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: FORGETTING FACES OVER A WEEK: INVESTIGATING SELF-REPORTED FACE RECOGNITION ABILITY AND PERSONALITY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Before this study is published in PeerJ, I recommend revising certain sections in text in order to improve the current structure and to clarify certain points.

Introduction

1.	While you provide a comprehensive literature review on your constructs of interest (long-term face recognition, belief in ability and personality) you do not make it clear why this gap in the literature is important to address

2.	Line 113 – you do not specify here that you are referring to the belief in ability (as measured by the Prosopagnosia index) being associated with performance

3.	Line 163 – unclear what you mean by "ambient and unconstrained" images

Experiment 1

1.	Your intention to pick out the optimal stimuli from Exp 1 to be used in Exp 2 should be known to the reader sooner (e.g. Current Study section and introduction of Exp 1).

2.	Line 277 - it is an odd place to discuss your stimulus selection for Exp 2. It may be better off in the materials section of Exp 2.

3.	Please make a clear distinction between the old/new test and the questionnaire in your materials descriptions (e.g. with subheadings)

4.	It is unusual to have no mention of your planned analyses prior to the results section, for example, in form of a Design section, or at the very least, in the first paragraph of your results section.
Experimental design: Current Study

1.	You do not explain in your introduction or anywhere else in the manuscript why it is important to examine the relationship between face recognition ability across different delays and self-reported belief in ability as well as personality. Please contextualise your study and research questions to make it clearer why this gap in the literature is important to address. This should be highlighted again in the General Discussion.

Experiment 1

1.	Your intention to pick out the optimal stimuli from Exp 1 to be used in Exp 2 should be known to the reader sooner (e.g. Current study section, and introduction of Exp 1). Exp 1 is quite basic in design, where you merely make a similar observation as previous research (association between ability and belief in ability) and point out a well-established limitation (image recognition rather than identity recognition). Therefore, perhaps its role in stimuli selection for Exp 2 should be viewed as its primary purpose, and therefore should be highlighted at the start of Exp 1, not at the end.

2.	Line 281 - could you provide a brief comment in text justifying your selection criteria for identities to be used in Exp 2 i.e. why “the lowest and then every ninth identity across the range of values for hit rate”?

3.	If the images were extracted from videos, why not get two images for each identity to use across learning and recognition stages?

4.	Why such a short exposure duration of 1500ms? Also having these briefly presented images shown one after the other, without letting participants pace themselves, seems unnecessarily demanding for a learning task. Please clarify in text this design choice, as it does not seem to reflect “typical” identity learning or familiarisation

5.	How was the HK15 overall score computed and what did higher/lower score indicate? You may have mentioned it in the results, but it should be initially specified here. Please also provide the Cronbach’s alpha for the scale

6.	Line 253 - How many participants were excluded for reason a) and how many for reason b)?

Experiment 2

1.	Please provide all the relevant information on the TIPI scale in the materials section, i.e., item examples, response options, how scores were computed, Cronbach’s alpha scores, etc.

2.	Having 10 items to measure 5 personality types feels a bit limited. Perhaps you can add a line justifying the use of such a short measure, either in the materials section or the discussion.

3.	The HK15 should be included in the materials of Exp 2.

4.	Line 417 - please clarify in text how you categorised old and new responses from the 1-5 scale, and clarify what you did with response 3 “I don’t know”?
Validity of the findings: Results partially replicate but also extend previous findings in this area. The studies are generally well executed with good participant samples and sound data analyses.

1.	Other than having recruited participants with lower extraversion scores compared to the general population, what other explanations can you propose for the unexpected negative association between performance and extraversion?

2.	Line 510 - the possible role of sleep and wakefulness in memory consolidation is an interesting observation in relation to your findings. I would, however, restructure/rephrase these last 9 lines of the paragraph to make it clearer to the reader that your findings are in line with previous research looking into sleep and wakefulness effects on memory.

3.	Line 529 – Perhaps you could first specify why using a between subject design might be a limitation (other than a less powerful approach).
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: FORGETTING FACES OVER A WEEK: INVESTIGATING SELF-REPORTED FACE RECOGNITION ABILITY AND PERSONALITY
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: See general comments.
Validity of the findings: See general comments.
Additional comments: This paper examined the relationship between self-reported facial recognition ability and facial recognition performance (Exp 1), as well as the rate at which individuals forget faces over one week, and whether accuracy correlates with self-reported facial recognition ability or self-reported personality traits (Exp 2). In the first experiment participants learned unfamiliar faces, and then completed an old/new recognition task immediately after using the exact same images. In the second experiment, participants filled out self-reported questionnaires of recognition ability and personality, then saw video footage of unfamiliar participants and were asked to complete an old/new recognition task using new images hours or days later. Across the two experiments, the authors found that self-reported facial recognition ability had a moderate correlation with actual facial recognition ability, and that extraversion had a small negative association with facial recognition performance. In Exp 2, recognition accuracy dropped substantially within 1 day but did not show evidence of further decline after 7 days.

Overall, the paper investigates research questions that are timely and of interest to the field. However, there are some issues that would need to be addressed before recommending publication.

MAJOR COMMENTS
The introduction sets out two aims: forgetting faces over time and the relationship between self-reported measures of ability and personality with face recognition accuracy. It’s not clear why these two things were investigated in the same paper – are they conceptually related? The only time the author links the two is lines 454-456, and only to note they don’t interact. Would you expect them to? If not, why investigate both questions at the same time? The conceptual framing of the paper needs to be more cohesive.

The author should strongly consider removing Experiment 1 from the paper. Experiment 1 uses the exact same images at learning and test. As the author notes (lines 297-303), this is widely considered bad practice because the test taps into low-level image recognition, not face recognition. The fact that the experiment “worked” (i.e. the sig correlation between perceived and actual performance) does not get around the issue. These days, there is really no justification to use such a design to investigate face recognition, and so meaningful conclusions cannot be drawn from the Exp 1 data.

There is a potential ethical issue in this study. How long did participants take to complete the experiments? The payment of US$0.75 for each part seems very low. I believe the standard/ethical rate is US$1-1.35/10mins (i.e. $6-$8/hr).

MINOR COMMENTS
Introduction
•	The introduction focuses mainly on forgetting over time, so it comes as a surprise that Exp 1 only focuses on the relationship between perceived and actual face recognition ability.
•	Lines 36-42: The first paragraph of the introduction is very clunky. The concept of face familiarity as a continuum and the difference between familiar and unfamiliar face processing are two separate ideas and the link between them is unclear.

Results: Experiment 1
•	Lines 277-288: It’s unclear why this section is in the Exp 1 results, before the discussion of Exp 1 findings, and before the reader knows what Exp 2 is. The author should move this to the Method section of Exp 2.

Method: Experiment 2
•	Were participants asked about the languages they speak? Although the author tested English native-speaking countries and confirmed participants’ ethnicity, this does not necessarily mean they speak English as their first and/or only language.
•	Was the author able to identify which participants had sound turned on during the learning task. Could this have impacted the findings?
•	Why were the HK11 and personality questionnaires administered before assessing facial recognition abilities? Could providing the questionnaires prior to face tests have alerted participants to the purpose of the experiment, or affected the results in some way?
•	Lines 329-332: It should be made clear to readers that the pyMTurkR package is used to send messages to participants inviting them to complete part 2 – phrasing of “maximising likelihood” is ambiguous otherwise.
•	Line 373: Was the attention check provided via audio or shown as text on-screen?
•	Lines 398-399: The delay conditions are only explained here, but are referred to earlier in line 377, 362 and 333 without any explanation.
•	Line 397: “logistical reasons” is unclear. Why weren’t participants randomly allocated to delay condition?
•	Line 401: What does “until participation was exhausted” mean?
•	Lines 406-409: Why were participants from Australia and New Zealand, but not other countries, excluded from the six-hour and twelve-hour delay conditions?

Results: Experiment 2
•	Lines 438-440: More detail as to what predictors were and were not significant would be helpful. Related, it would be helpful to mention in the body of the paper what results are important to take away from Tables 2 and 3.
•	Lines 452-454: This finding, as well as other correlation measures, were not clearly stated in the results section of the paper.
•	Lines 441-442: It would be informative for the reader to present some measure of how well the projected learning curve fit the data points plotted.

General Discussion
•	Could the authors please clarify if this work is the first demonstration of the forgetting curve for facial stimuli?
•	Lines 512-513: It would be helpful to include the point in brackets in the method section.
•	Lines 528-540: It’s unclear why this paragraph has been included in the discussion. Why raise an alternative design only to thoroughly explain why it’s a bad idea?
•	Lines 507-508: Repeated use of “indeed”.


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: FORGETTING FACES OVER A WEEK: INVESTIGATING SELF-REPORTED FACE RECOGNITION ABILITY AND PERSONALITY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: FORGETTING FACES OVER A WEEK: INVESTIGATING SELF-REPORTED FACE RECOGNITION ABILITY AND PERSONALITY
Review round: 2
Reviewer: 2

Output:
Basic reporting: See general comments.
Experimental design: See general comments.
Validity of the findings: See general comments.
Additional comments: The author has carefully revised the manuscript and addressed all comments. I am therefore happy to recommend publication.

The author may wish to consider the following suggestions to improve clarity:
•	Line 443-444: Consider removing brackets.
•	Lines 519-522: Explanation regarding “representational” and “decisional” components is unclear.
•	Lines 526-528: Sentence explaining how AUC quantifies a classifier could be clearer.
•	Lines 559-560: Sentence in brackets is confusing and could be removed.
•	Lines 659-661: Consider removing brackets.
•	Lines 681-682: Sentence regarding random distribution is a confusing justification for the design choice.
•	Line 632: The author noted that extraversion may be comprised of two sub-components and may therefore make the measure difficult to interpret. Why does the author believe this? For example, does the author believe specific elements of extraversion may map onto facial recognition better than others?


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: NACRE MORPHOLOGY AND CHEMICAL COMPOSITION IN ATLANTIC WINGED OYSTER PTERIA COLYMBUS (RÖDING, 1798)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is concise and clearly written in a sufficiently correct English.
The Reference format is not that requested by the Journal.
The figures are well done but there are no captions to the figures.
Experimental design: The research topic is within the scope of the journal.
The methods are described with sufficient detail and the investigation conducted in a rigorous manner.
Validity of the findings: no comment
Additional comments: Just a few specific comments:
- the technique used is the powder XRD, so I would add the word powder at line 79 and throughout the text.
- At line 92 please correct Briker with Bruker.
- Please rephrase the sentence at lines 152-155.


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: NACRE MORPHOLOGY AND CHEMICAL COMPOSITION IN ATLANTIC WINGED OYSTER PTERIA COLYMBUS (RÖDING, 1798)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper by Santana and Aranda reports a preliminary characterization of the structure of Pteria colymbus oyster shell by using an appropriate set of experimental techniques. The results are sound and, in my opinion, this work can be published after only minor revisions as outlined below.
Experimental design: In the Materials & Methods section, the Authors say that six 1 cm2 samples were cut from the shells.  For sake of reproducibility of the experiments, a sentence on how powder samples for XRD and FTIR measurements have been prepared should be added.
Figure 4 reports the XRD pattern of nacre powder. However, the spectrum presents few reflections and it resembles the spectrum of the nacre from mussels, while it differs from the XRD spectrum of powdered mussel shells, as reported by Ren et al. (see reference list). The Authors should add a comment about this (i.e.: does it depends from a different grinding procedure?). Figure 4 should also report the position and indexing of aragonite reflections present in the reference ICDD card (no. 76-606) for comparison.
The title of the X-axis of Figure 4 is better written as 2θ.
The title of the X-axis of Figure 5 is wrong. It should report wavenumbers in cm-1. Also, the Y-axis of this figure should read as just “Intensity” or “Intensity / a.u.”
Validity of the findings: As stated above, the findings of this study are valuable and should be published.
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: UTILIZATION OF SOIL RESIDUAL PHOSPHORUS AND INTERNAL REUSE OF PHOSPHORUS BY CROPS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This review entitled Utilization of soil residual and reuse of P within crops addressed some ideas to ameliorate the P deficiency in the soil and to optimize its use for plants.
This unreneable nutrient is essential for plant growth and productivity and its dependency has been increased worldwide.
This review brings an important discussion on the subject.
Experimental design: Some concerns
Line -173 - The authors said that the intercropping and crop rotation reduce the competition of soil P by enhancing the secretion of phosphatases. The question is: what does it mean? The phosphatases from different crops in the soil will be accumulated? Or organic P will be accumulated then mineralized?

Line 195. What would be the optimal planting? Crops rotation? Intercropping?
Organic P fertilization promotes lower amount of adsorbed P than mineral P fertilization in the soil? Why?

Line-289 Plant senescence decreases RNA, even in the grain production? Where a large amount of protein are being produced?

There are some English mistakes throughout the text.
Validity of the findings: This manuscript is a review. The discussion about the subject is very good. Some good ideas to optimize the use of P in the agriculture were presented.

I think the authors should use more current references than only old references.
Additional comments: The subject is so important. There is a lack of information and practices how to increase the P efficiency in the crop production.  The demand of this essential nutrient has been increased worldwide and this review brings a great discussion.

I think the authors should use current references and answer some concerns cited 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: UTILIZATION OF SOIL RESIDUAL PHOSPHORUS AND INTERNAL REUSE OF PHOSPHORUS BY CROPS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The review brings information about phosphorus (P) utilization from soil, specifically about residual P that remains adsorbed in soil particles and is not readily available for plant absorption. I think that this is a relevant subject and a review about this theme would be of great interest. The text provided by the authors brings important information, however, significant deficiencies were detected.
English language needs to be revised by professionals.
References used are most too old and more recent findings must be included.
Here I present some comments on the text, and the authors can find more details in the attached file.

Line 41: 13,19x108 hm² = 13,19x108 hm²? – This information has no reference.

Line 88: Actually, P provided by fertilization is not absorbed by soil particles, but adsorbed. The adsorption occurs when soluble P components become unavailable to the plants because they perform covalent bonds or electrostatic interactions with soil particles, or, they can convert to insoluble forms by precipitation. Several references can be included explaining this mechanism.

Line 89: What do the authors mean with “difficult to use?”

Line 100: I think it is important to state a definition for “residual P” here. The authors based much of the text in this concept but a proper definition is not presented.

Line 121; line 133: As a suggestion, it would be very interesting that the authors include more information about the solubilization of P by microorganisms. Several bacteria and fungi are able to produce organic acids, phosphatases and also phytases (not mentioned by the authors) which play essential role in the uptake of insoluble P forms to the plants. The future of “residual P” from soils for agricultural purposes certainly involves the use of microbes as main partners, thus, the theme fits in the text and would enrich the research even more. In this case, the subtitles should be reconsidered and the sections about inorganic and organic P utilization can be merged for a better understanding.

Lines 144-145: I suggest to make it clear that this enzyme is produced by the plants. The paragraph before mentions microorganisms. It can cause doubt in the way it is.

Lines 146-148: As it is stated in these lines, the reader can conclude that this enzymatic activity in the rhizosphere is only due plant metabolism, while the true is that microbes (fungi and bacteria) are also deeply involved in this process.

Lines 150-157: Several points caused doubt in these lines: 1) the authors indicate that plant phosphatases are the main enzymes involved in P uptake from P-deficient soils. Is that right? 2) If this was correctly stated, the example at the lines 155-157 is not in accordance, because it describes microbial action under low P conditions, and the authors just mentioned above that microbial action is responsible for aiding in P uptake from P-rich soils. 3) The authors can find in a generic research in scientific databases, uncountable researches describing that microbial inoculation is effective under low P conditions. In a significant frequency, microbial inoculation overcomes P uptake in relation to control treatments (with no microbial solubilizers). I think that this paragraph transmits a wrong idea and the authors should perform a deeper research, including a higher number of studies, and so it would be possible to better discuss the idea presented here.

Lines 192-193: Again, several references in this paragraph are old and more recent ones should be included to confirm the information. Specifically in these lines, crops like maize, wheat and soybean, for example, are submitted to constant crop breeding, which means that many characteristics can change. It is important to be sure that crop breeding did not affect these properties and I suggest the search for recent references which confirms this information.

Lines 213-215: The sentence has no sense. I did not understand.
Experimental design: Using the term “P cycle” to perform a research at the Web of Knowledge database, 718 results were provided, and only 8 results for “Soil residual P”. When a review is proposed, the reader expect to find important information about a subject, presented with information from the past and, especially, with the most recent findings about it. This review contains good information, but is superficial, basic, with few examples in many parts and based at most in old references. A deeper research is necessary and maybe to change the terms used for the search in the databases will be also necessary. I’ve found a great difference using “P cycle” and “Phosphorus cycle”, for example. I would also suggest other terms as “P solubilization” and “P uptake” which will bring new references that can complement ideas and provide information for a more consistent review.
Validity of the findings: Lines 331-335: The “Conclusions” section is overall redundant and the authors should improve it, merging important information and presenting their opinion in a really conclusive way. Specifically, at the mentioned lines, the authors presented referenced information, and this can not happen here. This must be included along the text in a pertinent subsection.

This is a relevant review. I encourage the authors to perform the improvement of the text to publish it.
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: UTILIZATION OF SOIL RESIDUAL PHOSPHORUS AND INTERNAL REUSE OF PHOSPHORUS BY CROPS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors accepted suggestions and answered our concerns accordingly.

I consider that this manuscript could be accepted for publishing.
Experimental design: The study design is appropriate
Validity of the findings: The study design is appropriate
Additional comments: The authors accepted suggestions and answered our concerns accordingly.

I consider that this manuscript could be accepted for publishing.


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: UTILIZATION OF SOIL RESIDUAL PHOSPHORUS AND INTERNAL REUSE OF PHOSPHORUS BY CROPS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors performed a great improvement in the text.
English language is now clear.
The review is now well structured, with good and recent literature embasing the text.
All requirements previously stated were carefully answered by the authors.
As I mentioned before, the issue of this review is of great importance nowadays, and I think that now this review will be useful for scientific research. Congratulations for the authors for thwy good job.

I've dettached in the text only some points with grammar mistakes. After correction, the paper is suitable for publication in my opinion.
Experimental design: Please see comments on Basic Report.
Validity of the findings: Please see comments on Basic Report
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: UTILIZATION OF SOIL RESIDUAL PHOSPHORUS AND INTERNAL REUSE OF PHOSPHORUS BY CROPS
Review round: 3
Reviewer: 1

Output:
Basic reporting: The points indicated to the authors were corrected. The review is now complete and the text is suitable for publication in my opinion.
Experimental design: See Basic Report.
Validity of the findings: See Basic Report.
Additional comments: See Basic Report.


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: ASSESSING THE DIVERSITY OF WHITEFLIES INFESTING CASSAVA IN BRAZIL
Review round: 1
Reviewer: 1

Output:
Basic reporting: Cassava (Manihot esculenta Crantz, Family Euphorbiaceae) is a tropical food crop for about a fifth of the world’s population, and one of the most efficient crops for converting solar energy to produce carbohydrates. Cassava mosaic geminiviruses (CMVs) cause cassava mosaic disease (CMD). Beside of where they origninated from African, in the last few years, there are a few reports about CMV expanding invasive infection in new counties of SouthEast Asia and East Asia, including Cambodia,Vietnam, China and so on ( Wang HL et al. Plant Disease 2016, Wang D et al. Plant Disease 2018,Minato et al. PLoS One 2019). CMV not also could infect cassava, but also jump into new host such as Jatropha curcas, an euphorbiaceae biofuel crop (Gao et al. Arch Virology 2010, Wang et al. Virus genes 2014). Therefore it is important to surveillance for invasive CMV in new world such as Southern Amercian, eg. Brazil. This work has its importance to be published in PeerJ. I suggest they include recent references listed above. Esp. the fact that there are at least two CMVs detected in China (Wang D et al. Plant Disease 2018, Wang D et al. Phytopathology Research 2020) are thought to be root-stock originated from Cambodia. The authors may discuss alternative transmission way instead of whitefly vector, but rootstock and international importing. They further confirmed that scucess virus transmission from the symptomatic cassava by viruliferous whiteflies Bemisia tabaci MEAM1 (Middle East-inor 1, formerly biotype B) into tomato (Solanum lycopersicum, Moneymaker) or Arabidopsis thaliana (Col-0). Importantly, both of two groups failed to detect any geminivirus with the universal primers PA/PB (PA,5’-TAATATTACCKGWKGVCCSC-3’; PB, 5’-TGGACYTTRCAWGGBCCTTCACA-3’) (Deng et al. 1994) on  symptomatic cassava, suggesting the tranditional primers and method may not be suitable for detect all geminiviruses. Wang D et al. Phytopathology Research 2020, provided an improved primers for rapid detection method.
Experimental design: The authors should tune down their claims and also better to discuss alternative explainations on their results based on several published researches.
Validity of the findings: They'd better to use optimized primers developed in Wang D et al. Phytopathology Research 2020,  for rapid detection method.
Additional comments: It is a very important survey experiment. The authors should be noticed with published new data about recent CMVs invasion events and be very careful with their data interpretation about the conclusion of no presence of any geminivirus in Brazil.


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: ASSESSING THE DIVERSITY OF WHITEFLIES INFESTING CASSAVA IN BRAZIL
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authros reported a country-wide whitefly diversity study in cassava in Brazil. A large number of whitefly specimens were collected from diversed areas and characterised by mitochondrial cytochrome oxidase subunit I sequening. The study updates the status of whitefly diversity in Brazil and hence it is important. The manuscript is well written, methodology is adequate, results are well presented. I suggest acceptance of the manuscript with minor revision.
Experimental design: From the methodology section, it seems that the PCR from individual whitefly DNA was carried out and sequenced. The utility of fRFLP analsysis of the amplified PCR products is not clear as the current method of whitefly genotyping is sequence-specific. Please clarify this section.
Lines 206-209- difficult to follow. Were the additional individuals for each stage analyzed in RFLP or sequenced?
The authors have not detected the presence of begomovirus in the cassava plants. If there are some other begomovirus infected plants nearby, have the author checked the presence of begomoviruses in the vector? I believe by doing so, the authors can compare if the vectors are incapable of transmitting the virus or the plants are resistant to the nearby begomoviruses.
The authors used universal DNA primers for begomovirus detection and no begomovirus was detected. I suggest to undertake a rolling cycle amplification and digestion as a confirmatory step.
Validity of the findings: I suggest the following revisions:
As there is no detetction of begomoviruses and I did not find any evidence in the current study that shows the begomovirus dynamics, the title may be revised and restricted to the whitefly diversity in cassava.
The interpretation of RFLP data is not adequate.
The authors stated the specimens were collected from 66 spots of different agroecological zones of Brazil. I suggest to provide a figure that shows the locations on the map.
Diversity of the whitefly in each spots will also provide important data on their distribution.
The altitude, temperature and time of collection would provide important information on their ecological and host adaptation. This should be included in the revised version.
Additional comments: B. tabaci MEAM1 has been recorded by the authors. Whether it can transmit the begomoviruses infecting other crops at the same ecological niches? or the cassava cultivars are resistant to begomoviruses: will be an interesting study.  B. tabaci MEAM1 is a superior vector of many begomovirus species. But this is not universal. The efficiency of other predominat B tabaci species can also be checked for a comprehensive understanding.


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: ASSESSING THE DIVERSITY OF WHITEFLIES INFESTING CASSAVA IN BRAZIL
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors mentioned cassava virus disease such as CMD was severe in Africa. However, they did not listed the key competent vector, i.e., the cryptic species of Bemisia tabaci complex that transmit the begomoviruses in Africa. Is the BtMEAM1 the competent vector for CMD or other indigenous whitefly the competent vector in Africa? This information should be provided for readers as it is helpful to infer the potential begomovirus occurrence in South America.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Based on the phenomenon that begomoviruses were not occurred in cassava in South America, this manuscript investigates whitefly diversity, composition and prevalence in Brazil. The hypothesis proposed by authors is that begomoviruses epidemic have not occurred in cassava due to lack of competent vectors. This is an interesting topic with valuable information for vector and disease interaction and cassava production.


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: ASSESSING THE DIVERSITY OF WHITEFLIES INFESTING CASSAVA IN BRAZIL
Review round: 2
Reviewer: 1

Output:
Basic reporting: Adequate
Experimental design: Adequate
Validity of the findings: Adequate
Additional comments: The authors have not detected any begomovirus during the study. The occurrence or dynamics of begomoviruses have not been reported here. I suggest revising the title to "Assessing diversity of whitefly infesting cassava in Brazil"


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: TIME SERIES DATA ANALYSIS AND ARIMA MODELING TO FORECAST THE SHORT-TERM TRAJECTORY OF THE ACCELERATION OF FATALITIES IN BRAZIL CAUSED BY THE CORONA VIRUS (COVID-19)
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is well written. It borrows the concept of velocity and acceleration to forecast the coronavirus by using time series and multivariate linear regression. The mathematical explanation is clear and the results are complete. The language is  One suggestion on the literature review is to add comparison with other covid forecast models. What makes this study unique when there exist other coronavirus projection models?
Experimental design: The methodology is clear especially in the explanation of velocity and acceleration related functions. The author could add more details, in both the paper and the attached code, on how the training set and test set are selected when applying cross-validation.
Validity of the findings: The covid cases and deaths are changing all the time, and it worth comparing and validating the forecast results with the current situation (from Sep 16, when the data was acquired, to the most recent dates). It will also be interesting to see how this model could be applied to other countries or even different Brazilian states.
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: TIME SERIES DATA ANALYSIS AND ARIMA MODELING TO FORECAST THE SHORT-TERM TRAJECTORY OF THE ACCELERATION OF FATALITIES IN BRAZIL CAUSED BY THE CORONA VIRUS (COVID-19)
Review round: 1
Reviewer: 2

Output:
Basic reporting: the topic is good with the  global recent interest.
using time series data is accepted at this level since the world still have not much information about covid -19. Furthermore, the article within the journal scope
However, the work has too many non necessary figures. and need more explanation and justification about the used model

Thus it is  recommended to do major corrections the attached notes with the manuscript before accepting the article
Experimental design: NA
Validity of the findings: needs to validate the results
Additional comments: please respond the the  comments attached with the original article


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: TIME SERIES DATA ANALYSIS AND ARIMA MODELING TO FORECAST THE SHORT-TERM TRAJECTORY OF THE ACCELERATION OF FATALITIES IN BRAZIL CAUSED BY THE CORONA VIRUS (COVID-19)
Review round: 1
Reviewer: 3

Output:
Basic reporting: Structure and overall presentation of the article can be improved a bit. A more comprehensive discussion regarding motivation and novelty of the study can improve its readability. Please explain a bit more how your contribution is different from the contribution of (Chen and Yu, 2020) .
Experimental design: The study is relevant to journal, however the novelty of the contribution seems not much high. I would like to see whether the proposed methodology will work efficiently using some other datasets (COVID cases from some other countries).
Validity of the findings: The results have been validated using the codes and data provided by the authors and they satisfactory. However, I am afraid that forecasts for next six months can be obtained with reasonable efficiency. in addition, the contents in the Figure 13 to Figure 16 are not clear. For example, there is no clarity about X.axis and Y-axis.
Additional comments: The manuscript is publishable after satisfactory response to the above 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: TIME SERIES DATA ANALYSIS AND ARIMA MODELING TO FORECAST THE SHORT-TERM TRAJECTORY OF THE ACCELERATION OF FATALITIES IN BRAZIL CAUSED BY THE CORONA VIRUS (COVID-19)
Review round: 1
Reviewer: 4

Output:
Basic reporting: Here are the comments:
•	The language is sometimes difficult to read. The manuscript requires a complete rephrasing of sentences and correction of grammatical errors.  The writing center on campus can be a useful resource.
•	Equations 3 and 4 have a typo. The upper limit in the first integral and first summation should be (t+1). It is recommended to define F’(x) and H’(x) in equations 3 and 4 in a standard form instead of repeating the same formula. Similarly, the second derivative definitions in equations 5 and 6 can be written in a generalized form. Eqns 7 and 8 can be formatted in a single line.
•	There are too many figures and tables.  Figures 3 and 7-11 have x-axis and y-axis labels that are difficult to read.
•	Few references of ARIMA, MA can be replaced by well-known books like Time Series Analysis: Forecasting and Control by Box and Jenkins.
Experimental design: •	In the Methods section, standard procedures of time series analysis like exploratory analysis, decomposition, ACF, and PACF can be summarized more coherently and comprehensively. Adding a schematic diagram of the research process may be helpful.
•	Data under the Results section can be relocated to the Methods section.
•	Repetitive statements/conclusions can be avoided, e.g., The last line of the “Discussion” and “Conclusion” sections are the same.
•	In the Results section, reporting error rates like Mean Absolute Error or root mean square error can be essential for choosing the best forecasting model and its accuracy accompanied by the already conducted exploratory analysis.
Validity of the findings: •	Limitations of the study, future research directions, and comparison of results with background literature are suggested.
Additional comments: Overall, the manuscript is organized and represented in a well-structured manner. The results and figures were easily reproducible with the code and data provided.


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: TIME SERIES DATA ANALYSIS AND ARIMA MODELING TO FORECAST THE SHORT-TERM TRAJECTORY OF THE ACCELERATION OF FATALITIES IN BRAZIL CAUSED BY THE CORONA VIRUS (COVID-19)
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised manuscript provides more details in the background and literature review. It is good to see that this version updates the methods to support the conclusion.

I am confused by three versions of manuscripts in this revised package. The resubmitted articles in the Word document (peerj-53390-Tracked_Changes_PeerJ-research-manuscript.docx) and the PDF document (peerj-reviewing-53390-v1.pdf) are not exactly the same. The literature review sections are slightly different among these documents: the author’s letter (peerj-53390-Rebuttal_Letter.pdf), the Word document (peerj-53390-Tracked_Changes_PeerJ-research-manuscript.docx), and the PDF document (peerj-reviewing-53390-v1.pdf).

The following comments and line numbers are based on this document: peerj-reviewing-53390-v1.pdf.
Experimental design: 1. About the cleaned function (Line 391). Is it a function removing possible outliers? If so, how you define the outliers? Visually clean out the outliers?
2. When comparing the weekly and monthly moving averages to the cleaned functions, the manuscript mentions that the moving averages are over-smoothing? How do you mathematically define over-smoothing?
Validity of the findings: 1. About forecast. Instead of providing forecasts of the multivariate function and the composite function, could you provide forecasts of the real cases and deaths in Brazil and Indonesia? As the limitations section mentions, the current y-axis has little explanation for the forecast.
2. Instead of replicating the model in Indonesia, why not replicate the model in each Brazil state and see if the aggregation of the state-level forecast matches the country-level forecast? If we need to apply the same model for countries other than Brazil and Indonesia, why not apply it to more countries? I would see it is just a change of the input for each country. Without an explanation of randomly selecting Indonesia, I would doubt the external validity of this model.
Additional comments: 1. Examples of format/grammar issues:
1) Capitalize “b” in “best” in this subtitle: Further Testing, Selecting the best Model, Forecasting and Analyzing (Line 449). Similar issue found in the Figure 7 caption.
2) Need a better sentence structure: The models are the Auto ARIMA Model without seasonality, a custom made ARIMA model that compensates for the serious lags found in the auto ARIMA model without seasonality, where necessary, named the adjusted lag model and the Auto ARIMA model with seasonality. (Lines 430-432)
3) Using the same indication for figures. For instance, when referring to a figure, the article sometimes uses Fig 2, while using Figure 2 in other places. (Lines 490-493)

2. Better graphs:
1) Use x-axis to label the exact dates in Figure 7 and 8 so the reader will know the real forecast time window. What do you mean by saying “dominant frequency” in the limitations section?
2) Correct the image distortion. Unify the labels, such as “a” and “(a).” Add axis labels in Figure 5, 7 and 8.


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: TIME SERIES DATA ANALYSIS AND ARIMA MODELING TO FORECAST THE SHORT-TERM TRAJECTORY OF THE ACCELERATION OF FATALITIES IN BRAZIL CAUSED BY THE CORONA VIRUS (COVID-19)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript has been improved and publishable now
Experimental design: The manuscript has been revised to my satisfaction
Validity of the findings: The manuscript has been revised to my satisfaction
Additional comments: I recommend the manuscript for publication


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

Input:
Title: TIME SERIES DATA ANALYSIS AND ARIMA MODELING TO FORECAST THE SHORT-TERM TRAJECTORY OF THE ACCELERATION OF FATALITIES IN BRAZIL CAUSED BY THE CORONA VIRUS (COVID-19)
Review round: 2
Reviewer: 3

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: The authors have addressed all the 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: TIME SERIES DATA ANALYSIS AND ARIMA MODELING TO FORECAST THE SHORT-TERM TRAJECTORY OF THE ACCELERATION OF FATALITIES IN BRAZIL CAUSED BY THE CORONA VIRUS (COVID-19)
Review round: 3
Reviewer: 1

Output:
Basic reporting: The basic reporting looks good. The author need to add the number in Line 50: On 30th June 2020, Brazil recorded - - the 2nd highest number of 50 confirmed cases of the coronavirus in the world.
Experimental design: Experimental design looks good.
Validity of the findings: Validity looks good and clear after the revision.
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: COMPARING AUDIO- AND VIDEO-DELIVERED INSTRUCTIONS IN DISPATCHER-ASSISTED CARDIOPULMONARY RESUSCITATION WITH DRONE-DELIVERED AUTOMATIC EXTERNAL DEFIBRILLATOR: A MIXED METHODS SIMULATION STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: - "Accordingly, to increase the rate of CPR during cardiac arrest, it is performed by the dispatcher.": Sentence is ambiguous. How can the dispatcher do CPR? Pls rephrase
- "pre-hospital cardiac arrest should be "out-of-hospital cardiac arrest"
- "post-mortem experiment" pls rephrase to something less misleading
- Literature review. Suggest the authors incorporate important relevant references including:
1. Lin Y-Y, Chiang W-C, Hsieh M-J, Sun J-T, Chang Y-C, Ma MH-M. Quality of audio-assisted versus video-assisted dispatcher-instructed bystander cardiopulmonary resuscitation: A systematic review and meta-analysis. Resuscitation. 2018 Feb;123:77–85.
2. Ho, A. F. W. et al. Barriers to dispatcher-assisted cardiopulmonary resuscitation in Singapore. Resuscitation 105, 149–155 (2016).
3. Ho, A. F. W. et al. Evaluation of culture-specific popular music as a mental metronome for cardiopulmonary resuscitation: a randomised crossover trial. Proceedings of Singapore Healthcare 28, 159–166 (2019).
4. Dong X, Zhang L, Myklebust H, Birkenes TS, Zheng Z-J. Effect of a real-time feedback smartphone application (TCPRLink) on the quality of telephone-assisted CPR performed by trained laypeople in China: a manikin-based randomised controlled study. BMJ Open. 2020 Oct 1;10(10):e038813.
- there is no discussion on the strengths and limitations of the study
Experimental design: - How were participants assigned to audio-only and mixed video-audio?
Validity of the findings: - Line 197 "homogeneity was ensured". There are actually substantial differences between the 2 groups, eg % male 58.3% vs 33.3%. Your p values were all >0.05 only because of small sample size. Also you compared 4 characteristics, when there are many more characteristics that influence performance of CPR. I don't think you should so assertively say that homogeneity was ensured.
- What were the baseline CPR training of the participants? How about separately in the 2 arms. Prior training is probably one of the most important determinent of DACPR quality
- Line 413 "This study confirmed the difference". I don't think your study design allows such a strong conclusion. Suggest soften this assertion
- Generalizability of findings severely limited because there is no current system that uses AED-drones.
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: COMPARING AUDIO- AND VIDEO-DELIVERED INSTRUCTIONS IN DISPATCHER-ASSISTED CARDIOPULMONARY RESUSCITATION WITH DRONE-DELIVERED AUTOMATIC EXTERNAL DEFIBRILLATOR: A MIXED METHODS SIMULATION STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The aim of this study was compare first responders’ cardiopulmonary resuscitation (CPR) performance when a dispatcher provides audio instructions only and when both audio and video instructions are given.

The manuscript is written in a clear English, unambiguous, technically correct text. It is conform to professional standards of courtesy and expression. The manuscript include sufficient introduction and background to demonstrate how this article fits into this field of knowledge. The authors referenced relevant literature.

The article conform to an acceptable structure and format. The figures and tables of the article are relevant to the content of the manuscript.
Experimental design: The authors clearly define the aim anda research question. The  manuscript authors identified the knowledge gap and statements were made as to how the study contributes to filling this gap.
The research have been conducted rigorously and to a high technical standard. The investigation have been conducted in conformity with the prevailing ethical standards in the field.
Methods have been described with sufficient information to be reproducible by another investigator
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: COMPARING AUDIO- AND VIDEO-DELIVERED INSTRUCTIONS IN DISPATCHER-ASSISTED CARDIOPULMONARY RESUSCITATION WITH DRONE-DELIVERED AUTOMATIC EXTERNAL DEFIBRILLATOR: A MIXED METHODS SIMULATION STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall hard work and good intentions and design.  1) not clear on methods of how Audio-visual coaching was accomplished (simple hand held cell phone by rescuer with both methods, or special/extra setup for drone/AV coaching 2) terminology of "Stop time" is atypical (usually named chest compression fraction 3) The authors report simple comparisons between groups, but neither group achieved good quality of CPR (slow CC rates, poor # of ventilations)...there were statistical improvements without clinical significance. 4) the qualitative findings were interesting 5) unclear the content or training of the dispatchers and coaches (e.g. good audio coaching beats bad audio/visual coaching and visa versa)
Experimental design: MIxed methods:
Improvement to be made by comparing the two groups for COMPLIANCE to current guidelines (not simple comparison on one vs other)...comparison of 47 CC/min vs 63 CC/min is stat sigif different, but dismal in both groups....same for 3.5 vs 5 ventilation/min.
Both had good CCF (83% vs 90%), but stat signif different.
Validity of the findings: see above: caution for statistical differences vs clinically important differences and the lack of analysis of differences without a distinction. Going for terrible to bad cpr compression rates and ventilation rates may be statistically different but not important to patient outcome.

Good start on qualitative findings. intreresting results.
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: COMPARING AUDIO- AND VIDEO-DELIVERED INSTRUCTIONS IN DISPATCHER-ASSISTED CARDIOPULMONARY RESUSCITATION WITH DRONE-DELIVERED AUTOMATIC EXTERNAL DEFIBRILLATOR: A MIXED METHODS SIMULATION STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: My previous comments have been satisfactorily addressed.
Experimental design: My previous comments have been satisfactorily addressed.
Validity of the findings: My previous comments have been satisfactorily addressed.
Additional comments: My previous comments have been satisfactorily addressed.


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: COMPARING AUDIO- AND VIDEO-DELIVERED INSTRUCTIONS IN DISPATCHER-ASSISTED CARDIOPULMONARY RESUSCITATION WITH DRONE-DELIVERED AUTOMATIC EXTERNAL DEFIBRILLATOR: A MIXED METHODS SIMULATION STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: I do not feel the need to re-review
Experimental design: .
Validity of the findings: .
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: ADDITIVE AND MULTIPLICATIVE PROBABILISTIC MODELS OF INFANT LOOKING TIMES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Seems OK
Experimental design: Seems OK; design was approved.
Validity of the findings: OK, likely to have little impact on the field.
Additional comments: I've made comments in the attached review which is to be shared with the author.


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: ADDITIVE AND MULTIPLICATIVE PROBABILISTIC MODELS OF INFANT LOOKING TIMES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: See attached.
Validity of the findings: No comment.
Additional comments: See attached.


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: ADDITIVE AND MULTIPLICATIVE PROBABILISTIC MODELS OF INFANT LOOKING TIMES
Review round: 2
Reviewer: 1

Output:
Basic reporting: See attachment
Experimental design: See attachment
Validity of the findings: See attachment
Additional comments: See attachment


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: ADDITIVE AND MULTIPLICATIVE PROBABILISTIC MODELS OF INFANT LOOKING TIMES
Review round: 3
Reviewer: 1

Output:
Basic reporting: The ms addresses the issue of how to best model quantitatively infant habituation using probabilistic approaches. The topic is important since infant habituation is a critical tool to study the development of perception, attention, and other cognitive abilities in infants. The main result is that partial-pooling models provided more accurate predictions.
Experimental design: The authors compared various additive and multiplicative regression models of habituation to fit looking times of a habituation experiment with infants in three age cohorts (4, 7 and 10 months). They used visual stimuli consisting of rectangles with different luminance, color and orientation. Overall, 359 experiments were performed.
The authors tested 5 probability distributions: truncated normal, truncated normal with exponential mean, lognormal, Weibull, and gamma distribution.
Validity of the findings: Results showed that partial-pooling models provided more accurate predictions than the no-pooling models, reducing the bias due to over-fitting inherent in no-pooling models. The multiplicative trend models and the gamma trend model in particular provided better data fit, better predictive fit, and lower parameter correlation.
In the Discussion the authors address the potential role of confound stimuli associated with the presentation of test stimuli.
Additional comments: Overall, the ms has been carefully revised relative to previous reviewers’ comments. As a minor comment, I noticed that (unless I missed it!) the number of infants included in each of the 3 cohort groups is not specified, only the number of trials included for each condition in each cohort group is given in Table 1.


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

Input:
Title: EFFICACY OF COMPUTATIONAL PREDICTIONS OF THE FUNCTIONAL EFFECT OF IDIOSYNCRATIC PHARMACOGENETIC VARIANTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript aims to assess the ability of current functional prediction algorithms to predict the severity of pharmacogenetic variants that are thought to be associated with off-target adverse drug reactions of drugs.

On the whole the language of the manuscript is good, in clear English with the topic well introduced.

However, I feel the title a touch imprecise. A generic variant can’t have off-target effects only a defined function/impact on protein and/or genetic traits. In a sense, each genetic variant is doing exactly what it is supposed to do. However, variants can be associated with increased/decreased off target adverse effects of drugs. I would suggest to revise the title to reflect this and be more precise.

Additionally variants are referred to as off-target variants throughout the manuscript, this probably needs tightening up, maybe define it at the beginning: “variants associated with off target effects (referred to as off-target variants)”.
Experimental design: The hypothesis is that many functional variation prediction algorithms rely on sequence conservation to predict variants that have a functional impact on a protein with the sequence conservation maintained by some purifying selection. However, because drugs have only been used over a short period of time, no purifying selection has acted on the drug target with regard to response to the drug and as such, the algorithms perform badly with respect to predicting non-benign function consequences of variants in drug targets. Moreover, the same hypothesis can be applied to off-targets of drugs, i.e. there has been no selection against increased off target effects of drugs and as such functional prediction algorithms are not accurate as their core training is not generalisable to this context.

The hypothesis has been clearly defined in the manuscript, however, I feel there are some things to address with it, particularly with the lack of selection at drug targets. Obviously it is true that drugs have only been used over a short period of time and not enough time for selection to act. However, it is unclear if evolution would act upon an individual’s drug response or adverse drug response, for this to happen, it would have to impair their ability to reproduce which would essentially mean killing them before reproductive age. Given that the majority of the drug consumption is in the middle age/elderly (with the exception of recreational drugs) this is probably not the case.

Moreover, this question touches upon “what makes a good drug target?” and amongst the many attributes, is the ability to elicit a large response to a relatively small drug dose. There is some evidence of an association between reduced residual evidence intolerance score (RVIS) (a metric of the tolerance of a gene to mutational perturbation) and targets of approved drugs (10.1038/ng.3314  page 857), however, it is unknown if this extends to off-targets. However, given this association, it is unlikely that drug targets are just random and that there may be some selection operating on them as small variations within them have the ability to manifest in relatively large changes in the phenotype of an organism.

To guide the reader, when defining the hypothesis, it might be worth tackling what some of these algorithms are actually attempting to predict  (i.e. the definition of deleterious) and perhaps give an example where deleterious amino acid changes have given rise to adverse off target effects. This will give the reader some context as to why one might expect a functional prediction algorithm to have some predictive ability for off-target adverse effects.

The classification scheme (lines 121-134) for off-target variants was good although, I am I am not 100% sure why preference was given to variants where “or when a protein or cellular system related to the intended drug effect was involved” (line 133). Surely off target effects can effect different systems? It was good to see the ADME genes removed though. Whilst the rationale is obvious for the removal non-coding and synonymous variants that will not be covered by the prediction algorithms – it would be nice to acknowledge (either in the introduction or discussion) that functional variation is just one avenue for genetic variation associating with adverse effects. One can envisage that  increased or decreased expression of a target or off-target gene/protein in a non-therapeutic tissue could also cause (off-target) off-tissue adverse effects.

Functional Effect Prediction (lines  136-141), a nice range of prediction algorithms were evaluated, I am not 100% familiar with them all but I am sure some must have tuning parameters? It would be essential in an evaluation manuscript such as this to give more detail of the parameters used, perhaps in a supplementary note.
Validity of the findings: Overall the results are quite straightforward, many of the tools performed similarly. However, the authors only present the results from 6 of the 11 tools and it is unclear why the remainder are not discussed – although they do appear in the supplementary table 2, this should be referenced from the main text and probably should be a csv (if allowed) as the computational tractability of word docs is limited). I also, noted that some of the predictions in supplementary table 2 gave a lot of missing data, this probably needs commenting or assessed in some way.

Something, I am unclear on, is the classifications of the off targets are limited to categories 1A, 1B, 2A, 2B but the predictions are across 4 categories, I am not sure how to interpret this and perhaps some explanation is needed to  guide the reader through, are you predicting across all categories even when they have no possibility of being classed as “off-target”? It maybe that I have miss-interpreted something here.

The section of the results discussing category 3 variants needs to be appraised in the context of how many type B variants are in the database overall as the reader can not gauge if category 3 variants are enriched for type B variants. The methods probably need adjusting to include category three in the off target predictions (see paragraph above).

I feel some consideration of causality of the variants should be given also. In the discussion for example the phrase “variants causing off-target effects” is used. I would suggest that this is changed to  associated with off target effects, as in many cases the causal nature will be ambiguous. If we consider the results in the general context of causality, is the probability of being causal associated with category? Is this is why the prediction tools predict better for the most robust category 1 variants? Where as category 3 variants have a lower prior probability of being causal for an off target effect but are marking (in linkage disequilibrium) with a causal variant? In that way they may be predictive of an off-target effect whilst not demonstrating any predicted functional impact.

Overall, I think the results suffer from never really knowing the denominator for any of the analysis and I would recommend some sort of formal enrichment/association analysis. Also, no reference is ever made to the distributions of the random predictions.

Additionally, many of the tools predict on the quantitative scale but are interpreted on a categorical scale (benign, deleterious etc...). It would be useful to guide the reader where these cut offs exist on the scale. Additionally some context on what is the predictive accuracy under the best possible conditions will also help evaluation of the results
Additional comments: Overall, I think the topic of this publication is relevant and under explored. The role of genetic variation in adverse effects is not well understood. Additionally, many people use off-the shelf predictive tools with out considering what the tool is really predicting. In that sense I think this  manuscript highlights these important issues, however, in it’s current form I do not think it fully addresses them and I feel that if the authors can address the points in this review this manuscript could add to the knowledge in this area.


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: EFFICACY OF COMPUTATIONAL PREDICTIONS OF THE FUNCTIONAL EFFECT OF IDIOSYNCRATIC PHARMACOGENETIC VARIANTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Minor comment  - line 38: ‘predicative’ is used incorrectly and could be deleted or replaced with ‘predictive’.

In addition comments in experimental design section overlap with considerations here.
Experimental design: 1) The introduction should include greater discussion of the diverse evidence bases used, for example in the CADD tool.

2) Considering the sentence at the end of the introduction “Hence, the strength of purifying selection to remove non-functional or poorly functional variants from the population is the strongest evidence presently used to classify a variant as either benign or deleterious.” This is not well substantiated and should be supported by empirical results, removed or appropriately rephrased. It is not rigorous to claim that selection is the strongest evidence for variant classification simply because this information is commonly used by the available algorithms.

3) The methods section requires more detailed information about the datasets used in this study, so that a clear description for each dataset is given in a way that is accessible to the reader. This should include (a) more detail to specify exactly how the randomly selected set of 2155 SNVs were obtained and (b) the number of off-target SNPs that were curated, these should be included for each row of table 1.

4) The Figure and associated discussion does not give any indication of the meaning of the scores or threshold values that may be applicable in the six tools evaluated. For example the data for CADD shows a range of scores from 0 to 40, it is difficult to interpret the Figure without showing a threshold. Please refer to https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4980758/

Also relating to the consideration of thresholds, in the text the authors set a conservative threshold value (20) for CADD and then identify that a majority of the high-confidence variants fall below this threshold. Results for a lower threshold value should also be quoted, a value of 10 would seem appropriate in this context (CADD suggest values between 10 and 20; a value of 10 has been shown to perform best in the above article Fig S1A).

5) In order to enable effective comparison of the tools evaluated ROC curves should be presented with an AUC value and where threshold values can be determined standard metrics should be quoted including Matthew’s Correlation Coefficient, TPR and FPR.

6) The authors should describe in detail the 6 variants classified as benign by PolyPhen2 that were found in PharmGKB category 1.

7) The discussion of score distributions (e.g for PolyPhen2) around different variant categories should take into account the distribution of nsSNVs, rSNVs and ncSNVs in these categories – which may explain the variation observed.

8) One limitation of this study is restricting to missense SNPs, because a portion of pharmacogenetic variation is non-coding. It would be valuable to include some consideration of noncoding variants in this work.
Validity of the findings: 9) A central assumption implicit in this study is that algorithms which predict SNV effects on protein function should also identify pharmacogenetic variation. This does not always hold - for example, a SNV could disrupt a protein-drug interaction without impairing the protein’s function in the cell. While algorithms that predict SNV effects on protein function typically examine the relationship of predicted deleterious SNVs to disease/drug responses, it does not hold that all ‘pharmacogenetic’ SNVs are deleterious to protein function. Discussion around the implications of this assumption and it’s relevance to the work presented should be included in the manuscript.

10) The claim that "variants causing off-target effects are unlikely to have been subject to purifying selection" (in contrast to on-target effects) requires substantiation or should be removed from the manuscript. It may be argued that the large majority of deleterious mutations have not been subject to purifying selection (because they would have been eliminated from the population). There is a subtle difference to the author's statement in the above sentence, compared to the idea that evolutionary constraint at sites that contribute to variation in off-target effects should differ to that for on-target effects -- which is perhaps the message that is intended. However the manuscript does not provide evidence for the difference in evolutionary constraint discussed above. There are also a number of confounding factors involved that the authors have not accounted for or even discussed, such as the multiple biases towards specific biological pathways in drug development efforts.

11) The statement “our investigation showed little difference between tools which use structural features and those which do not” is not well supported. In it’s current form, the study has not compared the other tools in sufficient detail in order to draw this conclusion. Nor is the specific statement well formed because ‘little difference’ is too vague. Specific metrics should be employed to enable a quantitative (and qualitative) evaluation of the differing tools; and the similarities and differences considered. Some standard approaches for this are identified in point (5) above.
Additional comments: While the work embarks upon an interesting area of study, there are significant flaws in it’s current form - including issues with the reasoning and insufficient evidence to support the claims made.


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: EFFICACY OF COMPUTATIONAL PREDICTIONS OF THE FUNCTIONAL EFFECT OF IDIOSYNCRATIC PHARMACOGENETIC VARIANTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: It is my opinion that the revised manuscript is greatly improved and that the authors have done a good job at implementing the comments from my review. I am of the opinion that it meeting the publication criteria for PeerJ.


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

Input:
Title: EFFICACY OF COMPUTATIONAL PREDICTIONS OF THE FUNCTIONAL EFFECT OF IDIOSYNCRATIC PHARMACOGENETIC VARIANTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: a) The manuscript needs careful attention to and modification of the language used to ensure scientific rigour and clarity. For example:
- In the abstract "these idiosyncratic pharmacogenetic variants very likely violate the assumptions of predictive software commonly used to infer their effect" seems overstated/imprecise. This should be reformulated accordingly, for example to quantify or tone down (e.g. "... may violate the assumptions ...").
- In the introduction lines 54-55: "Numerous other factors play a role in variable drug response, including age, ethnicity, gender and differences in alcohol intake." this sentence uses 'other' to contrast with genetic factors. However the above factors include a genetic component; the text should be reformulated to avoid this confusion.
- The wording "These are data tools that" on line 72 does not read well and should be reformulated.
- Methods lines 170-171: 'These variants were used as a truth set to measure the performance of the classification scheme.' would be better phrased along these lines: 'These 30 variants were taken as gold-standard data for benchmarking our approach to determine variants associated with off-target effects.'
- Introduction lines 84-5; " The types of evidence employed by the algorithms are numerous with CADD considered 60 annotation sets based largely based on conservation" requires rewording for clarity (key issues underlined).
- The authors have used a structured abstract but omitted to include a final "Discussion" or "Conclusions" section - this section should be provided.
- The full stop is misplaced in the text "(pharmacogenes). (Sim et al. 2011)".
-  Line 258 "...our classification scheme (Supplementary Table S3)." Should include reference to Table 1 for clarity.

b) Introduction, lines 75-76: The authors cite their own work to support the notion that predicted deleterious variants had little impact on protein function. This statement over-interprets the results (in PNAS 2015;112:E5189-E5198), which examined phenotypes in vivo and included a case study on TP53 transcription. Therefore this work assessed function at the level of changing the attractor state of protein networks which have evolved for robustness to perturbations in individual components and so is not equivalent to examining function at the single protein level. Indeed, prediction tools define 'deleterious' in relation to disrupting the properties of an individual protein (e.g. binding, catalysis). Accordingly the claim of >40% false positive rate is not supported by the work that they have cited. The introduction should be reworked to account for this.

c) Introduction lines 87-92. The following sentences present oversimplifications which should be corrected "Despite the diversity of evidence types however, in almost all cases if a variant or mutation lies in a highly conserved region in a multi-species alignment of orthologous gene sequences, the variant will very likely be considered deleterious or damaging. Conversely, should the variant be broadly similar to existing sequence variation in this same alignment, the variant will be considered benign or functionally homologous."

d) The point "Hence, sequence conservation is the strongest evidence presently used to classify a variant as either benign or deleterious." is not adequately substantiated by the preceding text. The authors could make reference to feature weightings (in the algorithms considered) for substantiation. Alternatively, the point could be toned down to say that sequence conservation is an important and widely used feature in identification of deleterious variants.

e) Organisation of the manuscript needs attention. For example:
- The methods section refers to results (especially Figure 1, Supplemental Table S1 and Table 2) which clearly should be not presented in Methods (but should be given in the Results section).
- In the Results section, lines 199-200 the sentence: "Instances where a tool produced no value for a given SNV were recorded as an NA value" should be placed in methods.

f) Lines 255 to 269 are difficult to follow and require revising for clarity/rigour. For example " Of the starting set of 30 variants, the filtering scheme retained eight putative Type B variants. Of these eight, five were true positive Type B variants (with no false negatives) and three were false positives."
Experimental design: h) Methods, lines 185-190.  "All high-confident PharmGKB Category 1 variants were input as the positive set while a set of randomly selected common variants (MAF > 0.1) were input as the negative set using the Perl function rand() across the entire set of dbSNP missense variants. Labels were inverted for SIFT due to lower scores representing likely damaging mutations and CADD and Mutation Assessor scores were scaled into the range of 0-1. Area under the curve and Matthew Correlation Coefficient were calculated using the R-package ROCR performance function".

This text is not sufficiently detailed to enable reproduction of the work. A definition of "high-confident" should be given, and the score threshold value used to determine MCC requires explanation (how is the threshold determined, or is the maximum MCC value quoted?). In addition there are issues with language (e.g. "Matthew" should be "Matthews").

h) I cannot understand how the scheme in Table 1 includes a literature review (ie manual) step, but the results differ to the manual literature review step taken for a further 30 variants. How do the authors explain this?
Validity of the findings: i)  Results lines 217 to 227; the authors quote median values for the PolyPhen2 scores in different categories of variants (four categories). It would be helpful to include statistical evaluation of these differences. One possibility could be to use the Mann-Whitney test, comparing each of the categories 2-4 against category 1.

j) The ROC curves are only calculated for Category 1 variants -- and several of the tools perform extremely well (e.g. with AUC values of 0.97, 0.94 or MCC values of 0.99, 0.97). These results appear to contradict the point by the authors that the algorithms do not perform well on the type B 'idiosyncratic' variants - however this aspect is not resolved or acknowledged in the manuscript text. An analysis should be undertaken to specifically investigate the difference in prediction performance on the Type A vs Type B variants (or the 'Type B enriched') set for each of the six main algorithms evaluated and the text adjusted accordingly.

k) Lines 235-236 "While there are significant differences," requires substantiation with p-values and specific comparisons.

l) The evaluation of the putative Type B variants (lines 267 to 269) given for PolyPhred2 should be performed across all six primary algorithms evaluated and must include statistical comparisons (for example using the Mann-Whitney test, with appropriate FDR correction for the six comparisons to be made).
Additional comments: m) In general, the authors have substantially improved the manuscript, including some refocusing and addition of new results which have partially addressed the comments made. However significant issues remain. There is still insufficient data supporting the key point about performance on 'idiosyncratic' (type B) variants. Indeed, at face value, some of the new data presented shows that the methods perform extremely well.

n) The authors have not addressed the point raised in the earlier set of comments about discussing the variants that are misclassified by PolyPhen. These variants should be used as case studies to exemplify the points made in the manuscript - in particular to address the question of the extent to which they disrupt the core protein architecture/function. It is straightforward to assess this using public databases (including information in dbSNP and UniProt). For example, rs116855232 is a Arg139Cys mutation in the Nudix hydrolase domain of NUDT15 that affects metabolism of Thiopurines by causing loss of diphosphatase activity (see https://europepmc.org/article/MED/26878724). This investigation took me just 10 minutes to perform and identifies rs116855232 as a false negative. It does not seem onerous for the authors to carry out similar investigations of the other variants and to discuss them in a paragraph in the manuscript in order to inform the point about misprediction vs functional differences.


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: EFFICACY OF COMPUTATIONAL PREDICTIONS OF THE FUNCTIONAL EFFECT OF IDIOSYNCRATIC PHARMACOGENETIC VARIANTS
Review round: 3
Reviewer: 1

Output:
Basic reporting: please see below
Experimental design: please see below
Validity of the findings: please see below
Additional comments: The manuscript has been considerably improved. However, a number of important issues remain, noted below.

1.  Authorship is inconsistent (equal contribution/corresponding authors information) between first and second appearance of title and abstract in ‘Manuscript to be reviewed’ PDF file.

2. Title should be revised for clarity, for example the word ‘of ‘ appears three times

3. Structured abstract, Results section says that functional inference tools perform poorly on the complete set of PharmGKB variants. This conflicts with the data reported in table 1, with MCC values that are extremely good (although flawed, please see below).

4. I have serious concerns about the validity of results presented, especially for the type B variants. For example Polyphen AUC is reported at 0.40, with MCC=1; SIFT has reported AUC=0.41 with MCC=0.99. The reported AUC values (and shapes of the curves) are incompatible with the values given for MCC. Therefore, I attempted to replicate the values for Polyphen using supplementary table S4 and supplementary table S2. I took all of the 'random' variants from supplementary Table S2 as the negative class, and all of the type B variants in supplementary table S4 as the positive class. I found a similar, although not identical, AUC value (0.43 vs the reported value of 0.40). The maximum MCC value was 0.027, in stark contrast to the reported maximum MCC value of 1. I have deduced that this discrepancy is a result of an error in the computer code used to calculate the MCC value with the ROCR package (from inspection of the code given in Supplementary data S3). Specifically, the x.values are being quoted rather than the y.values from the ROCR ‘performance’ object that holds the MCC results. Furthermore, the authors appear to be using an unbalanced gold standard dataset, which will skew the AUC calculation towards the larger class (the negative class). This issue portends further concerns about the reproducibility and validity of the study as a whole.

5. There are issues with the data provided. For example the final line of supplementary table S4 does not have data for the first three columns, although prediction scores are provided.


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

Input:
Title: GENOME-WIDE IDENTIFICATION OF CANDIDATE AQUAPORINS INVOLVED IN WATER ACCUMULATION OF POMEGRANATE OUTER SEED COAT
Review round: 1
Reviewer: 1

Output:
Basic reporting: English is acceptable, the literature review is not sufficient, raw data (of RNA-seq) is not shared.
Experimental design: Experimental design has flaws. See my comments below for details.
Validity of the findings: Not satisfactory. See my comments below for details.
Additional comments: The authors have identified aquaporin encoding genes in pomegranate using in silico tools and characterized the protein as well as genomic properties. Also, the transcript levels of the identified genes were studied in two different cultivars. With the data, the manuscript was constructed with organized tables and figures. However, I have several concerns over the data presented:

1.	The work attempts to derive a correlation between water accumulation and expression profiles of AQP genes, but no further experiments were performed to establish this claim. Correlating water content data with the expression data of genes is not sufficiently justified with experimental proofs.

2.	Line 121: While saying ‘primary gene structure,’ authors have put protein length, molecular weight, and isoelectric points within the brackets!

3.	Subcellular localization was predicted using WoLF PSORT, but the data is not validated in wet-lab. Given the availability of several tools, one can do infinite ‘computational analyses’; however, validation of such data is important to derive confidence. I am also concerned about using a single tool for predicting the subcellular localization.

4.	 Lines 127-129 – The MSA data should be presented and studied for possible sequence variations (and their impact on the structure).

5.	‘TBtools’ has been mentioned at several places (seems, 80 % of the analyses were performed using this tool), but nowhere is the information on how it was performed, the parameters maintained, etc. are missing!

6.	Section 2.3: I have concerned with studying the motifs (using MEME). Why shouldn’t the authors study the domain architecture than looking for motifs? This data should be correlated with the phylogenetic tree.

7.	Gene duplication analysis is not new, and it has already been discussed in the genome sequencing paper at whole genome-level. When such comprehensive data is already available, studying the duplication of a small gene family is not scientifically significant.

8.	The basis for choosing two cultivars is unclear. Also, DAPs should be justified.

9.	Transcript profiling is not performed using qRT-PCR (as being done in routine genome-wide papers), but the authors have used RNA-seq. However, the information about RNA-sequencing is incomplete. How many replicate libraries are sequenced? Statistical significance of the data? How was expression measured? Data availability?

10.	The raw data underlying heatmap presented to show the expression should be given in supplementary information.

11.	How correct it is to correlate the RNA-seq data with microarray data of Qin et al. (2017)? Did Qin et al. paper perform the experiments in the same cultivar used in this study?

12.	The ‘Results’ section lacks insights as the sub-headings summarize the data presented in tables, figures, and supplementary information.


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

Input:
Title: GENOME-WIDE IDENTIFICATION OF CANDIDATE AQUAPORINS INVOLVED IN WATER ACCUMULATION OF POMEGRANATE OUTER SEED COAT
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall language is clear. I have noted some typing error or sentences which could be improved for clarity below:
•	Page 8, line 69, “selectivity” spelt incorrectly.
•	Page 8, lines 79-83, Sentence structure could be improved to be clearer.
•	Page 8, line 85, “pollen pollination” could be changed to “flower pollination” or “pollen tube development”- unsure what you are actually referring to.
•	Page 15, line 212 and 215, “plasma” spelt incorrectly.
•	Page 18, line 276, “ar/R” spelt incorrectly.
•	Page 28, lines 489, sentence error ‘phyletic evolutionary’, unsure of meaning.
•	Page 28, line 492, typing error, ‘evolution’ spelt incorrectly.
•	Page 28, line 495, ‘Furthermore’ spelt incorrectly.

Sufficient literature references and background/context provided.
•	Additional references could be added to Line 73, page 8, after ‘specificity of solute transport and transport rate’.
•	On Page 24, lines 401-403, the sentence is quite vague. Would be good to add a reference also.

Professional Article structure and figures displayed, all appropriate data has been made available (including raw data).
Experimental design: This research is original and seems to apply to Aims and Scopes of this journal, a research Article for Biological Science.
Although the authors mention in the introduction that aquaporins have important physiological roles within plants, there could be more specific emphasis on how this research article is could be a valuable resource for other researchers not only researching pomegranate seed coat development, but also concerned with advancing other aspects of plant performance e.g. tolerance to abiotic stresses, water and nutrient-use efficiency.

The research question is well defined. Aquaporins are vital for numerous plant physiological functions and furthering our understanding of their biology is dependant firstly on establishing the AQP gene family within a species of interest.

The investigation seems rigorous and of a good technical standard.

Methods is overall well-described. However, I have a few comments:
•	The authors describe that Arabidopsis AQP sequences were used as BLAST queries to identify AQP isoforms in the pomegranate genome. It would have also been good to use AQP sequences from a species more closely related to pomegranate, such as Eucalyptus. It would allow for a more thorough search, especially as Arabidopsis does not have XIP isoforms, and pomegranate does.

•	The description for methodology used for naming the pomegranate AQP isoforms is misleading. The authors state that the PIP, NIP, SIP, TIP and XIP isoforms were classified according to the nomenclature used for Arabidopsis (even though Arabidopsis does not contain XIPs). There is no further description as to how the genes we actually named considering that the phylogeny shows that the Arabidopsis AQPs do not cluster with PgrAQPs in the majority of cases (in particular for the PIPs), and as such the naming would have been assigned based on other criteria not included in the methods. The description of gene naming is often overlooked in AQP family classifications which can have implications future research interpretations i.e. mis-assigning orthologs across different species.
Validity of the findings: •	In your results section, page 14-15, lines 209-210, you state that the predicted trans membrane domains (TMDs) varied from 4-7 TMDs. There is no further information as to whether the AQP isoforms containing less than 6 TMD (comprising on ~17% of the genes identified) would actually be functional genes, or whether they might be eroding/non-functional genes. AQPs have a highly conserved structure across all kingdoms of life, having 6 TMDs, so a shorter sequence or altered structure would greatly impact function and tetramer formation.
•	On page 17, line 256, you mention that your finding of PgrNIPs and PgrPIPs being the most and least conserved subfamilies at amino acids level, respectively, was NOT consistent with findings in Nicotiana tabacum. This interpretation is incorrect, as your findings are actually in agreement with finding from Nicotiana tabacum.

The data on which the conclusions are based were provided.
Conclusions are well stated, linked to original research question & limited to supporting results.
Additional comments: No Additional comments.


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

Input:
Title: GENOME-WIDE IDENTIFICATION OF CANDIDATE AQUAPORINS INVOLVED IN WATER ACCUMULATION OF POMEGRANATE OUTER SEED COAT
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No comment


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

Input:
Title: GENOME-WIDE IDENTIFICATION OF CANDIDATE AQUAPORINS INVOLVED IN WATER ACCUMULATION OF POMEGRANATE OUTER SEED COAT
Review round: 2
Reviewer: 2

Output:
Basic reporting: - Grammatical/sentence error on Page 8, line 77-80. I commented on this in the previous report. I would amend to “The AQP gene family has been widely studied in numerous plant species, such as…”.
-	Page 8, line 85, Species name should be provided before introducing as “PvPIPs”.
-	Page 9, line 90, Species name should be provided before introducing as “PsNIPs”.

Previous comments requesting additional references have been addressed.
-	Page 26, line 450, reference missing at the end of sentence: “Variation in the number of TMDs to different plant species has been reported (reference)”
Experimental design: Clarifications have been provided in regards to the identification of the XIP isoforms in pomegranate, using Populus trichocarpa XIPs.

The authors have addressed my concern relating to the naming methodology of the pomegranate AQP isoforms. In the methods, however, you still state that the “Pomegranate AQPs were named according to the standardized MIP nomenclature” which is not very informative, as there isn’t really such a thing.
Instead, the methods description would be improved by mentioning that the PgrAQps were named based on homology to Populus trichocarpa AQP isoforms, and state why you chose this species to guide your naming.
I have a question as to why you did not include the Populus trichocarpa AQP sequences in your Figure 1 Phylogeny, if they were actually the basis of your naming.
Validity of the findings: Additional information was added in the discussion in regards to the impaired functionality of truncated AQP isoforms in other species (e.g. truncated TaPIP2;1 had no water function activity). Functional AQP proteins generally have 6 TMDs, therefore a clearer indication could be added by the authors as to whether the PgrAQPs which have less than 6 TMDs are even functional (these could be noted in a column in Table 1 for example). This would be important for researchers looking to do further study on your identified proteins, as one might not want to do further study on a truncated/non-functional protein.

The sentence on page18, line 283-287: “Multiple sequence alignments showed that PgrNIPs and PgrPIPs were the most diverse (38.5%) and conserved (72.7%) subfamily at the amino acid level, respectively (Table. S3). This finding is consistent with the AQPs from Nicotiana tabacum, suggesting that PgrNIP and PgrPIP subfamily genes may have a similar role in water transport in pomegranate” is not clear. It implies that the authors are inferring water permeability based on based on within family homology/diversity of PIP and NIP sequences (although NIPs are generally poor water transporters)? More explanation/reasoning could to be included if you were to make this statement.
Additional comments: The line numbers in the ‘Rebuttal’ document do not match up with the amended document. This made following up the revisions difficult. I would strongly encourage the authors to ensure that in future manuscripts the line numbering can be clearly followed.