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: PATTERNS IN ARTISANAL CORAL REEF FISHERIES REVEALED THROUGH LOCAL MONITORING EFFORTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors did a great job in reporting on the disparate data of creel surveys. The MS is clearly written although could benefit from an additional read-through to streamline the text as some is duplicated. Sufficient background is included to provide context and understand the usefulness of non-commercial data to sustainably manage near-shore fisheries.

It appears that the reported data is not the raw creel survey data but the estimated data by each of the literature sources. The results could benefit from adding SEs especially the CPUE data to improve the spatial comparisons. Of course this would mean that the raw data is accessible from the 18 literature resources used in this review.
Experimental design: The title indicates guidelines of ‘best practices’ but the MS seems more a compilation of the creel survey data from the various literature sources and misses in-depth analyses. ‘Best practices’ seem to be, reduced effort on those gear types that are most effective overall (highest CPUE) while low in total gear-hours. However, as the introduction and discussion mention, knowing the human use (e.g. a recreational fisherman fishing with hook and line for fun versus a fisherman putting out his laynet to catch a living) is of course more important than establishing the general overall gear-hours per gear type. Furthermore, gear types do not always target the same species e,g, catching parrotfish with spearfishing versus catching octopus with the same gear type has very different ecological consequences. The MS would benefit from an evaluation of the species caught and how a reduction on those species might benefit the ecosystem.

It is a great and laudable effort to compile all these data in one place. However, these data could benefit from standardization to make use of them more efficient. For example, In reporting effort, gill nets and surround nets were not included while total catch does include the catches of these methods (e.g. for Kane’ohe 58% of the total catch was from surround/gill nets and in Hanalei these gear types comprised 69% of the total catch). The MS would further benefit from separating out the invertebrates (e.g. the catches in Kane’ohe were largely comprised of invertebrates (octopus) caught by spear fishing – hence high spear fishing effort for that location), akelu/opelu (e.g. Hanalei catches comprised of 69% akule/opelu) and coral reef fish. This would benefit managers trying to regulate the fishery based on gear types/ species / species complexes as regulations for octopus could be very different from e.g. opelu. Moreover, it would facilitate comparing just reef fish (or invertebrates or opelu/akule) spatial patterns which I would argue is more interesting to reef managers and the fishing community then the overall total catch or effort where this information is lost.

The data set comprises a temporal time span from 1980 – 2015 with most data sets from the latest 10 year. The Puako data showed that there can be very large temporal changes in the fishery over a 30 year time span as the authors mention as well in the discussion. The authors acknowledge that over a time span of 20 or 10 years similar changes could have occurred at other reefs. Maybe results can be binned by survey year to see if temporal patterns emerge which might be more important than the spatial patterns? Even if no additional analyses are done, it would be better to include the year of the survey in the results for clarity.
Validity of the findings: In general, some of the conclusions are not well backed up by arguments/findings. For example, the statement that "The findings can directly improve the design of more cost-effective and standardized creel survey approaches that can be instituted to facilitate more informed fisheries management in Hawai‘i and beyond" is not well argumented. It would be very interesting if the authors include the "How". Knowing that fishing effort, catch and CPUE estimates varies across space could be partly due to the differences in target species, the inclusion of gill net & surround net in some places, or the temporal differences in survey years, it is unclear to me how these findings can improve a more cost-effective creel survey.
As I think the authors are aware of, there is a movement to make reporting of recreational/non-commercial fisheries obligatory (through license fees) which of course would also give us information on the non-commercial catches and efforts once implemented. The MS would improve from including these efforts and maybe comparing the pros and cons of both. Additionally, NMFS-PIFSC has recently published a technical memorandum with stock assessments of 27 reef fish species. These could help inform the setting of ACLs. It is unclear and not elaborated on why the authors think that ACLs are 'most effective' for high valued invertebrates.

Lastly, I am surprised that the authors find the results from the fish flow (i.e. that most of the catch is not sold) 'surprising' as this has been reported in pretty much all literature on non-commercial fishing.
Additional comments: Some more specific comments:
Ln 42 “Surprisingly’? In almost all articles related to non-commercial fishing it is reported that a great majority of the catch is not sold e.g. Friedlander and Parrish 1997, Friedlander et al 2012. Suggest to re-word.
Ln 81-83: This sentence is of course true but some head-way has been made with the stock assessment of 27 reef fishes and is worth mentioning. (Nadon et al 2017 NMFS-PIFSC Tech Memo #60)
Ln 96-97. This sentence seems to imply that all creel surveys are designed by community members which is not the case for most creel surveys mentioned in the tables. Suggest to delete last part of the sentence (everything after the second comma)
Ln 117-119: is it not the lack of obligatory reporting of non-commercial fishing that hinders the data collection more so than that this fishery is non-commercial? In other words, the fisherman do not have to report their catches, (unlike the commercial fisherman) so don’t do it unless they participate in the MRIP data collection by DAR, and therefore data is limited.
Ln 197 and ln 198 seem to say the same?
Ln 197, 198. From table 3 it seems that line fishing is 79% (not 94%), spear 14% (not 0%) and net 7%? Please clarify discrepancy.
Ln 208 Table 4. Without having checked all refs, it seems that for Kaneohe, the CPUE is reported for shore and boat based line fishing whereas the methods say that boat-based is not included. Not sure about others but suggest to review your methods/results so they are in line with the original literature. I understand the info given in the creel survey papers might be not sufficient to separate them out but if that is the case this should be mentioned so we know the table does not compare like with like.
Ln 227. Figure 3. These catches include gill net and surround net for some locations (e.g. Kaneohe Bay and Hanalei) which makes them not comparable with other locations that do not include the catches of those gear types. Suggest to adjust catches to make them comparable.
Ln 259 “Surprisingly” see comment earlier
Ln 282-283. Some of this variation is because of inclusion/exclusion of gear types, targeted species (e.g. opelu v octopus) and would be more interesting if the authors can specify their results separately for reef fish, invertebrates, and akule/opelu.
Ln 283-285. Can the authors expand on how the findings can improve cost-effect survey design?
Ln 287. Can the authors explain how the define “health”.
Ln 302. Isn’t a spatial measure also an input control as it restricts effort?
Ln 307. What is meant by “inputs” (other than fishing technology and effective gear types)?
Ln 308. What is meant by “outputs”, catches?
Ln 343. Why are ACLs ‘most effective’ for a high value invertebrates? Pls expand.
Ln 383-385. Suggest to include Jokiel et al 2011 Journal of Marine Biology where the authors compare traditional with western management.
Ln 399. There is a movement to make reporting of recreational/non-commercial fisheries obligatory which of course would also give us information on the non-commercial catches and efforts once implemented. Might be worth mentioning.


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: PATTERNS IN ARTISANAL CORAL REEF FISHERIES REVEALED THROUGH LOCAL MONITORING EFFORTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: L1-2: The title seems to imply some kind of comparison between different monitoring/monitoring approaches. The paper focused mostly on characterizing fishery and perhaps this should be reflected in title instead?

L34: This “collaborative” dimension isn't very clear from methods/results. How does the approach mentioned in the study promotes/facilitates collaboration? For example, aren’t fishers simply asked questions (and if so, is that a collaborative process?)?

L41: The word “rampant” seems to imply some kind of magnitude or direction has been assessed. Perhaps reword?

L42: Why “surprisingly”? Is this different from most similar fisheries? Clarify or reword.

L53: Perhaps you mean “services” instead of “values” here?

L95: How is this participatory? Clarify as it currently seems information is simply requested of them.

L124-125: I think this should be clarified in abstract as well as mentioning how this study differs from previous studies (e.g. by putting everything together, study is able to draw comparisons, identify regional patterns, etc).

L126: What do you mean by “intercept” survey? Clarify.

L147: Can't read full label in first column.

L152: how do creel surveys differ from the interview-based surveys mentioned below then? Unclear.

L162: Redundant? Interviews can only be undertaken with participants… rephrase.

L168: What's this reference meant to support here? Also, if in review, perhaps it's not available to readers anyway?

L259: See my comment above regarding term “surprisingly”.
Experimental design: L129-137: What's rationale for inclusion of each different area? How were these selected? Are there any key differences among them that might be useful for interpreting results?

L180: what about potential temporal effects? Does it make sense putting everything together? Some consideration or discussion required.

L217 and others: I think these differences among study areas need to be stated much earlier on manuscript.
Validity of the findings: L253: How was this information obtained? Clarify in methods. Also, examples don’t provide specific time periods or magnitude of problem so difficult to use them to assess situation (although every useful for illustrating potential threats). Examples should be more specific (for example, “33% of the fishing activity recorded was illegal” refers to how many fishers? When?)
Additional comments: The manuscript “Patterns in artisanal coral reef fisheries reveal best practices for monitoring and management” by Delaney et al. provides useful insights about small-scale fisheries in Hawai‘i with clear implications for natural resource management. However, several key issues should be addressed before further consideration for publication.

Firstly, the contribution of the study should be made clearer. To do so, I think the authors should: (1) explicitly mention their general approach in terms of data gathering from previously published/unpublished studies much earlier on the manuscript (e.g. in the abstract) and explain how this study differs/builds upon those (see specific comment); and (2) clarify how this study aims to contribute in terms of data collection/monitoring protocols. For example, are creel surveys widespread in fisheries studies or only occasionally used (and if so, are the authors suggesting this should be elsewhere?). Either way, this should be clearer so that readers understand how this study fits within wider literature and fisheries assessments and how it contributes to advancing any knowledge gaps.

Secondly, in the introduction, more focus should be given to the types of challenges and barriers involved in small scale fisheries monitoring and managing in data-poor contexts as well as different approaches used to address this issue. I think that would be useful for putting this study into wider context. I also felt the introduction was a bit repetitive (e.g. the livelihoods/social/economic/etc. issue was mentioned several times throughout introduction) and occasionally jumped between general and specific issues with somehow unclear flow. I recommend restructuring and rewriting some sections so that it reads better in terms of narrative and is more focused around key management/monitoring challenges.

Finally, while I commend the authors for the work involved in bringing all the survey information together, I think the potential caveats in doing so haven’t been properly mentioned and discussed. For example, it’s clear from reading appendix material that a lot of different assumptions and steps were involved in producing estimates from different data sources. I thank the authors for providing a detailed description in the appendix. Nevertheless, some discussion of potential biases due to different survey approaches, sampling period (e.g. the authors pooled together data from different decades), etc., is required.


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: PATTERNS IN ARTISANAL CORAL REEF FISHERIES REVEALED THROUGH LOCAL MONITORING EFFORTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Well written some minor comments:

Ln 329 Define “health” (health of reef fisheries and ‘health of associated ecological community” – maybe replace by “productivity of reef fisheries” and “status of associated ecological community” although I am not sure why this sentence is added as the rest of this section focused on fishing and nothing is mentioned about “numerous ways to assess the health”. Suggest to delete or add a sentence that includes refs for the latter part of this sentence.
Ln 331-336 This paragraph comes a bit out of the blue – the results show that the catches are hardly sold (fig 5) and there is no mention about the composition of commercial and non-commercial catches so the reader has no idea how much of the reef fish is actually sold. Maybe the authors could start this paragraph with a comparison of commercial and noncommercial fisheries? And back up these claims by references.
Ln 378, 379 The refs used to back up this sentence seem not appropriate. Donovan et al 2016 has references therein that are appropriate and I would recommend to use them. DAR 2017 has regulations but no justifications (or at least not that I could find on the linked website).
Ln 398 a scale or scales; against impacts of climate change
Editorial comments
Ln 86 “remains” should be “remain”
Ln 225 add “they” compose
Table 5, Pupukae “illegally fish”
Ln 468 at at least
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have done an excellent job in addressing my previous concerns and I look forward to seeing this MS being published.


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

Input:
Title: THE PHT4;1-3 MUTANT LINE CONTAINS A LOSS OF FUNCTION ALLELE IN THE FATTY ACID DESATURASE 7 GENE CAUSED BY A REMNANT INACTIVATED SELECTION MARKER—A CAUTIONARY TALE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors use of English is clear and professional, and there are some few minor recommended corrections that will further improve the clarity of the manuscript.

However, I think that the introduction is insufficient and more background needs to be provided to establish which is the gap in research that the authors aim to fill. The question being answered needs to be stated clearly in order to set up an appropriate context for the reader.
Experimental design: Please clearly state the question being addressed with your experiments.
Validity of the findings: No comment.
Additional comments: The authors address a problem often overlooked in reverse genetics. However, in my opinion the manuscript needs to state the question more specifically, as I found the introduction a little vague in that regard. Perhaps the authors would be better able to guide their readers by discussing the problem with establishing phenotypes of loss-of-function mutants, the need for researchers to ensure no other mutations in the background that might be causing them, and that having two or more alleles is preferable to define a
Aside from this, I recommend some minor corrections for clarity before resubmitting.
1.	The major issue is that the introduction needs to be more specific about the aim of the study. One paragraph of introduction does not seem sufficient to lay out the background and the gap in research that this study means to fill.
2.	Correct nomenclature of the genes and mutant alleles should be used consistently and clearly throughout the manuscript. For example, in line 36, PHT4 refers to the entire gene family (the correct gene name is PHT4;1). So it would be simpler to refer to “the transposon in pht4;1-3”
3.	Line 34, change “were” to “was”.
4.	Line 50, since the pht4;1-1 mutant allele was not mentioned elsewhere in the manuscript, I assume this is a typo and the authors meant to write “pht4;1-2 and pht4;1-3”. Please clarify.
5.	Line 79, add a comma after fad7 and “was” after “conducted”.
6.	Line 83, change to “F2 plants were”, instead of “F2 plants was”.


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

Input:
Title: THE PHT4;1-3 MUTANT LINE CONTAINS A LOSS OF FUNCTION ALLELE IN THE FATTY ACID DESATURASE 7 GENE CAUSED BY A REMNANT INACTIVATED SELECTION MARKER—A CAUTIONARY TALE
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this paper, the authors discribed a cautionary tale that the mutant line pht4;1-3 carried a remnant insertion in the FAD7 gene. And a series of biochemical and genetic evidences were supplied. The English laguage are professional and clear to understand. However, from this study, the authors concluded that every mutant should be confirmed by at least two independent lines. This is a well-known conclusion. Is it necessary to confirm again? Also, there are some major concerns as follows:
1. Introduction:
1) The introduction is too simple. Only PHT4;1 was discribed. More details about the phenotypes of pht4;1 mutants, FADs, as well as lipids and fatty acids should be introduced. Also, some mutagenesis methods should also be mentioned.

2. Materials and methods:
1) The mutant genotyping and the lipid analysis should be divided into two parts with two separate subtitles.
2) How did the authors get these mutant lines? From ABRC stock or given by the others? The stock numbers for these mutants?
3) How the Arabdopsis DNA was extracted? How did PCR and electrophoresis run?
4) Line 38: the tables should be listed in order. Table 1 is first, then folloed with Table 2, Table 3…
5) How many biological and technical repeats were carried? How many samples were included in each repeat?

3. Results and discussion:
1) Lines 50-51: the data about the lipid compositions are not shown?
2) Lines 53-55: in Fig 1, both DGDG and MGDG showed the quite different fatty acid compositions, why only MGDG was mentioned?
3) For all of the mutant lines mentioned in this paper, the authors should carry out the experiments such as Real-time PCR to detect the expression levels of PHT4 and FAD7.
4) The transposon was inserted into two separate positions (PHT4;1 and FAD7). This means more than one Ds copies in the mutant genome, maybe some other experiments such as southern blotting would be needed to detect the transposon insertion copies.

5. Tables and figures:
1) For the data in Fig1 and Table1, the significance analysis is required.
2) In Fig2, the insertion site in FAD7 should be marked in the gene model.

6. Supplemental data:
1) What did the capital letters and the lowercases mean in the FAD7 sequence? The blue letters are the coding sequence of FAD7 or not? If yes, the authors should indicate the triple coden, and the amino acid sequence should also be listed.


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

Input:
Title: THE PHT4;1-3 MUTANT LINE CONTAINS A LOSS OF FUNCTION ALLELE IN THE FATTY ACID DESATURASE 7 GENE CAUSED BY A REMNANT INACTIVATED SELECTION MARKER—A CAUTIONARY TALE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have satisfactorily expanded the introduction and added sufficient background as to aid in better understanding of the reasoning behind the experiments. I recommend only some minor changes to the manuscript for clarity:

1.	Line 22: Reverse genetics
2.	Line 52: phosphoglycerolipids
3.	Line 77: change “were” to “was”
4.	Line 100: “leading us to suspect” (delete “e” and “d”)
5.	Line 105: revealed
6.	Line 107: same as #5


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: UNANTICIPATED DISCOVERY OF TWO RARE GASTROPOD MOLLUSCS FROM RECENTLY LOCATED HYDROTHERMALLY INFLUENCED AREAS IN THE OKINAWA TROUGH
Review round: 1
Reviewer: 1

Output:
Basic reporting: See attached report.
Experimental design: See attached report.
Validity of the findings: See attached report.
Additional comments: See attached 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: UNANTICIPATED DISCOVERY OF TWO RARE GASTROPOD MOLLUSCS FROM RECENTLY LOCATED HYDROTHERMALLY INFLUENCED AREAS IN THE OKINAWA TROUGH
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript language is good both in overall structure and specific use. Literature citation is mostly adequate although limited (suggestions below). Figures are fine.
 Fasta sequences were provided but I don’t see them in DDBJ.
Experimental design: It’s an observational study. Methods are adequate.
Validity of the findings: It is fine to draw attention to these records at chemosynthetic systems.  However, as neither two species themselves nor the presence of the family at vents is new, I would suggest the authors make a larger contribution by:
i)	Drawing a better picture of the likely role these animals play in this ecosystem (grazer?  predator?)
ii)	Comment on the intersection of vent and non-vent species.  There is a fairly robust literature that details the peripheral vent environment – this record is an important contribution so set it in that context.  The most recent review, I believe, is Levin et al. 2016. 2016. Hydrothermal vents and methane seeps:  Rethinking the sphere of influence.  Frontiers in Marine Science, 3, dx.doi.org/10.3389/fmars.2016.00072 There are quite a few instances of deep-water gastropods on the periphery of vents and seeps – why are they successful in this niche? (I see Buccinum viridum frequently among tubeworms in the northern Juan de Fuca Ridge).
Additional comments: Do you think they are competing with species that use the resources in a similar fashion? Or are these available niches?  Why are they not found at the other vents in the region?
Suggest that the last sentence of the Introduction is part of the habitat characterization and should move to the Discussion to explain the presence of these taxa. …. and when I get to end of Discussion, I do not understand this “maybe a seep” comment.  The best indication of whether it is a cross-over habitat is your list of species – how do they compare with Watanabe et al’s list of vent fauna in the region?  Are there seep fauna here, too? Are there any supporting temperature data to decide if there is a thermal anomaly here?

Other points
L 62:  “drastically”?  Are you talking about end-member fluids?  pH in waters around animals is often no different from seawater. But you can justify if the Okinawa region is notably different in diffuse fluids.
l 69: Lutz and Kennish do not really test this idea – but this paper does: Van Dover CL, Trask JL.  2000. Diversity at deep-sea hydrothermal vent and intertidal mussel beds. Marine Ecology Progress Series 195:169-178.
l  90: in English, “Neither” takes singular subject and verb.
l. 104: remove ‘by the junior author.’   Are there any temperature or chemical measurements made?
Good imagery of  T. ikukoae.  Is the size within the range originally reported for the species?
Figure 1:  Add N and E to lat/long; attach two or three island names to orient the reader.  Also, I think it useful to indicate the other vent sites from Watanabe and Kojima 2015.


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: EFFECTS OF SHINBUTO AND NINJINTO ON PROSTAGLANDIN E2 PRODUCTION IN LIPOPOLYSACCHARIDE-TREATED HUMAN GINGIVAL FIBROBLASTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: The methods are appropriate and the experiments are well performed.
Validity of the findings: no comment
Additional comments: In this manuscript, the author described the effect of shinbuto and ninjinto on prostaglandin E2 production and potential mechanism. The manuscript has potential interest to the field. The methods are appropriate and the experiments are well performed. Understanding more about the effect of kampo drugs is an essential step for medication usage. The manuscript have potential interest in the field. The methods are appropriate and the experiments are well performed. The manuscript is also acceptable to me except a few questions.

1.	Line 182-185. I think “Shokyo and kankyo” here should be “shinbuto and ninjinto”.
2.	Figure2 legend title is wrong. cPLA, annexin1 and cox-2 is not mentioned in this figure.
3.	For the westernblot data, it is better if the statistical data is provided. Especially for fig.7. I think shoky and kankyo have effect for cPLA expression.


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: EFFECTS OF SHINBUTO AND NINJINTO ON PROSTAGLANDIN E2 PRODUCTION IN LIPOPOLYSACCHARIDE-TREATED HUMAN GINGIVAL FIBROBLASTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors investigate the anti-inflammatory effect of two kampo medicines (shinbuto and ninjinto) on human gingival fibroblasts (HGF) derived from patients affected by periodontal disease with deficiency pattern.
They show these two compounds able to decrease PGE2 production while increasing IL-6 and not affecting IL-8 levels. They exclude the modulatory effect on PGE2 effect as a consequence of COX-2 inhibition, impact on ERK activation or modulation of expression of factors cPLA2, ammexin1, and COX-2. Finally, they tested the effect on PGE2 of single herbal components composing the two formulations and identified shokyo and kankyo as inhibitors of PGE2 production without affecting the above mention factors.
The authors conclude about a potential impact of the two campo medicines on PLA2 activity.

The ms is clear; however, english proofreading would be recommended due to the presence of several mistakes.
Relevant literature is adequately provided.
Figures are clear.
Experimental design: The experimental procedures are clear as reported in Materials and Methods with ethical approval indicated regarding the use of specimens from patients .

The aims of the present investigation are clearly indicated in abstract as well as in the introduction section.
Validity of the findings: In its present form the ms, raises some questions to solve.

The two kampo medicines decrease PGE2 levels while increasing IL-6 and not affecting IL-8 production. The authors show the ability of single components shokyo and kankyo to similarly affect PGE2 levels while not affecting the expression of PLA-related factors.

1)
It would be interesting to verify if shokyo and kankyo are able to produce the same pattern of modulation of interleukin-6/8 as shinbuto and ninjinto. This phenomena might correspond to a kind of combinational effect of different components contained in shinbuto and ninjinto.

2)
The authors hypothesize the impact of shinbuto and ninjinto on cPLA2 activity. It would be interesting to provide this additional experiment to make robust their hypothesis.
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: EFFECTS OF SHINBUTO AND NINJINTO ON PROSTAGLANDIN E2 PRODUCTION IN LIPOPOLYSACCHARIDE-TREATED HUMAN GINGIVAL FIBROBLASTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors considered all remarks and addressed the points raised.
Experimental design: The experimental procedures are clear as reported in Materials and Methods with ethical approval indicated regarding the use of specimens from patients.
Original files for consent and ethics have been provided (in their original language).
Validity of the findings: The ms has been implemented with additional experiments as suggested or strategies anyway have been considered and tempted.
Additional comments: The ms has been implemented in its experimental part.
Language has been revised.


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

Input:
Title: PLANTCV V2: IMAGE ANALYSIS SOFTWARE FOR HIGH-THROUGHPUT PLANT PHENOTYPING
Review round: 1
Reviewer: 1

Output:
Basic reporting: Nothing to add
Experimental design: The paper includes details of the listing of the available methods through PlantCV.  This is fitting as the paper is about this new software.

The main impact of the paper would be enabling the potential users to leverage this software.  In that regard, adding a few "how to" could be helpful.  For example, what is the general guideline of which method to use for segmenting?  And how to tune many parameters?  How to create a series of steps to work for some common tasks? How to fix any errors from the algorithm?  What is the expected speed of each method?
Validity of the findings: Nothing to add
Additional comments: The paper is a good introduction to the PlantCV software.  Overall the paper and proposed method seem to address much need of the field.  The future steps are insightful and should further increase impact.  Main comments are to maximize the utilization of the tool by answering typical struggle that non-technical users would face.


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: PLANTCV V2: IMAGE ANALYSIS SOFTWARE FOR HIGH-THROUGHPUT PLANT PHENOTYPING
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language used is clear throughout and the relevant phenotyping literature is well cited. One of the sections I am direct to comment on here is whether the results are relevant to the hypothesis proposed, however this is a methods/resource paper and does not include hypothesis driven research.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Lines 52-54: The point about floral structures being different colors in different plants (and the need for fixable analysis approaches as a result) is a good one, but the specific example used opens up a big can of worms.  The floral organs (ie flowers) of Camelina are yellow and the inflorescence/glumes of brachypodium are green. The floral organs of brachypodium (such as anthers) would also be yellow and since anthesis is often used as the milestone for "flowering" in grasses, it would often be the case that folks would be looking for yellow in photos of grass inflorescences. What about yellow Camelina flowers vs white arabidopsis flowers?

Line 85-86: I am afraid it wasn't clear what picture "The image of Arabidopsis thaliana" was in context here as there are several Arabidopsis images in different figures. Maybe include "used in Figure X or analysis Y" here. and for the wheat image listed a little later in this section.

In the discussion of unit tests it is not clear if the development and maintence of unit tests is an expectation of contributors who write new modules for incorporation into Plant CV or of the core management team.

155-158: I would encourage the authors to include a copy of the SQLite database schema as it exists with the writing of this paper as a figure or supplementary figure. I assume the schema on github will continue to be updates at PlantCV matures, which may make the reference to github less relevant to the version of the software described in this manuscript. This could potentially replace the current Figure 1.

Page 16: Could the authors add one to two sentences on the circumstances where a researcher might want to trade a reduction in image detail for a reduction in image noise?

Page 19: "The ‘watershed_segmentation’ function can be used to estimate the number of leaves for certain plant architecture types and imaging platforms (Fig. 3)" It might be useful to add a little more detail on the characteristics of plant architectures where the watershed method is likely to work or likely to fail at this point.

Pages 23-24: If the Bayesian method provides approximately the same output as a theshold-based analysis, but the Bayesian method requires fewer total steps that is a clear advantage to the Bayesian method. However, it wasn't clear what the other advantage(s) were to the Bayesian method since the sentence describing that point starts with "An additional advantage to using the naive Bayes..." (Lines 421-423).


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: PLANTCV V2: IMAGE ANALYSIS SOFTWARE FOR HIGH-THROUGHPUT PLANT PHENOTYPING
Review round: 1
Reviewer: 3

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


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

Input:
Title: EXAMINING PUBLICATION BIAS—A SIMULATION-BASED EVALUATION OF STATISTICAL TESTS ON PUBLICATION BIAS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Please see report.
Experimental design: Please see report.
Validity of the findings: Please see report.
Additional comments: General Comments:

This paper uses Monte Carlo simulations to test four different methods to identify publication bias: (i) Egger’s Test/Funnel Asymmetry Test (FAT), (ii) the p-uniform test (PU), (iii) the test for excess significance (TES), and (iv) the caliper test (CT – where 4 different versions of the CT are compared).  The Monte Carlo experiments vary over a number of dimensions: (i) existence and type of publication bias (“p-hacking”; “file drawer”), (ii) number of observations in primary studies (N); (iii) number of studies included in simulated meta-analyses (K); and (iv) population effect size (both fixed at different values, and heterogeneous). Tests were compared on two dimensions, Type I error rates and power.  As the author notes, there are a wide variety of results, making it difficult to come up with a single conclusion.  But given the interest in identifying “best practice,” the author concludes: “The FAT is recommended as a test for publication bias in standard meta-analyses with no or only small effect heterogeneity. If no clear direction of publication bias is suspected the TES is the first alternative to the FAT. The 5%-caliper tests is recommended under conditions of effect heterogeneity, which may be found if publication bias is examined in a discipline-wide setting when primary studies cover different research problems” (cf. “Discussion”).  Overall, the paper is clear and well-constructed.  It makes a valuable contribution to an important topic about which relatively little is known.  In this reviewer’s opinion, there is insufficient evidence to support the recommendations.  However, the paper begins to fill in a blank sheet and hopefully moves the discipline closer to a better understanding of this issue.  Specific comments follow.

Specific Comments:

1.	The paper attempts to construct realistic situations by which to support recommendations for meta-analysis researchers.  In the opinion of this reviewer, the paper is too narrow to do that.  Most of the emphasis in the paper is based on fixed effects models.  There is only one variation of a heterogeneous effect, the case identified as “Het.” As this latter case surely most matches realistic situations, there is an insufficient database of realistic situations on which to support recommendations.  This reviewer is not recommending that the author change her Monte Carlo experiments.  The fixed effect cases are of interest as a benchmark.  Instead, this reviewer recommends that the conclusion be rewritten to downplay recommendations and focus more on what we can learn from this narrow set of experiments.

2.	One important issue that is overlooked in this and related studies is the relationship between effect size and publication bias.  The author seems to think that the 50% and 100% publication bias regimes are holding constant the degree of publication selection bias.  They are not.  As effect sizes increase, the degree of publication selection bias changes.  This is evident in the power results in Tables 7-10. Again, this reviewer does not suggest that the author change her Monte Carlo experiments.  However, it would be useful if the “percent positive and significant studies” was reported as a separate column for each of the “N/K/Effect size” experiments.

3.	Relatively little analysis is done of the results.  This author needs to be more thoughtful about explaining why results differ across N/K/Effect Size (and “percent positive and significant studies”/incidence of publication selection bias).  In this reviewer’s opinion, the major contribution of this study relies on the insights that can be learned about how these parameters affect the Type I error rates and power results.

4.	Related to the previous point, more effort needs to be paid to how the publication selection process is likely to affect the results across different parameter settings.  For example, in the Reed (2015) and Alinaghi and Reed (2016) papers cited by the author, it is noted how effect size is related to the incidence of publication selection bias, and how this generates different kinds of estimation bias depending on the type of publication selection bias (bias against insignificance, bias against negative signs).  The author has chosen to model a publication selection process that simultaneously targets both the sign of the estimate and its statistical significance.  This is common across simulation studies (such as any of the many Stanley and Doucouliagos studies), so this reviewer has no problem with this approach.  However, it does complicate the relationship between the incidence of publication selection and the degree of estimation bias, and hence Type I error rates and power and thus it will be that much more challenging, and important, that the author explain this relationship.

5. 	The perils of implementing these tests with heterogeneous effects should be emphasized.  In that context, the following references should be discussed and cited:

-- Lau, J., Ioannidis J.P.A., Terrin, N., Schmid, C.H., and Olkin, I. (2006). The case of the misleading funnel plot. British Medical Journal 333: 597-600.

-- Sterne, J.A.C., Sutton, A.J., Ioannidis, J.P.A., Terrin, N., Jones, D.R., Lau, J., Carpenter, J., Rucker, G., Harbord, R.M., Schmid, C.H., Tetzlaff, J., Deeks, J., Peters, J., Macaskill, P., Schwarzer, G., Duval, S., Altman, D.G., Moher, D., and Higgins, J.P. (2011). Recommendations for examining and interpreting funnel plot asymmetry in meta-analyses of randomised controlled trials. British Medical Journal, 343: d4002.

-- Terrin, N., Schmid, C.H., Lau, J. and Olkin, I., (2003).  Adjusting for publication bias in the presence of heterogeneity. Statistics in Medicine, 22: 2113-2126.


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: EXAMINING PUBLICATION BIAS—A SIMULATION-BASED EVALUATION OF STATISTICAL TESTS ON PUBLICATION BIAS
Review round: 1
Reviewer: 2

Output:
Basic reporting: I was able to load raw data from the supplement using R's haven::read_dta(). There's no codebook so I'm not sure what all the columns represent, however.

I can also confirm that the enclosed .do files appear to contain code; however, I do not know STATA and cannot comment on the quality of the code.

Tables would benefit from more thorough captions. I often did not understand what the tables represented (particularly Table 5).
Experimental design: The author compares the performance of four tests or publication bias / p-hacking: Egger's test, TES, p-uniform, and the caliper test. I think that this is a worthwhile endeavor. Among these four tools, it would be useful to know which ones perform well under which conditions.

I was confused by the use of effect size Beta. I am familiar with Cohen's d, odds ratios, and Pearson's r. Isn't Beta equivalent to a Pearson r? It must not be because r cannot exceed zero. Please clarify what the effect metric is.

I was a little surprised by the sizes selected for N and K. Are these parameters intended to be representative of a particular research area? These Ns are larger than I would expect in my area of experimental psychology. Also, I think it is unusual for a substantive meta-analysis to have k = 100. Perhaps it is your intent to test an entire research literature for publication bias (e.g. 1000 studies from some journal) -- it is generally my opinion that these samples are too heterogeneous to be informative. Please justify the decision to use these Ns and Ks.

It is worth considering that the implemented form of p-hacking is only one form of p-hacking. P-hacking may come in many forms (selection among several dvs, selection among several treatment groups, optional stopping, outlier exclusion), all of which increase the Type I error rate to various degrees and may influence these tests in different ways. Thus, it is sensible to caution that the results may not generalize to all forms of p-hacking.
Validity of the findings: See general comments.
Additional comments: Unfortunately, I had a lot of trouble understanding the manuscript. Reorganization, use of subheadings, and pruning of unnecessary text would be very helpful.

1. Organization
The manuscript is very long and dense. It would be helpful to give it a fresh read and evaluate what is most important. Organization by subheadings, especially in the results section, would be very helpful.

Some technical details, such as how long the code took to run, are technically impressive but not of scientific importance. I'm also not sure that it's necessary to fully explicate the math behind each test when they are described in their respective publications.

Footnotes are also frequent and not all seem necessary. Some footnotes contain factual inaccuracies; for example, footnote 4 cites Nuijten et al. 2016 as an estimate of the prevalence of fraud, but this paper only checks the prevalence of p-values that don't match their test statistics (which can happen for benign reasons). I am also unsure about whether "publication bias is heavily punished" in any area except clinical trials.

2. Results
The results are confusing to me because they seem to describe many results in terms of unconditional probabilities, e.g. averaged across all conditions. This is confusing because many of these probabilities will depend heavily on the condition. For example, the frequency with which null results are censored will depend heavily on the true effect and the number of observations.

The regression model might help to address this concern, but I remained too confused about what data and conditions were in the model to learn anything from this section.

Additionally, I find the emphasis on dichotomous significance tests a little dissatisfying. A better question might be, how badly has the true effect been misestimated? You mention that "PU was only able to discover file-drawer behaviour under low underling true effects." (line 449). Perhaps at this N and this K, file-drawing does little to influence the results of a meta-analysis? Just how bad is the bias?

I don't understand Table 5.

3. Interpretation.
The Discussion and Conclusion seems very brief compared to the rest of the manuscript. I found this disappointing because there is a lot that is done in the Results section that was not clear to me. I was hoping that the Discussion would establish the meaning and importance of all these analyses and tables.

The author recommends the use of TES when publication bias selects for results of either sign. It is not clear to me that two-tailed significance selection is a hazard in the same way that one-tailed significance selection is. Consider that when publication selects for significant results of either sign, this doesn't always lead to bias in the meta-analytic effect size estimate. There is a loss of efficiency due to the censored studies in the middle, but the positive and negative results often cancel each other out. With this in mind, what is learned by a significant TES result? Does one learn that the naive meta-analytic result is necessarily wrong? Or is the idea that somebody has to be punished for file-drawering, even if the meta-analytic estimate is roughly unbiased? It doesn't seem very informative to scientific progress.

Some other corrections to the introduction may influence the interpretation of your results. Simonsohn and van Aert disagree (line 196) because they are considering different estimands and different meanings of heterogeneity. van Aert attempts to recover the overall mean of all studies whereas Simonsohn attempts to recover the true mean of only the significant studies. If it's Beta or Delta or Rho you intend to recapture, then van Aert is correct: p-uniform will overestimate the true mean under heterogeneity. You may need to reinterpret your p-uniform results accordingly.

Second, there are studies that have considered the FAT under heterogeneity. See https://www.ncbi.nlm.nih.gov/pubmed/12205693 and http://onlinelibrary.wiley.com/doi/10.1002/sim.1461/full.

I apologize that I must sound a bit slow given how much I did not quite understand. I assure you that I tried my best.

I always sign my reviews,
Joseph Hilgard


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: EXAMINING PUBLICATION BIAS—A SIMULATION-BASED EVALUATION OF STATISTICAL TESTS ON PUBLICATION BIAS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The revised manuscript successfully addresses my previous 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: EXAMINING PUBLICATION BIAS—A SIMULATION-BASED EVALUATION OF STATISTICAL TESTS ON PUBLICATION BIAS
Review round: 2
Reviewer: 2

Output:
Basic reporting: It's fine.

I don’t mean to be picky, but I found myself struggling with the language at points. Line 316, commas are misplaced. If I understand it correctly, it should read as, “For β = 0.5 in the 50% publication bias condition only 35%; for β = 1, 15%; for β = 1.5, only 9%; and in the heterogeneous condition, 22% of the studies employed publication bias practices.”

Minor points.

Line 383: Don’t you mean compared to the file-drawering condition?

You may find it helpful to make explicit what is the predicted quantity in Table 3’s OLS regression. It was not clear to me. The number of analyses conducted? The mean p-value?

Graphs may also be useful – in general, I found it difficult to interpret these many tables and their many numbers.
Experimental design: I find myself wishing there was more attention to the bias in the actual effect size estimate. I think the attention on the p-value and the p-value alone is rather shortsighted. I understand that this suggestion would potentially lead to a rather different paper, however.

This unusual emphasis on the p-value alone leads to unusual statements such as line 306, “Because the heterogeneous effect condition does not allow an absolute bias measure, the p-value deflation factor was used for all decisions.” I find this strange – why not conduct random-effects meta-analysis and compare the meta-analytic mean (and tau) against the true mean (and tau)? Consideration of the p-value deflation factor alone seems odd to me. If there is some true effect, I don’t particularly care whether 5/10 studies find it or 10/10 studies find it so long as the resulting meta-analytic estimate and inference is correct.
Validity of the findings: You may also consider the nature of your file-drawer condition. This is a relatively mild form of publication bias in that each agent has only a (1-(.95^10)) = 40% chance of getting a significant result, and if they get no significant result, they publish a nonsignificant result. More commonly, simulations like this generate k studies and publish only some percentage of the nonsignificant results. Compared to social psychology, where almost every published result is significant, having 60% of published results be nonsignificant may be pretty modest bias.

Also, does it really make sense to compare the power of tests under file-drawering vs. p-hacking given that they inflict different amounts of bias in the meta-analytic result? I can see the utility of comparing these methods against each other, but to make inferences about the power of the method under one scenario, as compared to another scenario, seems inappropriate. To say that methods gained or lost power in going from p-hacking to file-drawering seems to overlook that the two practices inflict different amounts of bias.

The noted weakness of the caliper test is interesting, namely that under less-than-huge K, few studies fall within the caliper. But at Line 357, discussing high false-positive rates of caliper tests, can you provide evidence that the underlying true effect yielded an overrepresentation of just-significant values? That doesn’t sound like something that should happen, if I understand how p-values work. It is also curious that this happens at what appear to be specific levels of Beta, N, and K, rather than behaving in some predictable relationship.

I am a little wary of endorsement of the TES given the numerous criticisms of it that have been published —see https://alexanderetz.com/tag/test-of-excess-significance/ for a compendium.
Additional comments: The revised paper is rather easier to read, and the conclusions seem sensible. FAT works well under homogeneity and one-sided selection, but the CT and TES may work under heterogeneity and two-sided selection.

I have a litany of suggestions, which you are free to accept or to reject. I do not want to be the reviewer who asks for a completely different paper, but I think consideration of these points would make for a clearer, more informative paper.


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

Input:
Title: A TYRANNOSAUROID METATARSUS FROM THE MERCHANTVILLE FORMATION OF DELAWARE INCREASES THE DIVERSITY OF NON-TYRANNOSAURID TYRANNOSAUROIDS ON APPALACHIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: This paper describes two new dinosaur specimens from the Late Cretaceous of New Jersey. Dinosaur material remains very rare in the eastern United States, so any new specimens are noteworthy and deserve publication, particularly as many of them are latest Cretaceous in age, so have relevance for understanding dinosaur diversity and biogeography during the run-up to the mass extinction. I have worked on several of the east coast theropod specimens, particularly the tyrannosauroids, and so I am happy to see new material discovered and described. There is no doubt that these specimens are worthy of publication in the scientific literature.

However, I cannot yet recommend publication of this paper. The presentation and content require major revisions. Here are my main issues. I hope you can address them, and at that point, the paper will be ready for publication in PeerJ:

1) More information is needed on how the specimens were found. Were they found associated? How close together were they, and in what orientation? What else was found with them? How do we know they belong to the same individual? Particularly as the metatarsal IV has marks indicative of shark feeding traces, and the specimens are found in a marine unit, meaning they must have been transported far from the site of death.

2) You need to make very clear which features support a tyrannosauroid affinity, rather than, say, an ornithomimosaur affinity. The best way to do this is to include them in a broad phylogenetic analysis of coelurosaurian theropods, like the Theropod Working Group matrix (most recent version: Brusatte et al. 2014, Current Biology).

3) Is the metatarsal II actually a metatarsal II? In proximal view there are notches on both lateral and medial surfaces, which is not the case of metatarsal II in tyrannosauroids (there is only a notch on the lateral surface, where metatarsal III articulates). What would be articulating with the medial notch if this is a metatarsal II? There is nothing there in tyrannosauroids. Also, the proximal end is much more bulbous compared to the shaft than in other tyrannosauroids. Are you sure this is not a metatarsal III of a non-arctometatarsalian animal?

4) On first glance, the specimens (especially the metatarsal II) do not strike me as obviously tyrannosauroid. They seem to be a little smaller and more gracile than the metatarsals of Appalachiosaurus/Dryptosaurus-like tyrannosauroids, not to mention the larger and more robust Tyrannosaurus-like species. One possibility is that they belong to an ornithomimosaur (see above). The other is that they belong to a juvenile. Therefore, comparisons with juvenile tyrannosauroids are needed. If the specimens belong to juveniles, ontogenetic variation may explain some of the differences with Dryptosaurus and Appalachiosaurus (both of which are known from larger, presumably more mature, holotypes).

5) The specimens seem somewhat deformed. Could this have caused some of the subtle shape differences compared to Appalachiosaurus and Dryptosaurus? I agree that metatarsal IV does not have the autapomorphically ‘flattened’ condition of Dryptosaurus (in which the proximal articular surface is much wider mediolaterally than long anteroposteriorly). However, deformation must be ruled out as the reason for this difference. The same is true of other observed differences.

6) You simply assert that the few differences between your new specimens and Appalachiosaurus and Dryptosaurus cannot be the result of individual variation. You have to back this up with evidence. What type of individual variation is present in the metatarsals of well-sampled tyrannosauroids, such as Tyrannosaurus, Tarbosaurus, Albertosaurus, or Gorgosaurus? And more importantly: what type of ontogenetic variation is present in these taxa?

7) The treatment of the ‘unnamed specimen from the Maastrichtian of New Jersey’ is problematic. This specimen is alluded to throughout the text without mention of its specimen number, until that number is finally given in the discussion. This is AMNH 2550-2553. It is not a tyrannosauroid, but rather, an ornithomimosaur. I suggest that you simply ignore this specimen for the time being and leave it out of your paper. It isn’t very relevant to the material you are describing.

On that note, you say that you are currently writing up a description of this specimen. You may not be aware, but my colleagues and I (Brusatte, Benson, Choiniere, Norell) began studying this material in 2012 and wrote an SVP abstract about it, which was peer-reviewed and presented at the 2012 Raleigh meeting. I respectfully ask you to respect the priority we have established in describing and naming this material. We will be writing a paper on it; we already have a draft manuscript.

8) I agree that the distal end of metatarsal IV is different in shape to that of Appalachiosaurus, as you describe. However, you also need to describe how it is different in shape to that of Dryptosaurus. You simply assert this without delimiting the specific anatomical features that differ.

9) The figures need to be labelled—point out the most important anatomical features.

10) What would really beef up this paper, and drive home the differences with Appalachiosaurus and Dryptosaurus, are comparative figures and tables. Show photographs of the new specimens alongside the same bones of the Appalachiosaurus and Dryptosaurus holotypes, and also present a table of measurements for the specimens.

11) You should include the new specimens in a phylogenetic analysis. There are very detailed, comprehensive phylogenetic studies of tyrannosauroids in the literature, which use vast datasets of anatomical characters including many features of the metatarsus. The most comprehensive is the recent Brusatte & Carr analysis (2016, Scientific Reports), which is a follow-up of an earlier study (Brusatte et al. 2010). You could simply score the new specimens for this dataset, run the analysis, and see where it is placed on the cladogram.

In that vein, I was very surprised to see that these two studies weren’t even cited to support the following statement:  ‘The tyrannosauroid taxa of this landmass, Dryptosaurus and Appalachiosaurus, have repeatedly been found outside Tyrannosauridae in phylogenetic analyses’. They need to be read, considered, and cited.

12) You consider Dryptosaurus as present in both the Campanian and Maastrichtian, and even as present in the same formation as the new specimens. Be careful here. Yes, several specimens from across eastern North America have been referred to Dryptosaurus, but this has not been based on autapomorphies, but rather on general similarity. The holotype of Dryptosaurus is Maastrichtian in age. Do any of these other specimens share unique features with the holotype? If so, then you can confidently refer them to Dryptosaurus. If not, then you should probably consider them Tyrannosauroidea indet. This is important, because the identification of these specimens factors into your biogeographic discussion and conclusions. In fact, your biogeographic discussion hinges, in a sense, on whether or not these specimens are truly Dryptosaurus or belong to another taxon.

13) I think it is way, way too premature to argue that Appalachian tyrannosauroids had a similar diversity to Laramidian tyrannosauroids. I am not convinced that what you have here is a ‘new morphotype’ rather than an individual variant of Appalachiosaurus, or possibly Dryptosaurus. But even if it is a new taxon, that means there are three known tyrannosauroids from the entirety of the Campanian and Maastrichtian of Appalachia. That is far, far fewer than the known number from the entire Campanian and Maastrichtian of Laramidia. Of course, there are huge sampling biases—much less is known about Appalachian dinosaurs, because much less outcrop is available for study. But, at this point in time, there is simply no positive data to suggest that Appalachia ‘probably enjoyed similar (tyrannosauroid) diversity’ to Laramidia, as you conclude in the discussion. It is an hypothesis that can be tested by future discoveries, but we certainly cannot conclude that it is correct at this point!

14) Finally, there are many misspellings and grammatical issues throughout—e.g., autopomorphy instead of autapomorphy. The references are presented in a random, non-alphabetical order. There are also some basic anatomical errors in this paper. Metatarsal II is said to have an articular surface for metatarsal III in medial view; however, it would be the lateral surface of metatarsal II that articulates with metatarsal III. The manuscript needs a careful edit to reach the standard needed for the peer-reviewed literature.

Steve Brusatte, Univ of Edinburgh, July 23, 2017


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

Input:
Title: A TYRANNOSAUROID METATARSUS FROM THE MERCHANTVILLE FORMATION OF DELAWARE INCREASES THE DIVERSITY OF NON-TYRANNOSAURID TYRANNOSAUROIDS ON APPALACHIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: OK
Experimental design: OK
Validity of the findings: Identification of the bones as belonging to Tyrannosauroidea is not well supported. Alternative identifications are not considered.
Additional comments: The paper describes partial theropod metatarsus (proximal fragments of metatarsals II and IV) from the Campanian Merchantville Formation of New Jersey, USA. Because of extreme rarity of theropod dinosaurs from Appalachia, this funding represents a considerable interest. The author referred the specimen to the Tyrannosauroidea based on metatarsal III (reconstructed) of crescentic shape and restricted to the plantar surface of proximal end of metatarsus. These characters are considered by author following Holtz (2004) as autapomorphies for the Tyrannosauroidea. However, these characters are found also in the Ornithomimidae. The author did not discuss the alternative identification of the described specimen as an ornithomimid and did not rule out this possibility. However, described bones show considerable similarity with some ornithomimids (see, for example, a well described metatarsus of Qiupalong henanensis; Xu et al., 2011). By gracile nature I think that the described metatarsals from the Merchantville Formation are more referable to an ornithomimid rather than to the tyrannosauroids, which had massive and robust metatarsals. The author violates the International code of Zoological Nomenclature (Article 36). Some other comments are introduced in the attached pdf.


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

Input:
Title: A TYRANNOSAUROID METATARSUS FROM THE MERCHANTVILLE FORMATION OF DELAWARE INCREASES THE DIVERSITY OF NON-TYRANNOSAURID TYRANNOSAUROIDS ON APPALACHIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The prose could really be cleaned up, especially with regard to passive voice and redundancy.

Literature references are incomplete and insufficiently used.

Professional article structure is present.

More measurements could be included.

Self-contained and the results are relevant to hypotheses, although overstated and incomplete in places.

See general comments and confidential note for details.
Experimental design: original primary research is present, although arguably incomplete.

Research question is defined, but more thorough comparisons could be made.

The knowledge gap is incompletely filled.

Ethical, but not rigorous.

Methods are described and replicable.

See general comments and confidential note for details.
Validity of the findings: Impact and novelty could be improved with additional study of specimens and literature.

Data are incomplete.

Conclusions are overstated in places.

See general comments and confidential note for details.
Additional comments: Dear Editor,

I submit to you my review of “A tyrannosauroid metatarsus from the Merchantville Formation of New Jersey increases the diversity of non-tyrannosaurid tyrannosauroids on Appalachia” by Brownstein (ms #19258). The article describes the partial metatarsus of a basal tyrannosauroid in comparison with other taxa and isolated bones, all from the late Cretaceous of Appalachia.

My opinions on the ms are mixed, as I am happy to see an additional specimen added to the roster of tyrannosauroids from the Appalachia, but the description strikes me as incomplete. In particular, the comparisons of the new metatarsus with other Appalachian taxa appear to be fairly superficial, perhaps owing to the fact that only two museum collections were visited. To really nail down the comparisons, all of the relevant specimens must be examined first hand and, ideally, side by side. For example, it appears that the holotype of Appalachiosaurus was not view first-hand, and comparisons were only made from the published literature.

I am not convinced that the author could really determine that “the spectrum of individual variation” of Appalachian tyrannosaurids was truly identified, since the relevant taxa are represented by only one specimen. Also, the author did not take advantage of the recent phylogenetic work on tyrannosauroids (e.g., Brusatte and Carr, 2016; Carr et al., 2017), where character states of the metatarsus are listed that could have helped flesh out the comparisons and characterizations of the new material and the other species.

The figures could be more fully labeled so that they correspond to the observations made in the text. The captions are incomplete for metatarsal IV.

I think a table that summarizes all of the major similarities and differences between the new metatarsus and other Appalachian taxa would greatly benefit the manuscript.

The prose could really be cleaned up, especially with regard to passive voice and redundancy.

The biogeographic conclusions are somewhat overstated and can be simplified to just the facts.

In conclusion, I think the author could satisfactorily make the necessary revisions and so I recommend “major revision”.

The author may know my identity: Thomas D. Carr.

My specific comments are below.

Sincerely,

Thomas D. Carr, PhD
Associate Professor of Biology
Carthage College

Specific comments:

Lines 7-10: overuse of the word “obscure” and its variants.
Lines 9-10: “do seem to be”; passive voice – fix.

Lines 10-11: “significant”; this word has statistical meaning and should not be used informally here.

Lines 18-20: the spectrum of variation cannot be known for taxa that are represented by only one specimen – please fix.

Lines 19-20: replace “as well as by factoring in” with “and”.

Lines 19-20: replace “The new specimen thus has significance for representing” with “Therefore, the new specimen represents”.

Lines 21-25: convoluted – just state the result.

Last sentence of abstract: change to “Appalachian non-tyrannosaurid tyrannosauroids had a diversity that was comparable to tyrannosaurids in Laramidia during the Campanian”.

Line 31: in what way is Appalachia “very poorly known”? Clarify.

Line 31: replace “comparison” with “contrast”.

Line 40: delete “repeatedly”.

Lines 42-44: how is all of that unfortunate? Clarify.

Line 52: delete “described herein thus”.

Line 53: insert “a new,” between “possibly” and “unnamed”.

Line 53: delete “dinosaur”.

Line 54: replace “. Thus, the specimen adds to the diversity of the clade Tyrannosauroids” with “, adding to the diversity of the the clade”

Line 55: replace the comma with a period.

Line 55: replace ”suggesting” with “The specimen is evidence that”

Lines 56-57: replace “the aforementioned” with “that”.

Line 61: replace “the described” with “this”.

Line 67: in my experience, the full AMNH specimen number abbreviation is “AMNH FARB”.

Line 77: delete “described herein”.

Line 77: replace “retrieved” with “collected”.

Lines 77-81: were the two bones found together? State explicitly.

Line 79: replace the ampersand with “and”.

Lines 81-85: any radiometric dates? If so, please include here.

Lines 98-104: what are the sizes of the specimens?

Line 107: replace “of metatarsal II with” with “for”, and label the feature in the figure.

Lines 110: explain what is meant by “a more prominent articular facet”; this is vague – be exact.

Line 111: delete “exists”.

Line 111: insert “Therefore,” before “The”.

Line 112: delete “thus”; “not as distinct” is vague – be exact; delete “in medial view”; “and,….metatarsal II.” is convoluted – fix.

Line 115: replace “slight” with “shallow” and label it in the figure.

Line 118: delete “as measured along the proximal surface”.

Line 119: replace “better” with “best”.

Line 120: replace “metatarsls” woth “bones”; insert “that are” after “scrapes”.

Line 124: replace “confirms” with “is evidence”; replace “being” with “it was”; delete “and preserved”.

Line 125: “a sharp ventral edge” is vague – clarify and label in the figure; replace “rounded” with “convex”.

Line 126: is the ventral surface flat? Clarify.

Line 128: “just above the diaphysis” is vague – clarify.

Line 133: replace “suggests the presence of” with “is evidence for”.

Line 134: delete “having”.

Line 135: “plantar” – be consistent with terminology throughout the ms.

Line 136: what is the specimen number of the unnamed specimen? Mention it here.

Line 136: replace “also…specimen” with “less pronounced than in YPM…obs.); delete “distinguishing the two specimens”.

Line 138: delete “unnamed New Jersey specimen’s”.

Line 139: insert “of New Jersey” after “IV”; “a much thinner shaft” is vague, provide measurements; delete “(pers. obs.)”.

Line 140: deete “notably”.

Line 143: replace “further be” with “also be”, delete “in…latter”.

Lines 149-152: Delete “In…2011).”

Line 154: replace “an even less noticeable” with “more aubtle”.

Line 161: give the estimated total length here.

Line 167: “temporslly differentiated” is vague – be exact.

Line 171: give the measurements instead of giving “pers. obs.”

Lines 172-173: list all of the differences in a new paragraph here or provide a table of comparisons and differences.

Line 173: delete “morphological” from here and elsewhere.

Line 175: replace “element” with “bone”.

Line 178: “less robust” is vague – be exact.

Line 182: delete “the assignment of”, insert “is assigned to” after “21795”; delete “is considered best”.

Line 184: list the comparisons!

Line 184: delete “and this indeterminate taxon,”; delete “dinosaur”.

Line 186-187: fix the sentence that starts with “The identification”.

Line 188: replace “from” with “in”; replace “corresponding to this landmass” with “of Appalachia”.

Line 196: replace “a possibly” with “an”, replace “animal” with “taxon”.

Line 201” replace “tyrannosaur” with “tyrannosauroid”.

Lines 205-206: delete “especially…account”.

Line 207: replace “enjoyed” with “had a”.

Lines 210-212: convoluted – fix.

Line 217: what are the differences? List them here.

Line 218: replace “currently…author” with “in progress”.

Lines 218-219: what are they? Be exact.

Lines 221-237: doesn’t all of this boil down to a sampling issue? Delete.

Line 246: delete “from the lower 48”.

Line 247: replace “tyrannosaur” with “tyrannosauroid”.

Lines 248-250: Delete.

Line 254-255: replace “. Additionally thank” with “, and”.

Lines 255-256: delete “in…History”.

Figure 2 caption: the caption is incomplete – what is the arrow pointing to? The distal condylar region is not included.


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

Input:
Title: A TYRANNOSAUROID METATARSUS FROM THE MERCHANTVILLE FORMATION OF DELAWARE INCREASES THE DIVERSITY OF NON-TYRANNOSAURID TYRANNOSAUROIDS ON APPALACHIA
Review round: 3
Reviewer: 1

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: I thank the author for taking into account all of my suggestions and carefully revising the manuscript. I may have a few quibbles about some of the anatomical details, but at this point, I think the author has been very rigorous and deserves to have this manuscript published so others can assess the specimen.

One thing I would ask the author to do: explain in more detail the phylogenetic analysis and how it was conducted. It is said that a ‘strict consensus analysis’ was run in TNT. This doesn’t make sense. I presume the author means that the analysis was used to generate a strict consensus phylogeny of the most parsimonious trees, after the analysis was conducted. So the author needs to be clear on what protocols were used in the analysis: New Technology search (and the specs)?, TBR branch swapping (and the specs?) etc. The author should try to follow the exact protocol that we outlined in the Brusatte & Carr (2016) paper, to make it maximally comparable with our analysis.


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

Input:
Title: A TYRANNOSAUROID METATARSUS FROM THE MERCHANTVILLE FORMATION OF DELAWARE INCREASES THE DIVERSITY OF NON-TYRANNOSAURID TYRANNOSAUROIDS ON APPALACHIA
Review round: 3
Reviewer: 2

Output:
Basic reporting: In many places the prose is convoluted and compromised by redundancy and passive voice.

The literature references are sufficient.

Sufficient background and context is given.

A professional article structure is followed, although subheadings for comparisons with other taxa might be helpful.

The article is self-contained, although I think that the issues of individual and ontogenetic variation can be carried out more rigorously and concisely (see comments to author).

The author may know my identity: Thomas D. Carr, PhD
Experimental design: The article is within the aims and scope of the journal insofar as evidence for a new taxon of tyrannosauroid is presented, although based on a poorly preserved specimen.

The research question is straightforward, where the author presents evidence for a new taxon of Campanian tyrannosauroid; given the limited nature of the fossil, it fills a very small gap in our knowledge.

However, I am concerned that it hasn't been compared side-by-side with Appalachiosaurus, especially given that some differences between them are the result of damage to the Merchantville specimen (see ms Table 2).

I don't think the comparisons made are rigorous (see comments to author), but these can be improved.

The methods are adequately described and replicable, although I would run the Merchantville specimen in the latest TWiG matrix, not the Loewen et al. (2013) matrix.

The author may know my identity: Thomas D. Carr, PhD
Validity of the findings: Given the nature of the Merchantville fossil, and the limited scope of the paper, the impact is not great beyond the addition of a new tyrannosauroid from Appalachia. Not much can be said beyond that.

The novelty is limited to the possibility of a sympatric tyrannosauroid with Appalachiosaurus, but given the wide range of the age of the Merchantville Formation, they might not really have lived at the same time.

The Merchantville specimen does not reveal anything new about tyrannosauroid evolution, aside from increasing its diversity by one taxon.

The data are robust, but the RI for the Merchanville taxon is compromised by deformation (table 2), which reduces my confidence in its difference from Appalachiosaurus.

The conclusions are fine, but the closing statements regarding incomplete specimens isn't needed since the limited amount of information they contain is a given.

Speculation is thankfully avoided.

The author may know my identity: Thomas D. Carr, PhD
Additional comments: October 9, 2017

Dear Dr. Farke,

I submit to you my review of the second draft of “A tyrannosauroid metatarsus from the Merchantville Formation of Delaware increases the diversity of non-tyrannosaurid tyrannosauroids on Appalachia” #19258, by C. D. Brownstein. The author has taken care of many of the issues that I raised in the first draft, but some nagging problems remain: the prose is compromised by passive voice and excess verbiage, the introduction needs to be almost entirely redrafted, first-hand comparisons have not been made with Appalachiosaurus, and the discussions of individual and ontogenetic variation should be more rigorous.

The bottom line is that the sample sizes for the three taxa of concern are, effectively, one each; therefore, the only resort to clarifying individual and ontogenetic variation is for the author to examine a growth series of metatarsals of a known tyrannosaurid. Such a growth series is available at the AMNH, based on the Albertosaurus bonebed material. Using that, the author can parse out the features that do change with size (as a proxy for maturity, size is not the best option - I know - but the gross patterns should be clear) and those that don’t, and then compare the corresponding features with the other Appalachian fossils to identify which ones are taxonomically informative and which aren’t. If this was my project, that’s what I’d do.

If this procedure is followed, then the author would arrive at defensible, empirically based statements such as:

“The RI does not change in the growth series of A. sarcophagus, where it is 0.33 in all specimens. The RI of the Merchantville specimen is less than this and that of Appalachiosaurus; therefore, it is a different taxon from them. The RI of Dryptosaurus is 0.15; therefore, the Merchantville specimen is not referable to Dryptosaurus. Given these differences, the Merchantville metatarsus represents a new morphotype, and hence a new taxon.”

Or,

“In end view, the distal end of metatarsal IV is triangular and rectangular in the growth series of A. sarcophagus, without any pattern. Therefore, the triangular shape of the joint surface in the Merchantville specimen is taxonomically and ontogenetically uninformative, and so it is not a reliable point of comparison with Dryptosaurus and Appalachiosaurus.” And so on.

Unfortunately, I still think substantial revisions must be made. Please see my specific comments below for more areas of improvement.

Sincerely,

Thomas D. Carr, PhD
Associate Professor of Biology
Carthage College
Kenosha, WI 53140

Specific comments

Abstract
Line 11: replace “this latter landmass” with “Appalachia”.
Line 12: replace “of….apparently” with “were”.
Lines 12-13: replace “Laramidian ones” with “Laramidia”.
Lines 13-15: these sentences can be shortened and combined into one.
Lines 17-19: The justification for giving the metatarsus such attention must be stated here: is it well-preserved enough to bring new insights into Appalachian tyrannosauroid diversity and evolution?
Line 19: replace “may” with “can”.
Lines 21-23: please list the defining features here; otherwise this sentence is just indicative.
Line 24: replace “morphotype” with “taxon”.
Lines 25-26: adding a new taxon is not a test of the hypothesis that Appalachia was a refuge of relict taxa – it is just evidence of a new taxon. The evidence for a relict taxon is its phylogenetic position; so, if it falls out in a cladistic analysis outside of Bistahieversor, then you have evidence for a basal, relict tyrannosauroids. Otherwise, you don’t. I.e., please state the results of your phylogenetic analysis in the abstract.

Introduction
Lines 29-32: this first sentence is unnecessary – just get to the point, which is in the second sentence.
Line 46: keep in mind that we didn’t run a Bayesian analysis in Carr et al. (2017); the results published there were from a parsimony analysis.
Lines 46-49: redraft this sentence as “The fossil record of tyrannosauroids from Appalachia is limited to the holotypes of Dryptosaurus and Appalachiosaurus, undescribed partial specimens, and isolated bones and teeth.”
Lines: 50-88: This section is written like the discussion and conclusions, not a proper introduction that justifies the project, defines the research question and its importance and novelty, describes the methods and the main objectives of the project. Redraft.

Methods
Lines 92-95: As with the earlier draft, the author has not seen the holotype of Appalachiosaurus first hand.

Material
Lines 136-157: please restructure this by first stating the arctometatarsalian features that do not help to identify the taxon, followed by the unambiguous tyrannosauroid characters.
Lines 158-180: it isn’t at all clear if these features are seen in the specimen or not; for each feature, describe what is seen in the purported tyrannosauroid so that the reader can clearly see what features you are eliminating and why.

Lines 181-184: this is the biggest blunder of the article, given that Brusatte and Carr (2016) combined the data sets of Loewen et al. (2013) and Brusatte et al. (2010) to resolve the huge differences in results obtained from those data sets.

Therefore, scoring the specimen into the Loewen et al. matrix makes no sense on theoretical or practical grounds – it is just irrelevant. In fact, Carr et al. (2017) updated the Brusatte and Carr (2016) data matrix with additional characters (and taxa), so that should be the data matrix used to assess the affinities of the metatarsus, if it is a tyrannosauroid. Please redo the phylogenetic analysis using the most complete and up-to-date data set.

I also recommend scoring the specimen in the latest version of the TWiG (Theropod Working Group) data matrix to assess the identity of the metatarsus among Theropoda as a whole.

Line 181: delete the underscore in the specimen number.
Line 184: insert a space between the parentheses.

Description
Line 187: delete “noticeably”.
Line 189: replace “may be found” with “are”.
Line 190: is it deformed by the erosion or by something else? Clarify.
Lines 187-275: this part of the manuscript is rife with passive voice; please fix, which will help to shorten the text somewhat.
Lines 207-234: these sections are a return to assessing the taxonomic identity of the specimen, which is confusing. Please move the relevant parts up to where the identification as a tyrannosauroid is justified and referral to Ornithomimosauria is rejected.
Line 235: perhaps each metatarsal should get their own subheadings in the description to aid the reader.
Line 250: a comma usually precedes the words “but” and “which”.
Line 274: insert “long” after “mm”.

Discussion
Line 295: it is said here that the specimen was coded into the matrix of Brusatte and Carr (2016), whereas earlier it was stated that it was scored for the Loewen et al. (2013) data matrix – which is it? Please fix.
Lines 302-304: this description of the topology is ambiguous – how can the metatarsus and Bistahieversor both be the sister taxon of Tyrannosauridae? Please clarify and include a figure of the results.
Lines 304-306: analysis in the Loewen et al. matrix is unnecessary, as explained above.
Line 307: state the characters that support the position of the metatarsus on the topology before mentioning features that were not included in the data matrix.
Lines 310-314; please state how the RI was obtained, state the result, and give some indication of how it is different from tyrannosaurids.
Lines 315-317: this introductory sentence is convoluted; please rephrase concisely.
Line 330: the phrase “Regardless of the ontogeny” is confusing, as what is meant by that is not explained. Please simplify this sentence to refocus it on the comparison with Dryptosaurus.
Lines 333-335: make sure that this sentence is in reference to the Brusatte and Carr (2016) data matrix, because as stated here you could be talking about that analysis or the Loewen et al. results. Please fix.
Lines 336-341: both of these sentences say the exact same thing – get rid of one of them!
Line 349: the sentence “Description…author.” adds nothing; please delete.
Lines 347-360: I’d consider discarding this section, since you do not unambiguously assess the taxonomic identity of the AMNH specimens.
Lines 365-370: I’d rephrase this to say that the Merchantville metatarsus is approximately the same size as the Dryptosaurus and Appalachiosaurus fossils, and the differences between them are almost certainly not ontogenetic since the bones in the same taxon of the same ontogenetic stage would converge upon the same morphology.
Lines 361-412: this is an unacceptably long paragraph; I recommend breaks at lines 371, 378, 384, 393, 403.
Lines 371-373: the sample size for these taxa is effectively one each – please be exact to convey the point that individual variation is simply impossible to document for them.
Lines 376-378: size is a poor proxy for relative maturity, so the real limit on assessing ontogeny is the same for that of individual variation – you’d don’t have a adequate sample to work with. Fix.
Lines 382-384: You should compare the Merchantville specimen side-by-side with Appalachiosaurus in person. Briefly remind the reader here of what the difference are between the two.
Lines 384-390: I don’t find the argument of geographic separation to be convincing, especially when both taxa are on the one and the same landmass.
Lines 387-390: this sentence is too convoluted; be concise.
Lines 384-413: I think that all of this can be boiled down to one paragraph that summarizes the salient differences between the Merchantville specimen and Appalachiosaurus, excluding the biogeographic argument. What would potentially seal it is comparisons of the RI of metatarsals of the same species of tyrannosaurid that are the same length.
Line 403: please define what the RI is, and what measurements are used.
Line 407: please include the RIs here for T. rex and A. sarcophagus. Please include the RI for Dryptosaurus.
Line 408: delete “the author regards”.
Lines 408-411: the only relevant line of evidence to separate the two is the morphological differences. Revise.

Biogeography
Line 417: replace “morphotype” with “taxon”.
Lines 421-423: this sentence is redundant; delete and modify the following sentence accordingly.
Lines 429-430: delete this sentence; it does not contribute any meaningful information, especially since there are no overlapping bones with the Merchantville metatarsus.
Line 433: you have provided evidence for increased diversity; please delete.
Line 438: this could be changed to “cf. D. sp.”.
Line 451: insert a space between the parentheses.
Lines 457-460: restate this as a specific, defensible hypothesis or delete.
Lines 461-465: convoluted and excessively long sentence – please trim down and clarify.
Lines 469-471: there isn’t a clade – the Appalachian taxa form a grade, so there’s nothing to name.

Conclusions
Line 475: I think it is acceptable to say the morphotype is a new taxon, which you have wisely not named.
Line 477, and above biogeography discussion: I recommend that you avoid discussing the affinities of the other Appalachian material unless they are metatarsals. I think that teeth and postcranial bones that are not metatarsals are beyond the reach of what you actually have described. It is sufficient to mention those fossils, but it is important to point out that their identity cannot be assessed based on the Merchantville metatarsals, since none of them are associated with a metatarsus.
Lines 481: I’d restate this in terms of the challenge of identifying isolated bones that that autapomorphies.

Acknowledgements
Lines 487-493: make sure that you thank your reviewers by name.

Figures
The font size of the labels are different; please standardize.
I recommend adding a comparative figure of the Merchantville specimen side-by-side with the corresponding bones from the holotypes of Dryptosaurus and Appalachiosaurus.

Table 1.
Insert a space between adjacent sets of parentheses.
Insert a + next to “112” if that number is artificially low.
Table 2.
Insert a space between the parentheses and the preceding text.
“(this paper)” is unnecessary; delete.

Supplemental material
I recommend that the analysis of placing the Merchantville specimen within theropod (as a test of the Ornithomimosaurian hypothesis) be done using the latest version of the TWiG data matrix, not the Loewen et al. (2013) data set.


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: ACUTE ISCHEMIC PRECONDITIONING DOES NOT INFLUENCE HIGH-INTENSITY INTERMITTENT EXERCISE PERFORMANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Ischemic preconditioning (IPC) has been suggested as a novel treatment that has the potential to improve exercise performance. The current study is aimed to examine the acute effect of IPC on intense intermittent exercise performance and associated physiological markers in amateur soccer players. Subjects were divided into three groups receiving: a) IPC (high pressure exerted on each thigh during blood occlusion phase); b) IPC SHAM (low pressure exerted on each thigh during occlusion phase); and c) control (no treatment). Following the treatment, YoYo intermittent Endurance Test level 2 (YoYoIE2) was performed to evaluate intermittent maximal exercise performance in each group. The results showed that IPC has no significant effect on players’ performance of YoYoIE2. In addition, there was no marked difference in lactate concentration, rate of perceived exertion, and heart rate between the three groups.  These results show that IPC does not have any influence on vigorous intermittent exercise duration in amateur soccer players or related biomarkers.
Experimental design: see below
Validity of the findings: see below
Additional comments: Points:
1. The following sentence is shown in lines 138-139, “Mean HR and peak HR presented no difference (p=0.17) among the three trials (Table 1).” However, in table 1, the p value of HR peak is presented as 0.06 instead of 0.17. Could the authors explain which the correct p value for HR peak is?

2. It is concluded in this article that “IPC does not influence high-intensity intermittent exercise performance in amateur soccer players”. However, the study only tested IPC protocol consisting of four cycles of 5-min occlusion. Could the authors justify why they use this IPC protocol? Both the number of cycles and the duration of occlusion may have significant effects on exercise performance. To confirm their conclusion, different IPC protocols (such as increasing or decreasing the IPC cycles) should be tested for their effects on exercise performance. Furthermore, the current study should clarify in their conclusion that only acute IPC did not have effect on their exercise performance, because the study has not tested the effectiveness of chronic IPC protocols (for several days or weeks), which could be a future direction.

3. “HR” shown in line 29 in abstract should be defined first time shown in text; IPC in figure 2 should be defined in its figure legend.

4. The authors only measured 13 players, whose sample size is too small to justify their conclusion. Why did the authors say this suffices for statistical points? Please discuss the limitation of this with convincing details.

5. The discussion on the molecular levels of such study is not in-depth. Reactive oxygen species play an important role in both IPC and exercise. The authors need to discuss this aspect by adding a few sentences like this:
“Exercise can strengthen the body against ROS attack through redox-associated IPC preconditioning. This exercise-induced adaptation involves the enhancement of cellular antioxidant capacity to reduce ROS levels. Increased ROS generation in striated muscles plays a critical role in exercise adaptation as it can trigger exercise-mediated adaptive responses through redox regulations…..” Here for above the authors should cite the following recent key papers by experts in the fields: 1) Front Physiol. 2016; 7: 486. 2016. doi:  10.3389/fphys.2016.00486; 2) Cell death & disease 4 (9), e787, 2013.

6. In lines 41 and 42, change “its supposed exercise enhancement is still to be clarified” to “its supposed exercise enhancement has yet to be clarified”

7. In lines 42-44, change the sentence “Among potential mechanisms of IPC to exercise enhancement, are highlighted…” to “Potential mechanisms of IPC exercise enhancement are hyperemia (5-6 fold increase in muscle blood flow) during reperfusion (Libonati et al. 2001), attenuated ATP depletion, and increased phosphocreative production/oxygen uptake during the reperfusion phase (Andreas et al. 2011).”

8. In lines 51-53, change the sentence “In this context, the YoYo intermittent endurance test…” to “The YoYo intermittent endurance test level 2 (YoYoIE2) is useful to simulate high-intensity intermittent exercise similar to the activity seen in team sports, and is effective due to its simplicity, reproducibility, and its association with both V ́ O2 and citrate synthase activity in untrained men”

9. Please clarify what team sports are being simulated by the YoYo test. It is too vague to attribute high-intensity intermittent exercise to team sports in general as every team sport is very different from one another.

10. In lines 55-59, it is stated that “aerobic energy production plays a more important role in fatigue resistance in the untrained during the YoYoIE2 compared with trained soccer players” however, high-intensity intermittent exercise implies predominantly anaerobic energy production. What is the role of aerobic energy production in the YoYoIE2 test?

11. In lines 170-171, change “These same authors have been argued that there are IPC responders and non-responders” to “These same authors have argued that there are IPC responders and non-responders”. Also, please clarify what is meant by IPC responders and non-responders and what differs between the two.


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: ACUTE ISCHEMIC PRECONDITIONING DOES NOT INFLUENCE HIGH-INTENSITY INTERMITTENT EXERCISE PERFORMANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The study investigated the acute effects of ischemia preconditioning on hign intensity intermittent exercise  performance in amateur soccer players. The authors found out that IPS had no influence on the exercise performance.
Experimental design: It's good.
Validity of the findings: OK.
Additional comments: Please confirm the IPS protocol did have a effective stimulation on the subjects. Any marker from the blood immediately can be used to evaluate the response of subjects to IPS before the exercise?