is a discrepancy between methods and results.
Validity of the findings: The findings have been validated with sufficient experimental methods, though technical or biological replicates need attention. Raw data needs to be shared in supplemental. The manuscript is written in good English with few typo errors. The discussion needs to be more coherent and elaborate to increase its significance.
Additional comments: There are certain main concerns, which need to be addressed. Other minor comments are listed in the attached file.


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: ASSESSMENT OF ANTIMYCOBACTERIAL ACTIVITIES OF PURE COMPOUNDS EXTRACTED FROM THAI MEDICINAL PLANTS AGAINST CLARITHROMYCIN-RESISTANT MYCOBACTERIUM ABSCESSUS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Language and grammar:
The English language is fine, some paragraphs need to be rewritten in order to better understand the idea of the text. These are marked on the PDF.

Literature and background:
The information provided in the introduction is very complete and covers everything mentioned in the work. You need to organize some paragraphs and add some bibliographies. The references that are cited in the introduction are related to the subject of study, which gives greater validity to the work.
Regarding the discussion, they explain all the results they obtained at work. Each of the findings was analyzed and compared with other research articles. The literature included in this section is linked to the results, which gives more support to the work. It is only necessary to mention the Gram-negative and Gram-positive microorganisms that are inhibited by the action of clarithromycin and add some bibliographic citations that are missing to the discussion.

Structure, figures, and tables:
The structure of the article is good and follows the basic writing parameters for a research article.
Regarding the figures and tables, the titles and descriptions are accurate and are complete. However, it is necessary to organize Table 2, add the percentages that are analyzed in the results of the work. In the Figure 2 and 3 is necessary to add the statistical analyzes. In Figure 2 and 4 the graphs should indicate if there are statistically significant data. These are marked on the PDF files.
Experimental design: Research question:
The research question is well defined and congruent with the discussion and conclusions.

Rigorous investigation:
The approaches and methodologies used are appropriate to answer the research question. However, it would be interesting to do the study in animals. It would be interesting to see how invertebrate organisms such as Drosophila melanogaster, Galleria mellonella, Tenebrio molitor, among others, react to this type of compound. I also consider that characterizing the types of compounds would be interesting. Learn more about its structure. Develop pilot studies to determine whether or not these compounds can affect human beings.

Methods:
It is necessary to detail more some methodologies, and add bibliographic citations. These are marked on the PDF. A statistical analysis section is needed.
Validity of the findings: Underlying data:
The controls necessary to carry out the experiments were included.

Conclusions:
The conclusions mentioned in this work are related to the original research question.
Additional comments: In general, the research question and methodologies are interesting and appropriate, as well as the results obtained. In addition, they aptly discuss what was found. They also mention what their results mean and the importance of these. The bibliographic support they used is very good, since the references are related to the work. It is an interesting job. However, other experiments must be carried out to test the results in patients or other organisms.


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: PHYLOGENY OF CRATAEGUS (ROSACEAE) BASED ON 257 NUCLEAR LOCI AND CHLOROPLAST GENOMES: EVALUATING THE IMPACT OF HYBRIDIZATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: • The article is well written in good professional English, although I find it a bit too (unnecessary) technical in some of the sections.
• Literature references are sufficient and the context is well provided.
• The structure is ok, but there is a bit too much discussion in the results section.
• The figures I have seen in the pdf, have too low resolution. They are not publishable.
• In my view, one figure should be removed, as well as one of the tables. The figures need work and I have suggestions below.
• I have seen no indication in the manuscript that the data (as analysed) are publicly available.
• The manuscript is weak on its aims and the relevance of its analytical methods, but contains proper sections on results, discussion, and conclusions.
Experimental design: • I consider the manuscript to be within the stated aims and scope of the journal.
• The manuscript presents the background well, but not its aims.
• The methods used are presented in much detail, but not what they are expected to show.
• The authors do not present clear reasons for using some of the analytical methods.
• The study (is stated to) supplement earlier results by adding much more data of a new kind - and it does.
• The methods of analysis are partly described in sufficient detail, but not all of them. Some are not possible to replicate from the manuscript information (see below)

Regarding field study permits
I was specifically asked by the journal to check the author’s field study permits. I find this is not relevant. All accessions used (listed in table 1) were either previously published elsewhere or the collections made by collectors who are not authors.
Validity of the findings: No comment
Additional comments: In general, I consider the lack of clarity of the aims of the manuscript, and the methods to be its weaknesses. In simple terms: I want to understand why the study was performed, why these particular methods where used, and what they might be expected to show (or not) – and I do not find this clearly stated.

Judging from the title, the idea is to acquire 257 nuclear loci and most of the plastid genome, and use those data to evaluate the impact of hybridization in Crataegus. However, this is not quite clear from the text itself. The authors state what they have done, but not what the aims are (“Here we supplement the earlier results”), nor how the methods chosen were expected to bear upon the problem at hand.
It occurs to me, however, that if the problem was to test the hypotheses of hybrid origin of certain North American species, why not use phylogeny directly? Instead, some indirect statistical methods are used. The nuclear loci used were previously selected because they were putatively orthologous (ms line 134) in a wide range of Rosaceae species. This would mean that a relatively recent tetraploid could be expected to have two copies of each of these loci. The position of these in a phylogenetic analysis including both copies might indicate the origin of the putative hybrid. As far as I know, such a direct approach would have been novel in Crataegus, and might have given more direct results regarding hybrid origins.
The authors were using HybPiper (ms line 150), but apparently not its extension HybPhaser which was made for cases like this (https://www.biorxiv.org/content/10.1101/2020.10.27.354589v1). It is recent but available (https://github.com/LarsNauheimer/HybPhaser) and the manuscript should at least include a discussion as to why such a more direct phylogenetic approach was not considered. Although HybPhaser is new, the idea of phasing target capture datasets is not, and other pipelines have been published (e.g. Andermann et al. 2019). Instead, in this study, information that might bear on the hybrid origin of species was apparently discarded: “all ambiguous bases replaced with Ns” (ms line 152). (It is not quite clear to me from the manuscript, however, if this was only done in the six loci flagged as potential paralogs by HybPiper. This needs to be made more clear.)

There are unexplained inconsistencies in the methods that I think should be explained. For the ML estimations of the nuclear target capture data, the authors used IQ-TREE, but RAxML for the plastome data. Why? The authors of IQ-TREE claim that their program yields results with a better likelihood than does RAxML (and PhyML). Would that not apply to plastome data? The results were compared, and perhaps inconsistencies between plastome and nuclear data might be partly explained by using different softwares to estimate the phylogenies?

Regarding the alignments, it is stated that MAFFT was used (ms lines 154, 202). Although the version number was indicated, all other parameter settings were omitted and they may be of great interest to someone who wants to repeat the analyses. The developers of the MAFFT software have even simplified the settings of groups of parameters by including helpful short commands which might be cited (such as “linsi”), simplifying this. Also, since the alignments (both nuclear and plastome) are said to have been manually edited, the end products used for the analyses in the manuscript should have been made available in an open repository. I see no indication of this in the manuscript.

The authors used Astral-III to estimate species trees from multilocus data. As far as I know, Astral takes into account ILS – but not allopolyploidy. Still, the polyploid species/samples (that in several places in the manuscript are said to be allopolyploids: lines 113, 234, 243, 253, 388, 438, figure legends, table 2 etc) were included. I do not know what the possible effects are of including data that violate the models of the program in such a way, but since the authors use Astral-III under the circumstances, a discussion of this methodological problem is necessary at least (see below).

It is unclear what the “Neighbor-net” in fig. 1 is for. It is mentioned in the introduction, in the materials and methods section, but not in the results and whatever it shows (unclear) is never discussed.

The congruence of the gene trees to each other and to the previous classification was investigated, by using a number of (statistical) methods. It is difficult to evaluate this section because it it not very clear (to me) why precisely these methods were used and not any others – or what results might be expected. For example, regarding the calculation of tree distances, the authors say (ms line 287):
 “We calculated distances between our trees in order to display the variation they exhibit in the low-dimensional spaces of the first Principal Coordinates Analysis (PCoA) axes for which the proportion of variance accounted for by the axis exceeds that expected under the broken-stick model”. It would be helpful to get an explanation of what these calculated distances (as well as the other tree descriptors) are supposed to mean in relation to the aims of the paper.

The tree collapsing algorithm used (see comment to figure 2) seems not to always work well for the purpose it is being used when comparing the separate gene trees with the previous classification. This may constitute a problem for the interpretation of those comparisons.

Results

Plastome trees

Sweeping statements like “trees were generally well-supported” are not helpful, and thus should be avoided when in the diploids+polyploids tree (fig. 2D) almost half of the nodes have low support (marked by an asterisk in fig. 2D).

Gene trees

Most of the work on the gene trees focused on sorting and checking them with reference to previous classification (and the plastome tree). Apparently, this led to the selection of only 19 trees (out of 245) that showed “markedly high rtCF values” (ms line 368) which possibly indicates that they agreed well with the tree implied by the classification – although this is not made very clear in the results. This small sample of select trees (less than 8% of the obtained loci) were then further acted upon and some compared in detail. What was the rationale for this? Are they more “true” than the others so that the details are more interesting?

Phylogenetic invariants

The analyses of the species mentioned strongly suggests that they are intersubgeneric hybrids, apparently by “vanishing small p-values”. This description should be made clearer, because in most cases hypotheses are rejected when p-values are small. To understand, the reader needs to know what was being tested. It is not made clear in Materials and methods, nor in Table 3.

Multilocus trees

If there were allopolyploids in the analyses, is it not worrying that the coalescent trees where “highly concordant with the plastome trees”? In particular, if the analysis of phylogenetic invariants showed intersubgeneric allopolyploids to be present, would a strong agreement with the plastome tree be expected? I may be wrong, and I may have erroneously thought that “concordant” had to do with “congruent”.

In addition to the differences reported between that plastome tree(s) and the multilocus tree(s), “SANG Sang wilsonii s02” is resolved differently. In both plastome trees it is well supported in a clade with “SANG Nigr nigra s23”, while in the multilocus diploids only tree, it is well supported as sister to the other “SANG” samples. This is finally discussed at the end of the results section. There is actually a fair amount of discussion towards the end of the results section (line 435 and onwards) parts of which might be better to move to the discussion section.

Discussion

In the paragraph on lines 485–503, the causes of the tree heterogeneity is discussed. Although ILS was not rejected, it seems that hybridisation is the favoured cause (“all suggest that ILS has not been more important that hybridization”). I do not disagree with this conclusion, but the discussion would benefit from a more in-depth discussion of why the ILS test fails to reject ILS here, and which of the tests performed here might be of more general use. After all, as pointed out in the beginning of the discussion, results similar to these are not uncommon in phylogenomic studies. It would also be of interest to include a discussion of how such problems have been dealt with previously.
In this paragraph, it is of course a bit contradictory to (1) note that ILS is not rejected, (2) take that as support for considering the multilocus coalescent tree to be the most accurate estimate of the phylogeny, and (3) suggest that ILS has been less important here than hybridisation.

To reiterate a general comment above about the multilocus coalescence methods: Here it would be appropriate to discuss the possible effects when including allopolyploids in analyses such as performed with Astral-III, that possibly violate the models of the program. This is particularly interesting among plants where allopolyploidy is common. Perhaps it is not a problem, and the resulting tree is still the best estimate of phylogeny?

I still find the discussion about the Multivariate comparisons of gene trees obscure. This may be because I am not well enough versed in Principal Coordinates Analyses speak, but I would have liked to see something more understandable than (line 568) “We found that the related tree distances gave us the lowest dimensional summary of the diversity of tree topologies”, and the like.

Regarding the discussion on the position and ranking of the medlar, it is notable that although the plastome data (not surprisingly) yields a position in Crataegus for it like previous plastid data, the nuclear data (fig. 3, fig. 5) does not! What needs to be pointed out here is that since the apple was used as outgroup, and nothing else was sampled outside Crataegus, the nuclear data in this study has no bearing on the position of the medlar except that it is outside of Crataegus in the strict sense. If more taxa had been included, Mespilus need not have been sister to Crataegus, even.

Figures

All figures are of very low resolution and they contain visible artefacts from too much jpeg compression. They can not be published in this form.

Figure 1. The figure seems superfluous, except as general information. In the text it is only referred to in the introduction. It is not really used for anything and not reported as a result or discussed. In the Materials and methods section it is referred to as “Phylogenetic network”, which I think is incorrect.
The legend incorrectly claims the “tree” to be rooted. No, this shows an unrooted tree. Indeed, one of the branches connects the apple to the rest, but this does not mean that the tree is rooted.
The legend indicates the loci to be “low copy number loci”. Clearly, only a single copy is used here, and elsewhere “putatively orthologous” is used.
The description of labels is complex and unclear, and refers (sample numbers) to table 1 where they are hard to find. Similar (but not identical) labels are found in table 3. For easy comparison they should be identical, not just similar. I suggest that the authors use the same labels throughout.

Figure 2. The figure shows four trees. Two of these are relevant (A, D) while the two simplified are not (B, C), because the two former includes all information in the two latter. Also, B and C are confusing as they have been ladderized differently (outgroup at bottom instead of at top), and incorrect because they resolve nodes that are not supported (the node BREV+MESP+AMER+SANG in B, the node Brev+Mesp+Macr+Cocc+Doug+Sang+Sali in C, and incorrectly indicating Macr+Cocc to be sisters in C). I doubt that the collapsing algorithm used actually works correctly for the purpose it is used in this manuscript.
If B and C are retained, taxa need to be organised in the same way as A and D with outgroup to the same side and clades ordered in the same way. I am aware that this does not change the relationships in any way, but it should be done for ALL figures so that they can be more easily compared by the reader.

Figure 3. Here, for some reason, the figure order is different from figure 2: A and B shows the full trees, while C and D show the simplified trees. Like in figure 2, the simplified trees are unnecessary as well as confusing, being differently ladderized. Here also, tree A and B are drawn with the outermost node collapsed, while C and D are drawn resolved. Furthermore, the AMER and SAMG nodes have been rotated in tree B which is confusing. It should be like tree A (and trees A and D in figure 2) to increase clarity.
The last sentence of the legend distinctly looks like an editing mistake.

Figure 4. I am not sure if this figure shows more than the rather obvious “if you add more taxa the trees will change”. The legend is long, very complex and hard to understand due to lots of abbreviations. Although  long, the legends on the axes are still not explained (such as RT-PCo2 or PCo1-PCo28).
The legend above the scattergrams say “246 Diploid-only trees” and “245 Diploid+tetraploid trees”. Elsewhere, the corresponding numbers are 245 and 244, respectively. I assume that it is incorrect here?
The last sentence in the legend mentions that the trees were rooted before calculating distances. Why was this necessary? In which way would rooting affect the distance?

Figure 5. This is a very complex figure and it is so full of graphical elements that it is difficult to see the branching pattern. The word “cluttered” comes to mind, and I suggest that the authors consider not trying to show all of this in one figure.
In A and B, the clades AMER and SANG are rotated as compared to figure 2. They should be in the same order for easy comparison.

Table 1.
Is “stamen number per flower” relevant here? It is only shown in tables 1 and 2 and not mentioned or discussed in the text.

Table 2.
This table seems unnecessary. It is only cited once in the Materials and methods section and the information in it is not used or discussed.

Table 3. Legend is cut off.
It would be helpful to include a text on what H0 and H1 represents, not just that the “admixture statistic” is zero or larger than zero. So if the p value is low enough to reject H0, what does it mean? That the hybridization hypothesis is favoured? If this is the case, it would help the reader to say this.
The p-value for four hybrids is 0.0 in the table. Does this mean exactly zero? Could it mean 0.0001? I am unfamiliar with the usage.
The labels for samples here should be identical to those used elsewhere (such as in figure 1 etc). Here it is “s12riv” while in figure 1 it is “s12_riv”. I can guess that they are the same, but why make them different?


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: PHYLOGENY OF CRATAEGUS (ROSACEAE) BASED ON 257 NUCLEAR LOCI AND CHLOROPLAST GENOMES: EVALUATING THE IMPACT OF HYBRIDIZATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is an important contribution from an outstanding team of researchers. The work is technically sound, the methods are rigorous, and the interpretations are sound.  That said, I found the writing in many places to be quite dense and not accessible and engaging for readers outside of other specialists in Crataegus and/or the tree comparison methods. I understand that PeerJ does not consider possible readership an important criterion for publication; nonetheless, there are some aspects of the presentation that I think could be improved for clarity and precision in any case, as follows:
1. Lines 50-52: The last sentence of Abstract-Results (“Despite the high heterogeneity of individual gene trees, we corroborate earlier evidence for the importance of hybridization in the evolution of Crataegus.”) is quite general and not very informative, even for the Abstract. A more detailed and specific summary of the key findings regarding hybridization in the genus would be helpful.
2. Line 55: The construction “hybridization…has been contentious” is awkward; the question of the importance of hybridization has been contentious, not the process itself.
3. Line 61: The phrase “relatively early” is vague.
4. Lines 62-63: Use of present tense seems incongruous.
5. Lines 69-73: More detailed explanation of what past studies have shown, and how, would be helpful (though not necessary for those already familiar with these works).
6. Lines 79-81: Again, I think more specific details, especially examples of how the processes mentioned have contributed to “taxonomic complexity” would be helpful, but specialists may not find this necessary.
7. Lines 89-99: Perhaps I’m stuck on tradition, but I found the description of some details of methods and the citation of Figures depicting specific results of the study in the Introduction jarring.
8. Lines 556-576: This paragraph is very dense and focused on details of the results, rather than more general conclusions. It reads more like Results than Discussion.
9. Lines 578-607: Most of this paragraph concerns the question of whether or not Mespilus should be considered as a distinct genus from Crataegus, a subjective taxonomic decision given that the phylogenetic results are consistent with either treatment. The amount of space devoted to this one question that was not presented as a central focus of the study seems disproportionate.
10. Lines 611-630: Even in the Conclusions section, the descriptions are primarily focused on details of the Results rather than on big-picture “take-home” messages. On the other hand, the final sentence, especially the last phrase (“unforeseen consequences of methodological choices”) is so vague as to not be very informative.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: No additional comments


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

Input:
Title: PHYLOGENY OF CRATAEGUS (ROSACEAE) BASED ON 257 NUCLEAR LOCI AND CHLOROPLAST GENOMES: EVALUATING THE IMPACT OF HYBRIDIZATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: In my view the sequence alignment methods, in particular when using MAFFT, are not described in sufficient detail for replication. Using "default" settings and "auto" selection of algorithm is unfortunately a common practice, but it might make analyses difficult to replicate if default settings or method selection algorithms change in the future. I do not think this is a major problem in this case, however, as concatenated aligned data sets have been submitted to a repository.
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: MODERNISING TACTILE ACUITY ASSESSMENT; CLINIMETRICS OF SEMI-AUTOMATED TESTS AND EFFECTS OF AGE, SEX AND ANTHROPOMETRY ON PERFORMANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: English is of a very high standard although I would check the opinion provided by the native English reviewer, too. Only some references are missing that could complete the whole context of the study. I pasted them in the box "general comments". Figures and Tables are accurate and provided raw data seems to be correct. I was able to reproduce reliability coefficients according to analytical descriptions while doing a 'cross-check' of analyses. Methodologically sound paper.
Experimental design: Maybe a clear statement in the introduction about the gap in the literature would be a suggestion for improvement. The study is definitely of high ethical standards. Analysis and data are available for review. Regarding the description of the method, I found it very clear, only some procedural aspects are missing which in my opinion can improve replication of experiments (see comment in general comments).
Validity of the findings: Data are provided for review. Do authors plan to make them publicly available? I assume that the policy of the journal is to make access to the data easy and in the spirit of the open science framework. Conclusions should be extended by results of internal consistency analysis.
Additional comments: Thank you very much for the opportunity to review the manuscript by Olthof et al. It is an extremely interesting study that places the reinvigorated field of tactile acuity in the context of neck region and neck-related pain. The manuscript presents two independent studies, one with state-of-the-art reliability analysis of 2-point discrimination threshold and an innovative novel testing procedure that eliminates examiner and caliper-related error. The second study is dedicated to what authors refer to as the "internal consistency" of the test. The second study also targets factors that can potentially confound the results (e.g. mentioned floor effects).

In general, I have to congratulate the authors for this methodologically sound series of technical studies. Several novel aspects can be found here. In experiment 1, the iTAD has been contrasted in terms of inter-rater reliability analysis showing slightly higher ICCs for iTAD procedure than 2PD. I commend the authors for providing extensive reports including SEMs and different CIs possibilities while reporting SDC. In experiment 2, the authors found high internal consistency (ICCs > 0.84) and consistent pattern in prediction models: age and sex explained variance similarly in two calculated iTAD scores.

I have a few primary concerns that I think the authors can easily address:

i. Can the authors explain the importance of moving only one caliper tip having the other one 'fixed' in terms of stimulation site? Could it be that tactile corpuscles adapt heavily in the fixed site, leading to a larger discrimination threshold (as the subject could not feel that point clearly)? Where the mean and SD comparable to data from previous studies testing sensibility of the neck region? I would report it in the discussion. In addition, I really like how the whole protocol for 2PD is presented in the figure. I found it very informative and easy to reproduce.

ii. It is not clear from the description how the training of the raters was performed. Did they listen to instructions? Did they assess themselves as a part of testing? Or maybe there was another pilot form of assessment before the study commenced? It would be beneficial if the authors could add some more information, as it could further expand the existing literature on how to prepare the clinician for the assessment.

iii. ICC - measurement of the 2PD is actually being represented by the average of 4 runs. Would it be preferable to perhaps change the model? Also, I am wondering whether CoV (Table 1 data) should be calculated using the traditional formula with SD placed in the nominator instead of SEM (Lovie, 2005). Could the authors explain their choice or change the presenting method?

iv. The authors might consider discussing two aspects: a) some attempts have been made to make tactile acuity assessment automatic (for example: Frahm et al. 2021, Yokota et al. 2020). Can the authors contrast their results with mentioned methods?

v. I think it would be interesting to simply correlate 2PD data with iTAD data (btw. I think Apple will be very happy if the app for the device is released one day). It can further strengthen the paper by providing data on the validity of the novel test.

vi. In 2015 I thought that 2PD was a real horror. Many procedural aspects affected the outcome, thus I tried to somehow find alternatives. In the end, 2PD was winning as it is relatively easy and has a long tradition of application (since work done by Ernst Weber). Today I'm still struggling with this test and always return to the study by Tong et al. (2013). Maybe all of us failed. Maybe 2PD is too simplistic to measure discrimination over complex irregularities of receptive fields (Johansson & Vallbo, 1983). Could the grating-orientation-task be the abandoned solution? I would ask the authors to comment whether the iTAD has potential to measure acuity with a higher degree of internal validity compared to simple 2PD.

Small comments and suggestions

1. Introduction: "Patients with persistent pain typically demonstrate poorer tactile acuity than healthy controls, which is thought to reflect changes in somatosensory processing related to the condition" - authors might consider citing meta-analysis by Mark Catley (2014).

2. Were the locations for the measurements determined by each examiner separately? I would add this information.

3. The sample size description is very honest and transparently reported.

4. Lines 117 and 130: I would make consistent explanations as to why the acuity is better OR higher. Sometimes explanations refer to instances of "better acuity" and sometimes "lower acuity".

5. Was the assessor trained in study 2 as well?

6. "...values were somewhat better" - I would say " higher".

7. Tricky question: Do the authors think that previous intra-rater reliability would change with the updated prototype?

8. Mediations: Which was applied - Baron & Kenny method or Bootstrapping? (If so, the sampling should be reported).

References

1. Lovie, P. Encyclopedia of Statistics in Behavioral Science. (2005) doi:10.1002/0470013192.bsa107.

2. Yokota H, Otsuru N, Kikuchi R, Suzuki R, Kojima S, Saito K, Miyaguchi S, Inukai Y, Onishi H. Establishment of optimal two-point discrimination test method and consideration of reproducibility. Neurosci Lett. 2020 Jan 1;714:134525.

3. Frahm KS, Gervasio S. The two-point discrimination threshold depends both on the stimulation noxiousness and modality. Exp Brain Res. 2021 May;239(5):1439-1449.

4. Johansson, R. S. & Vallbo, Å. B. Tactile sensory coding in the glabrous skin of the human hand. Trends Neurosci 6, 27–32 (1983).


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: MODERNISING TACTILE ACUITY ASSESSMENT; CLINIMETRICS OF SEMI-AUTOMATED TESTS AND EFFECTS OF AGE, SEX AND ANTHROPOMETRY ON PERFORMANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: see comments to authors below:

Relevance of measuring tactile acuity at the neck is not made clear, Figure 3 appears redundant while figures showing the distribution of the individual scores is missing, raw data should be provided in a generic data format
Experimental design: see comments to authors below:

some methods details are missing
Validity of the findings: no comment
Additional comments: The study aimed at assessing clinimetric properties of the iTAD device for measuring tactile acuity with vibrotactile stimuli at the neck. Exp. 1 compared inter-rater reliability and measurement error between iTAD and more traditional two-point discrimination scores. Exp. 2 tested internal consistency and floor/ceiling effects of iTAD scores in a larger sample of n=100. In addition, relationships of iTAD scores with age, gender, BMI and neck surface area were tested. It was found that inter-rater reliability was moderate-to-good for iTAD and measurement error was lower than for TPD. Exp. 2 results showed high internal consistency, no overt floor/ceiling effects as well as a direct relation of iTAD scores with age and gender which was not mediated by BMI or neck surface area. Results are interpreted as showing suitability of iTAD device for assessing tactile acuity in clinical settings, in particular for assessing change in tactile acuity due to interventions.

Overall, I think methods-oriented studies like this are important to assess reliability and validity of psychophysical tests, but are somewhat lacking for tactile acuity measures. Thus, the present study is a welcome addition to the literature. However, there are several issues with the present manuscript that would need to be addressed in a revision:

Introduction:

The rationale why measuring tactile acuity at the neck is important or relevant (in a clinical context) is not clear. There are excellent alternatives to the traditional TPDT for measuring tactile acuity at the fingertip which outperform TPDT in terms of reliability and validity, e.g. the commercially available JVP domes introduced by Van Boven and Johnsen or tactile acuity charts (Legge et al., 2008, Percept Psychophys; Bruns et al., 2014, PLoS ONE). However, these measures are not discussed at all in the paper.

It might also be helpful to introduce the iTAD procedure (and how it differs from traditional TPDT) in more detail already in the introduction, I think that many readers will not be familiar with this method.

Methods:

There are a number of important information on the procedure missing that would be required if one were to replicate the study:

TPDT: What is the size/diameter of the two needles (the part that actually contacts the skin)? What was the approximate indentation depth and duration of stimulation?

It seems that one needle (as a control condition) was never applied, i.e. there were always two needles present and the correct answer would have been “two” in every trial?

Needle distance for ascending run is given (15mm, increasing with 5mm steps), but what about the descending runs?

What does "Before running the reversed direction, the distance was overshot by 10mm" mean? Does this mean that the start distance of subsequent run was determined by the reversal point of the previous run plus/minus 10 mm?

iTAD: no information regarding vibration frequency, strength and duration is provided

Trial procedure is not entirely clear, e.g. could only neighboring locations be activated in the direction task?

Section 2.1.2. participants Exp. 1: all essential information (number of participants, age and gender distribution, handedness) is entirely missing. Sample of Exp. 2 could also be described in more detail.

Figure 3 might be redundant because mediation analysis model does already become clear from Figure 4.

Results:

Unfortunately, any graphical presentation of the (individual) results is missing. For Exp. 2, it would be desirable to see the distribution of individual performance as a function of age (with gender color-coded).

For Exp. 1, an analysis of the relationship between TPDT and iTAD is missing. Arguably e.g. localization of one point on skin (as in iTAD localization task) measures a different property than discriminating one from two points (see e.g. Dinse et al., 2008, in Grunwald (Ed.), Human haptic perception). Thus, it would be important to establish the agreement between TPDT and iTAD measurements (i.e., do participants with high acuity in TPDT also show high acuity in iTAD?), in particular because the authors suggest the iTAD as a replacement of TPDT in clinical settings. Graphically, the agreement of the two methods could e.g. be shown using the limits of agreement approach introduced by Bland and Altman (see Bruns et al., 2014, PLoS ONE, for an example with different tactile acuity measures).

Discussion:

iTAD (unlike TPDT) was administered with an automated computer-controlled procedure. Thus, wouldn't assessor be expected to play less of a role than in TPDT? Yet ICC values are fairly similar between the two methods, I wonder whether this result actually indicates lower test-retest reliability (independent of assessor) than for TPDT?

Supplementary material:

Raw data is provided in SPSS format. A generic data format (e.g., txt or csv) would be preferable.


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: MODERNISING TACTILE ACUITY ASSESSMENT; CLINIMETRICS OF SEMI-AUTOMATED TESTS AND EFFECTS OF AGE, SEX AND ANTHROPOMETRY ON PERFORMANCE
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have done a great job in further improving their manuscript. All comments from the previous round of reviews have been addressed.