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: MOVING TO 3D: RELATIONSHIPS BETWEEN CORAL PLANAR AREA, SURFACE AREA AND VOLUME
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comments
Experimental design: 83-84 / 196: Authors need to be more clear about exactly which metrics they are going to compare between 2D and 3D. Cover, abundance and size seem to be used interchangeably however they are not (necessarily) the same. I expect that the authors know this, but it could be more clear.

121: Three photographs each time the coral was repositioned or one for each of three orientations? How was this data used in the regressions? Was an average used or was each used as an independent data point? This will either lead to error in the predictor or pseudo-replication, both of which should be avoided in OLS linear models …

174: As written it is not clear why live surface area is more ecologically meaningful, especially in regards to the creation of 3D structure on the reef, which is present whether or not a calcium carbonate structure is covered with live coral tissue.

175: What is the magnitude of the error here? I am concerned that this was not reported, especially as this was used as a predictor variable (which should not have error). It would be very useful to know how variable the SfM reconstructions are.

194-201: This paragraph is confusing as written and the first sentence is misleading. Also, at least a sentence (or two) of why a CT scan can be used to validate photogrammetry from SfM should be included.
Validity of the findings: No Comments
Additional comments: I appreciate the approach and am confident in the quality and rigor of work presented here. This is a powerful and innovative tool that they are recommending which could lead to very important and needed changes in the ways that coral reefs are studied. However, the introduction does not provide a well formed biological argument to justify their approach. The discussion does a better job in this respect, but arguments could be elaborated. As they are recommending that these tools be used in monitoring, the authors should spend more time explaining the details of the meshing and calculation of area, which are non trivial and can result in fundamental differences in data types and quality. I would like to see this paper go in a more ecological direction or a more methodological direction (preferably the former) and recommend that the introduction and discussions be retooled to this effect. With these changes, I would be very happy to support this manuscript.

Line-by-line comments:
7: It is not clear how the methods used here represent a tool that can used to incorporate 3D metrics in monitoring. More specific biological / ecological argument explaining the utility of these metrics is needed.
21: The paragraph does not explain how changes in 3D metrics are more meaningful than changes in 2D metrics.
45-46: I’m having trouble with the logical basis of this argument (not that I necessarily disagree with it). A great deal of the paper is devoted to showing that 3D metrics can be estimated from 2D metrics. Is this a good justification for the incorporation of 3D approaches?
51-52: How do they modulate ecosystem services? How do they support reef assemblages? At several points in the manuscript examples are given in this manner without any elaboration. It would greatly improve the quality of the manuscript if there were specific biological and ecological explanations and not simply lists of examples.
83-84 / 196: Authors need to be more clear about exactly which metrics they are going to compare between 2D and 3D. Cover, abundance and size seem to be used interchangeably however they are not (necessarily) the same. I expect that the authors know this, but it could be more clear.
317-318: This argument is not well formed.
344: This paper presents data of single coral photogrammetry and planar imagery of single corals. It is not clear how these techniques can be used to measure numerical abundance or cover at the scale used by most monitoring programs.


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: MOVING TO 3D: RELATIONSHIPS BETWEEN CORAL PLANAR AREA, SURFACE AREA AND VOLUME
Review round: 1
Reviewer: 3

Output:
Basic reporting: The submitted text is written in a professional English language, is clear and unambiguous as demanded by the guidelines. They contextualize the issue of obtaining geometric descriptors of corals, as they are used in most of the monitoring protocols of coral reefs, with key references. They argue in favor of shifting from 1D/2D approach to a 2D/3D approach, based on references that present modern techniques to obtain these parameters. There is only one concept that I think they need revising for the sake of precision, which is the concept of Photogrammetry. Photogrammetry is the science of obtaining reliable and accurate measurements of an object using photography. The use of multiple photographs to build a digital model is a specific activity of the science. So this is just a matter of rewrite the sentence. The structure of the paper conforms to PeerJ standard and discipline norm and is plainly clear. All figures are relevant and have good quality and descriptions but some lack labels (Figure 2). Raw data are supplied as Supplemental files but not for publication.
Experimental design: The paper presents an original research that is primarily Biological in scope, with a geometric approach as a tool for determining organismal surface and volume size, that is applicable to assess structural stability or biomass, for example. The two well-defined research questions are 1. Can one predict 3D metrics (volume) fro 2D metrics (area)? 2. Are photogrammectric techniques appropriate to estimate surface area and volume of coral skeletons of different morphotypes? These questions are relevant because one can increase accuracy of the metrics of corals that are useful in evaluating vulnerability and resilience of a reef system, based on coral morphology. The proposed photogrammetric technique was proposed as a cost effective tool to approach coral morphology. The number of coral replicates and data replication was appropriate to the accuracy and robustness of the statistical tests the authors applied. The methods are well described, with sufficient detail in general. However, when addressing the use of planar photographs, I found the description lacking details as to the calculation of the planar area on the photographs. They state “using methodology and code from Madin et al. (2014).” but I did not find any detailed calculation description or the R codes in the cited paper. There isn’t supplementary material in the publisher site either.
Validity of the findings: The results are robust, the statistics they used is sound and the conclusions, thus, robust either. They present the results in a straightforward manner. The figures illustrate well the relationship between the planar view descriptors and the CT derived descriptors, demonstrating the possibility of deriving the 3D metrics from the planar descriptors, if coral growth form is considered. They propose predictive functions for each descriptor per morphotype to be estimated from the planar descriptors. They also show that the photogrammetric technique is useful to calculate 2D and 3D descriptors, although still not as cost-effective as the planar photographs.
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: COMPLEX VERSUS SIMPLE MODELS: ION-CHANNEL CARDIAC TOXICITY PREDICTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: Line 64, give a sentence explaining that torsades de pointes is.  This should help explain why you use APD90 later.

Line 87, please give some information about Credible Meds.  Why is their rating the one you chose?  Are they considered the gold standard by the field?  Are there other ratings?  If so, what are the advantages and disadvantages of these other ratings and why were the other rating systems not chosen?

Line 100, change “the reduces the flow” to “that reduces the flow”

Line 105, change “known (KR)” to “known risk (KR)”

Line 112  – How was the EFTPC calculated?  Was it the average concentration for the clinically approved dose?  Was protein binding taken into account when comparing in vitro and clinically effective concentrations?

Line 117, What is the AP predict platform?  Briefly describe it in 1-2 sentences.

Line 128, Why is your parameter called Bnet?  Is it because it’s the “net difference” between the repolarization and depolarization block?  If so, consider using the words “net difference” in the definition of Bnet so that the reason for the name is clear.

Line 131 – which ion channels are polarizers and depolarizers?

Line 132 – Where did the idea to use APD90 come from?  Have other metrics been used in the past prediction?  Would the results be expected to change with a different threshold, say APD80?  Or are there other metrics one might consider?

Line 140 – An algorithm is described for using the complex model to assess risk, using the logistic regression presented by Cummins Lancaster and Sobie.  Can the author explain who these people are?  Did they develop either the gold standard model or the cardiac safety simulator?  Is this the only method that has been used to predict cardiac toxicity risk or are there others?  Is there consensus from the community that this metric is best?

Line 155, Line 207, Table 1 caption – add the words “ROC AUC” to make the phrase “leave-one-out cross validation ROC AUC” for clarity

Figure 2 – This figure is a bit hard to read.  It is hard to compare across panels because there is a different coloring and order for Crumb as for the other two.  For instance, iKr is red in two plots and yellow in the third.  I would propose the author redraw this figure so that all the key features of the data described in the text stand out in the figure.  I suggest
1)	Use just a single panel instead of 3 panels.
2)	Change the shape and color of the points based on the reference (Mirams, Kramer, Crumb)
3)	Sort the ion channels by variability rather than alphabetical order, such that the channel with the greatest variability (iKr) appears first
4)	I also suggest making this a forest plot where the ion channel labels are along the y-axis and the % block along the xaxis.  In this way, both names for the receptors [e.g. hERG (iKr)] can be printed and easily read.  This would be helpful for readers who may have some passing familiarity with hERG, but don’t know the “iKr” nomenclature.

Line 183 – delete the word “As” – currently this is a run-on sentence

Line 185 – I propose stronger language, deleting the words “has the potential to” because the key result is that the Bnet model does outperform the others.

Line 187-200.  This text belongs in the introduction as this text all describes background results from two previous studies.   The author could still briefly recap what this work adds over the previous studies in the Discussion section.

Line 187 – what are “those” previous studies?  Is it Colatsky and Mistry from the previous paragraph?  Please cite the two studies again, just for clarity.

Line 192 – The author is talking about the advantage of CredibleMeds to other classification schemes, but the author hasn’t described these other classification schemes.  What are the other schemes called?  Who has used them in the past?  And do the results change depending on the classification scheme?  Are there any other advantages to these schemes over CredibleMeds?

Line 207 – I don’t understand why the predictive accuracy of these three models cannot be prospectively tested.  Couldn’t they still be tested for drugs that are predicted not to have a TdeP risk and then either do or do not show this risk in the clinic.

Line 212 – replace “if not” with “or”

Line 213-221 – I propose deleting all but the first sentence of this paragraph because the rest of the paragraph just restates in detail all the results that were just presented in the Results section.  All that is needed here is a summary of the key message.

Line 237 – need comma after “available”

Line 238 – I don’t understand what it means to make the Bnet variables time dependent.  How would one then derive a single metric from this?

Line 243 – Propose adding the following text (demarked with asterisks)  In summary the study conducted here highlights the importance of benchmarking *complex models against simpler models*.
Experimental design: Line 192 If feasible, I’d ask the author to consider generating a new Figure with the results for alternative classification schemes (to CredibleMeds) to see if the results stay the same, or if a different model becomes the winner.  If this is not possible, (because the other classification schemes are not available for all compounds on the other studies, or for other reasons) then please say why it’s not possible.
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: COMPLEX VERSUS SIMPLE MODELS: ION-CHANNEL CARDIAC TOXICITY PREDICTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This article reports what has been done well, it is clear and unambiguous. I was able to reproduce all of the results that I tried to using the supplementary data files.

In terms of how the biophysically-detailed models are presented (‘gold-standard’ and ‘cardiac safety simulator’) I strongly suggest using their names instead (‘O’Hara 2011’ and ‘Ten Tusscher 2006’).

In the first case, whilst O’Hara may be a leading model some of its strongest advocates are optimising it for studies of drug action, so do not consider it a gold standard. I know that this term has been taken from a previous study, and that the use of italics may imply some questioning of that name, but I don’t think these subtleties will come across and it would be preferable to call it by its original name. (Incidentally updated versions of O’Hara have been published recently by the FDA team, I would be happy to provide a CellML file for this which we are working on testing at the moment and will publish shortly, if the author would like to re-run with the ‘CiPA v1.0’ O’Hara model).

In the second case, whilst the commercial ‘Cardiac Safety Simulator’ uses Ten Tusscher 2006 it is not the Cardiac Safety Simulator model.  The model in this study is simply the Ten Tusscher 2006 model, and was used for exactly this purpose in Mirams et al. Cardiovasc. Res. (2011). It would be better to simply call it Ten Tusscher (2006). I think the Cardiac Safety Simulator provides some additional endpoints in terms of a contraction model and electro-mechanical window etc. too.

In the introduction it is stated that “including more detail…the degree of structural uncertainty [increases]”. This sounds like common sense: at some point I agree there will be too much detail. But up to a point, the complexity may be warranted, parameterisable, and 'selectable' as a structure. Consider for instance a Closed-Open model for an ion channel. I can easily show this model is too simple for some channels, and a Close-Open-Inactive model is better. i.e. I am more certain in a more complex structure with more parameters. As we continue to add states, your statement is true, but there is a 'happy medium' we probably both agree the community should turn our attention to identifying for this application. I think this introduction risks over-simplifying the subtleties of model construction and selection.
Experimental design: Whilst the Crumb dataset does cover 7 ion channels, it does not feature significant activity at many of them, and is actually not dissimilar to considering only 2-3 ion channels. I wouldn’t strongly make a statement in any study based on that dataset that the information on the extra ion channels is interpreted better by a given model over another.

If a strong IK1 blocker, or Ito blocker was encountered I would still have more confidence in say a classifier based on Ten Tusscher 2006 APD predictions than a classical black box classifier. Where Bnet falls in this I am not entirely sure, but I would not be as confident as the author appears to be that it would perform as well. Perhaps some more limitations in terms of the ‘regimes’ that have been tested would be useful (Figure 2 goes some way to looking at this, but it is really an N-D dataset and is difficult to see how similar these datasets really are, or how much of the possible-block space they cover).
Validity of the findings: There is something of a problem with using Credible Meds for this study. PR is defined (on the credible meds website) as: "Possible Risk of TdP - These drugs can cause QT prolongation BUT currently lack evidence for a risk of TdP when taken as recommended". Note that this means compounds classified as PR could be QT prolongers that are NOT pro-TdeP, raising concerns about the dataset we are using for testing here. Such compounds do exist and are a major reason for the recent efforts to address TdeP risk. In taking Credible Meds as a ‘gold standard’ there is a danger of testing all these measures for QT prolongation rather than pro-arrhythmic risk. In terms of how this might change the findings, it is conceivable that the subtle transition to pro-arrhythmic behaviour may be captured better by more biophyscially-detailed models, or maybe vice-versa, but this article is tackling a slightly different question to the one that CiPA (www.cipaproject.org) is aiming to address.

Unfortunately I don't have a better suggestion at present, other than perhaps using the CiPA compound list where this distinction between QT and pro-arrhythmia was carefully considered and motivates the compound choice to some extent. But I acknowledge it is far more limited in number of compounds. It may be best just to expand the discussion of this testing set and acknowledge this explicitly as a limitation.
Additional comments: This is an interesting article and I believe the author is right to make the point that the use of biophysically detailed models in drug safety testing should be justified. The use of simple(r) models should set a benchmark that biophysically detailed models should have to beat to be widely adopted. I have written a blog on this myself, and agree with the main sentiment of the article: https://mirams.wordpress.com/2017/03/27/risk-regression-or-biophysics/

That said, in the article Discussion, I think it is worth stressing a few points in favour of biophysical models, that the author may wish to include in the discussion:
1.	Bnet itself is really a simple biophysical model – by relying on Hill curves and a knowledge of electrophysiology it could be called biophysical.
2.	In some sense Bnet is selected as it gives a good answer here, whilst the other models are operating a validation study. Whilst it is pleasingly simple and there is not much room for tweaking, the Bnet model structure itself was selected and is different to previous simple models the author has proposed. So there is an element of showing us the model that happened to work (which I will admit some simulation studies have also been doing recently), I don't think this is a massive issue as the Bnet model has no parameters, only structure, to tweak.
3.	Many of the currents were discovered with the aid of the biophysical models (not that that means we should necessarily use them in this context, but the readers should be aware of it).
4.	Chronologically, the big jump in predictive power - from hERG-only to multichannel block was actually performed because of the biophysically detailed models (including Ten Tusscher 2006 - labelled here as 'cardiac safety simulator'). The fact the models existed led us to try this, the multi-ion channel data had been available for some time before Mirams et al. 2011 proposed its use for improving TdP predictions because models suggested that combination of data would be useful!

3 and 4 aren’t necessarily a defence of keeping to using more detailed models for safety prediction if simpler models are shown to be as predictive, but they do strongly suggest that biophysically-based models may perform dimension reduction to a single 1D risk marker to deal better with ‘edge cases’ (combinations of ion channel block that have not been seen in training data for a simple classifier) than simpler models. Whether Bnet can also do this remains to be seen I would say.

I think the author should probably discuss and cite some of the whole-heart simulation studies that have been proposed for this purpose, as they are even further down the other end of the spectrum from the ones that he focusses attention on here.

I have made some more minor comments in direct annotations to 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: COMPLEX VERSUS SIMPLE MODELS: ION-CHANNEL CARDIAC TOXICITY PREDICTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The author addressed all my comments
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: SEA CUCUMBERS REDUCE CHROMOPHORIC DISSOLVED ORGANIC MATTER IN AQUACULTURE TANKS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This manuscript is excellent, and is the first time I have no recommendations for improvement. The authors executed a straightforward study, comprising a lengthy time series analysis of cnidarian aquaculture tanks, one with and one without holothurians (sea cucumbers) and measured with high frequency cDOM (various metrics, all of which told complementary pieces of the same story of removal of HMW DOM by the holothurians. They then properly designed and executed three replicate experiments to test causality, and found corroborating results. There is no effort to overextrapolate the findings, which is appreciated, but the results are strong and have clear implications for aquaculture management and the ecology of coastal benthic ecosystems.

A few minor grammatical corrections:
L31: “the former being”
L104 “species”
L187-88: Unless otherwise specified model effects (such as repeated experiments as a random factor, etc.), this was probably a t-test done on each experiment?


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: SEA CUCUMBERS REDUCE CHROMOPHORIC DISSOLVED ORGANIC MATTER IN AQUACULTURE TANKS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The main line of this article is clear, and the English is OK. The article structure, figs, tables are good.

However, there are some deficiency in the part of reference:
•	The formats of the references are not uniform. Some years are enclosed in brackets, while others are not.
Experimental design: The research of this paper is within the aims and scope of this journal.
The comments that need improving are as follows:

•	The equation (2) has some edit error

•	Line 171-173. The basis for setting up the number of experimental groups should be explained.

•	Line 195-202. The contents of these lines mainly refer to the method of CDOM absorption, and should be transferred to the section “Material and Methods”.
Validity of the findings: •	The conclusion of this paper (Line 93-96) seems disobey the common sense and need to be revised. An excessively low water transparency of the aquaculture water is not always good for the aquaculture. It will reduce the photosynthesis of algae. Thus, they will not only produce oxygen but also consume oxygen. In the long run, they will cause ammonia nitrogen, nitrite, hydrogen sulfide and other harmful substances accumulation, resulting in deterioration of water quality. In fact, only if the water transparency was in a reasonable range, the marine products would have a good growth and reproduction. Therefore, the author should supply the data of the water transparency (not just the absorption capacity of dissolved organic matter) to support this conculsion.

•	Line 238-241. These contents are lack of sufficient discussion. There is no enough word to explain the reason and mechanism of the holothurians effecting on the molecular weight of DOM in auqaculture water.

•	Line 264-267. These sentences are too subjective and need to be further discussed.
Additional comments: In this paper, the author employed sea cucumbers to reduce chromophoric dissolved organic matter in aquaculture tanks. This paper is clear and interesting. However, the paper is lack of deep discussion on the mechanism of sea cucubers reducing CDOM. Thus, this paper is needed to be further modified.


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: SEA CUCUMBERS REDUCE CHROMOPHORIC DISSOLVED ORGANIC MATTER IN AQUACULTURE TANKS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript describes an interesting observation: that holothurians appear to reduce the CDOM in sea anemone aquacultural effluent. The observations are made biweekly in large tanks over a year and in small tanks in triplicate over 3 days. The results appear to be clear, and the statistical analyses support the conclusion that holothurians do, in fact, have an effect on the transparency of the water. As such, I think this manuscript deserves publication.

There are a number of questions that arise in this new area of research. It would be good for the authors to consider these questions in this paper if possible:

1) It appears that the process of growing A. sulcata in aquacultural tanks produces CDOM. However, the actual source of this CDOM is unknown. Does it come from the feeding of chopped fish? There was no feeding and no increase over initial conditions in the -Holo short term experiments.

2)  There are variations in the large tanks over time.  What are the possible sources of variability for the influent in the large tanks? Sampling every two weeks does not resolve tidal, diurnal, or temperature effects or many other possible sources of variablility. Is the influent possibly impacted by nearby river flow? Blooms? Changes in coastal current? Is the influent treated, filtered, or settled? Understanding the variability of the influent can help attribute variability of the effluents.

3) For that matter, in the 3 short term experiments, the initial conditions varied quite a bit. Why was the identical influent (starting water) not used?

4) There is an apparent correlation between CDOM and POM in the large tanks. But, I don't see any reduction in POM concentrations in the +Holo compared to the -Holo conditions. There is a stated assumption that Holos reduce POM, and therefore CDOM production…but I do not see the POM reduction. Can this experiment be done or statistics be shown?

5) There is a conclusion that Holos can reduce CDOM in open pens. However, there is no analysis (even back-of-the-envelope calculations) that suggests that Holos can filter a significant amount of water or take up a siginificant amount of POM or CDOM compared to the relevant exchange volumes. Estimates of these parameters would make the potential application more believable than just a trend in a small batch experiment.

Here are some specific questions:

6) TOC is measured and available in the S1-5 tables. However, it is not mentioned in the results or conclusions. It is an important parameter for effluent (maybe more important than CDOM). Is there an effect on TOC by +Holo? If so, state it. If not, this is interesting…as CDOM/TOC ratio is also a measure of CDOM quality.

7)  Line 93-04: …presence of holothurians reduced significantly water transparency…" I think you mean increased water transparency….

8) Oveall there are several/many instances that thorough proofreading and editing for English grammar and style are necessary.
Experimental design: 9) What is residence time of water in tank? I can calculate, but better if you provide (41 hours)

10) Does food (chopped fish) introduce CDOM to the tank? This would be a simple leaching experiment.

11) Was plastic beaker (plastics are known to sometimes leach CDOM) tested to show that they did not leach CDOM?
Validity of the findings: Results
12) It appears that sea anemones increase the CDOM, and the holo decrease back to influent concentrations. The quality does seem to change a bit (Figure 2) with Holos reducing S275-325.

13) A. sulcata effluent under normal aquaculture condistion is how much volume annually? Compared to coastal exchange? Is it reasonable to think that these tanks may affect coastal water CDOM at maximum aquacultural rates? The authors state this as a possible application of Holos in aquaculture. Some estimates would help make that case.

14) What is the capacity for holothurians to filter water? Can the abundance of these filter the entire large tank before it is replaced by new influent (40 hours?).  This will help in interpretation of the impact of Holos.

15) It would be interesting to examine a mass balance for organic carbon in the tanks (small or large).  How much mass might go in as food, come out as DOM, be extracted by Holos, etc. Again, this would help in interpreting the data.

16) The authors state that CDOM probes are easy to use to monitor open ocean aquacultural pens. Why did they not use CDOM probes to monitor effluent?. They are suggested for future applications. This might have been helpful to examine variability.

17) Biweekly is not very high resolution. When effluent is higher than influent or vice versa, why? Is there something in the data that might explain this (just after feeding, high temp spike, bloom in influent waters? Etc.

18) Figure 4.  More CDOM with more POM. The caption says that no regression line is showen when not significant. However, the data in a (bacteria) and b (POM) do not look that different. Could regression lines with R2 be shown to let the reader decide what is significant?

19) Figure 5. What were differences in conditions of the 3 experiments? Same influent water? Different times? Different animal sources?
Additional comments: Summary
I am still wanting a better mechanistic understanding of the impact of Holos on CDOM. Where does the CDOM come from? How do Holos extract the large MW DOM? How much can the extract? There are all important questions, but maybe it is enough for this first paper to just get the observation out so others can follow up and explore.


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: DEFICIENT MISMATCH REPAIR AND RAS MUTATION IN COLORECTAL CARCINOMA PATIENTS: A RETROSPECTIVE STUDY IN EASTERN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study 'Deficient mismatch repair and RAS mutation in colorectal carcinoma patient: a retrospective study in Eastern China', the authors Zhang et al. conducted a well-designed clinical study basing on 813 Chinese patients with colorectal carcionma, and investigated the correlations between the clinicopathological characteristics and surival of patients with their dMMR status or RAS mutations.  The overall design of the study is well-laid out, with clear background information given in the introduction part. The discussion part is very nicely written, which sumarized a range of related and updated studies in China and western countries in this field. Moreover, the authors commented on the limitation of their studies, which does help improve the integrity of the whole paper.

The English language is generally well-used, however there are several places in the text where the language/grammer should be improved, for example lines 48, 112, 146, 155-156, 229, 232, 297, 311. In addition, abbreviation should be spelled out at its first appreance. In line 179, the full name of pMMR should be indicated.
Experimental design: The research question in the study is well defined, the authors also nicely stated the knowledge gap this study will fill in. The experiments used are appropriate, however, there are several issues need to be further addressed to support the authors' conclusion.

1. The authors replied on IHC to determine the presence/deficiency of the different MMR proteins. However, there is no definition as of how the authors determine what level of staining indicates protein expression deficiency. The authors should show/describe their standard of definition, positive and negative controls, and show representative IHC images of patients with either pMMR or dMMR.

2. As the authors stated in the discussion, the RAS mutations they detected rely on a kit produced in China. The mutations that could be picked up by this kit could be different from those reported in studies based on western populations. The authors should, therefore, list the mutations that are detected by this method, in order to improve reproductivity of the study and information sharing in this field.
Validity of the findings: The authors did a great job in performing statistical analysis, the conclusions are generally supported by robust data.  However, as the authors discussed, the small sample size in some studies (i.e. survival analysis) may lead to insignificant results. The authors should include power analysis at the beginning of these comparisons, to test how many subjects are needed to detect a statistically significant difference, and if their sample size has reached this power. This will help further determine the validity of the study/results.

One minor point is that in the statistical analysis section, the authors should add a description as of how they correct type I and II errors to adjust their results.
Additional comments: Nice study with important implication for finding biomarkers for colorectal cancer patients in China.  There are certain points that could be further improved to enhance the validity of the results and the flow of the 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: DEFICIENT MISMATCH REPAIR AND RAS MUTATION IN COLORECTAL CARCINOMA PATIENTS: A RETROSPECTIVE STUDY IN EASTERN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript “Deficient mismatch repair and RAS mutation in colorectal carcinoma patients: a retrospective study in Eastern China” By Zhang st al investigated the frequency of KRAS mutation and deficient MMR in colorectal cancer patients which report the frequency of 45.88% and 15.43%, respectively. In addition, dMMR and KRAS mt did not appear as prognostic factors in this population.
Overall, this is a clear and concise manuscript. The introduction is relevant and theory based. The strength of this study is a relatively large sample size (N=813) to detect the mutation frequencies. The methods are generally appropriate. However, there are several papers which reported the frequency of RAS and dMMR in Chinese population and little data is added from this manuscript. Moreover, the definition of dMMR should be revised to the standard criteria.  Finally, this manuscript has several grammatical errors and needs to be improved before publishing.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Major:
Material and Methods
1.  You excluded the patients who received preoperative EGFR-targeted therapy (which mean RAS wt patients) that lead to selection bias in this cohort. So, the prevalence of the KRAS gene mutation in your study might be higher than normal.
2. Please explain the reason why you did not include all of the patients that had tissue available for mutation testing in that period?
3. Please explain the reason why you had the survival data in only 15.6% (114/729) in the early stage of the disease?
4. Also, Might be better if you demonstrate the patient selection method in consort diagram.
5. Line 116-117, “Loss of expression of any MMR protein was regards as dMMR”.
 Actually you have to use the standard criteria for diagnosis of dMMR (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4583524/ ) which are
	dMMR in MLH1: loss of expression in MLH1 and PMS2
	dMMR in MSH2: loss of expression in MSH2 and MSH6
	dMMR in MSH6: loss of expression in MSH6
	dMMR in PMS2: loss of expression in PMS2

From your definition, if the IHC result show loss of expression in MLH1, you will interpret as dMMR which is incorrect.

Result
1.	You should categorize the patients into 4 groups according to the standard definition for dMMR. From  Table 2, there is a huge confuse? difference in the number. For example, female gender had dMMR in 50 cases. However, when you define in MLH-1/PMS2=42 cases and MSH2/MSH6=12, total of 53 cases.
Discussion
1.	Line 207: the MMR deficiency rate should be changed with the standard definition

Minor:

1.      Should use the term of “right/left sided colon rather than right/left colon” in all parts of the manuscript
2. Line 55: favorable prognosis and could not benefit of adjuvant 5FU based chemotherapy in which stage of the disease? You should specific only in early stage.
    Line 65: not only KRAS gene but the NCCN recommend both KRAS and NRAS gene mutation
    Line 166: RAS status was "tested" from 813 patients…… not "detected"
    Line 172: should be 46.6% vs 34.98%, P=0.001
    Line 220: specific the association i.e female gender, right sided tumor… etc


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

Input:
Title: RELATIVE EVOLUTIONARY RATE INFERENCE IN HYPHY WITH LEISR
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript introduces a useful extension to HyPhy to infer relative evolutionary rates of protein and nucleotide data. This work is clearly written, provides sufficient background material, contains well-organized figures, and is nicely self-contained. I have only minor discretionary comments which I have included in the “General comments for the author” section. I feel this work is ready for publication, though I would appreciate if the authors would consider my suggestions before submitting a final version.
Experimental design: The experiments designed to test their implementation are well described. I appreciate that the authors made their code available on github, and I feel this enhances the transparency of the work.
Validity of the findings: These findings appear to be robust, and the conclusions are well stated.
Additional comments: Line 28: Is HyPhy really “the leading molecular evolution inference platform”? It may be, but this seems like a pretty bold statement considering that you don’t give a reference. Consider changing the sentence to “a leading molecular evolution inference platform”.

Line 31: This sentence makes it seem like LEISR can only be used on non-coding data.

Line 33: Change to “In addition, LEISR is MPI-enabled”

Line 50: I am not suggesting you implement this in the current version, but in future versions, it would be nice if the normalized estimates were reported as well.

Line 59: The first sentence of this paragraph is very long and hard to unpack. Consider breaking it into two sentences

Line 74: A 100 sites seems pretty small. I get that it was probably chosen to keep the run-time of simulations and rate inferences short and I have no qualms with using shorter sequences. However, adding a sentence that points out that the validity of this analysis is not dependent on protein size may help to strengthen the manuscript.

Line 81: The word “during” is repeated

Line 89: It's confusing that this paragraph starts out talking about Figure 1, then switches to Figure 2, and then goes back to talking about Figure 1. Consider moving the discussion that starts on line 94 to after the sentence that ends on line 90, so that Figure 1 is discussed then Figure 2 is discussed.

Line 90: I assume the data shown in Figure 2 is the raw data and not normalized, but maybe it should be stated.

You claim that LEISR can use nucleotide data beyond the capacity of Rate4Site, but all of the analysis appears to be done on proteins. Is Rate4Site’s ability to deal with nucleotide data so poor that a comparison between Rate4Site and LEISR cannot be done? Would inference using nucleotide data be expected to work as well as analysis of protein data?  Consider sneaking a sentence in somewhere that addresses if any differences are expected when analyzing nucleotide data.


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: RELATIVE EVOLUTIONARY RATE INFERENCE IN HYPHY WITH LEISR
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is clearly written and the background is adequate. The authors provide clear links to the actual analysis code on GitHub used for this paper.

At the beginning of paragraph 2, the authors refer to `HyPhy` as "the leading molecular evolution inference platform." There are also other widely used packages, so it might be better to change "the leading" to "a leading."
Experimental design: The design is clear and well described with a few exceptions:

1. In Approach, the authors never clearly state if LEISR estimates the tree topology or not. My impression is that it does not. If this is so, it should be made clear that the tree is provided along with the alignment.

2. For the test simulations, the authors never explain the topology / branch lengths of the tree. This seems likely to strongly affect the results in the figures (presumably the results are much better with trees with long independent branches). So some information should be given about the tree used.

3. In the introduction they note that `Rate4Site` does not handle *large alignment* or *short sequences* particularly well. It is implied that `LEISR` address both of these issues but no evidence is presented to backup this claim. This could be addressed by simply giving a table of the respective runtimes of the programs, and providing an examples where `LEISR` converges well and `Rate4Site` does not.

4. Although not obligatory, it might be nice if Figure 2 also compared the inferred rates to the *true* values used for the simulation. In the sense that this paper just describes a re-implementation of Rate4Site, this is not required. However, it could be useful to have some sense of how accurate the methods are as well.

5. It would be nice to compare `Rate4Site` and `LEISR` on an empirical data to show that they give similar results on real as well as simulated data.
Validity of the findings: The findings are clearly supported except for the missing data about the superior performance of `LEISR` on large datasets mentioned above.
Additional comments: 1. The paper takes a bit of time to explain why you should normalize by the median, not the mean, but in the results they normalize by the mean. Why not normalize by the median?


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: COMPLETE MITOCHONDRIAL GENOME SEQUENCE OF THE “COPPER MOSS” MIELICHHOFERIA ELONGATA REVEALS INDEPENDENT NAD7 GENE FUNCTIONALITY LOSS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study “Complete mitochondrial genome sequence of the “copper moss” Mielichhoferia elongata reveals independent nad7 gene functionality loss” presents the complete sequence of the mitochondrial genome of the copper moss Mielichhoferia elongata. The results show that the structure of M. elongata mitochondrial genome is pretty similar to that of other moss species, which is in agreement with the fact that the mitochondrial genome of mosses and liverworts evolves at much lower rates than that of flowering plants. Also, the authors characterized a set of SSR loci that could be further used in population genetic and phylogenetic studies. In general, the study presents very valuable results that will help with the phylogenetic reconstruction of the Bryophyte clade (sometimes complicated as demonstrated by the location of the genus Mielichhoferia in different families according to the available literature) among other things. However, the manuscript needs to be revised in depth prior to publication as some major and minor concerns need to be addressed. My major concerns are related to the presentation of the scope of the work and the lack of some relevant information in the materials and methods section.
Experimental design: The scope of the study is not clearly presented. I assumed that lines 58-63 are trying to express the main aim of the work as you can read “So, mitochondrial genome (MG) of Mielichhoferia will be useful both for an understanding of some aspects of heavy metals tolerance mechanism and to find out appropriate taxonomical treatment of the taxa. Besides, mitogenome of M. elongata will facilitate taxonomy and population studies within Mielichhoferia that is important due to the disruptive character of the area, rarity, and habitats damage”. However, first of all, I think that the scope of the study should be expressed more clearly with some statement such as, “the aim of this study is to…”.
Secondly, one of the goals would be “… understanding of some aspects of heavy metals tolerance mechanism…”. I wonder whether there is any evidence (in any species) that points towards the existence of heavy metal tolerance-related genes (or regulatory elements) in plant mitochondrial genomes, if that’s what authors meant with their statement. In case of existing, they should use that information to justify their expectations of understanding heavy metal tolerance mechanisms from mitochondrial genome sequencing. Besides, the only reference made to this issue throughout the rest of the manuscript is in lines 181-182 where the authors point out that “Sequencing did not reveal any special features that can be attributed to high heavy metal tolerance of this moss”. The lack of discussion about this topic makes me think whether “understanding of some aspects of heavy metals tolerance mechanism” should be regarded as one of the aims of this study.
Finally, another goal was “to find out appropriate taxonomical treatment of the taxa”, however, in the discussion section (Lines 210-212) the authors point out that “The absence of MG sequence of Mniaceae and Bryaceae representatives make it impossible to clarify taxonomic position of Mielichhoferia”. If it is impossible to clarify the taxonomic position of Mielichhoferia due to the lack of MG sequences of relevant families, then finding out the appropriate taxonomical treatment of this species should not be one of the aims of the study.
For all these reasons I suggest the authors to revise and rewrite this last part of the introduction in a way that is more related to their results.

“Sample collection and DNA isolation” section: the authors do not provide any explanation about sample storage and preparation before DNA extraction. I think that this is crucial information that cannot be obviated in order to ensure the reproducibility of the experiment and also to assess the comparability of their results with other studies. Which part of the moss did the authors collect for DNA extraction (just tips, whole shoot, etc.)? Was the material cleaned somehow before storage? How was the material stored until DNA extraction (frozen in liquid N/dry ice, dried, etc.)? How much tissue did authors use for DNA extraction? Also, did authors use the DNA extraction kit following the manufacturers’ protocol or did they perform any modification on it? Did they assess the concentration and quality of the DNA? If so, how? The section needs to be completed with all this information.
Validity of the findings: As I stated in the previous section I think that the scope is not well defined and therefore the importance of the findings presented in this work is undermined.

Giving a deep thought to the introduction section and justifying better the importance of the results presented will increase the interest of the reader.

Finally, nad7 pseudogenization is an important feature of the mitochondrial genome of M. elongata, but, as a reader, I’d appreciate some information about its function and how its loss would affect these species that lack a functional nad7.
Additional comments: In general, each paragraph consists of one or two sentences making a total of 2-5 lines per paragraph. This makes the manuscript harder to read. Authors should make an effort gathering small paragraphs referring to the same topic/issue into the same paragraph; e.g. lines 36-49, 50-57, 196-208 could constitute just one paragraph each.

Minor concerns:
1) Abstract: acronyms such as SSR and CDS need to be fully written to ensure the clarity of the summary.
2) Keywords: where it says “Mielichhoferia elongate” it should say “Mielichhoferia elongata”.
3) Line 36: the sentence “Several mosses and hepatics species restricted to substrates enriched with heavy metals” lacks the verb between species and restricted.
4) Line 40: the first time (apart from the abstract section) you use the name of the species this has to be complete: Mielichhoferia elongata. Also, the complete name of M. elongata is not “M. elongata Homsch”, but “Mielichhoferia elongata (Hope & Hornsch) Nees & Hornsch.” According to Tropicos database (www.tropicos.org).
5) Line 50: the authors state that “There are 23 accepted species names of Mielichhoferia Hoppe & Hornsch in the Plant List” but, what does this mean? That there are 23 species under this genus? If that is the point, that is not true because both “The Plant List” and “Tropicos” provide a greater number of species within this genus. If not, please clarify what do you mean in the previous statement.
6) Line 75: what is MHA? Acronyms should be fully written the first time that they are used in the text.
7) Line 108: is there any specific reason why authors chose the MG of Bartramia pomiformis as a reference to annotate M. elongata MG? If so, this should be specified in the text.
8) Line 118: use a dot instead of a comma after M. elongata to shorten the extremely long sentence.
9) Line 136: the authors state that “MG of M. elongata contains 66 genes including genes for 3 rRNAs (rrn18, rrn26, and rrn5), 24 tRNAs, and 40 conserved mitochondrial proteins”, however this would make a total of 67 genes. Taking a look at Table 1 I count 39 protein coding genes, 27 RNA genes which would make a total of 66. Also, I don’t understand why the authors point out that there are 112 genes and one pseudogene in the caption of Table 1, is this a mistake?
10) Figure 2: the figure should be auto explicative so authors should mention in the caption (or legend) that the black filled sections in this figure indicate non-existing exons (or parts of them) in these species.
11) Lines 164-166: is there any reference that supports the criteria for SSR loci identification? If so, this should be added. If not, was this selection based on the criteria regularly used in the literature?
12) Figure 3: this figure needs to be improved. First of all, there is no y-axis label (frequency of SSR classes?) and the line of the x-axis is absent (at least in the PDF version).
13) Line 174: it should be 24,827 instead of 24827.
14) Caption Figure 4: CDS needs to be fully written in order to make the figure auto explicative.
15) Line 184: the sentence “MG size significantly varies even among closely related flowering plants (Allen et al., 2007; Alverson et al. 2010; Cho et al., 184 2004; Sloan et al., 2010; 2012), but extremely stable in bryophytes (Liu, Medina & Goffinet 2014)” needs a verb after but (…but it is extremely…).
16) Line 190: I assume ORF means open reading frame, but this should be specified on the text.
17) Line 213: the authors say that “Phylogenetic tree from 31 mitochondrial CDSes of 40 mosses species” but the tree was built with CDS from 39 moss species and 1 liverwort. This needs to be corrected in the manuscript.
18) Line 228: remove contraction “doesn’t”.
19) References: The reference Sloan et al., 2008 is not cited in the manuscript (in the manuscript I could only find Sloan et al., 2010, 2012).


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: COMPLETE MITOCHONDRIAL GENOME SEQUENCE OF THE “COPPER MOSS” MIELICHHOFERIA ELONGATA REVEALS INDEPENDENT NAD7 GENE FUNCTIONALITY LOSS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1.	The writing and organization of the introduction section need to be improved, the present version was composed of many sentences rather than well-organized paragraphs. The authors may provide information regarding to the life style/cycle of mosses, the general features and the current research progress in the mitochondrial genome of mosses, and how they differ from other land plant lineages (liverworts, hornworts and vascular plants).
2.	There are many grammatical errors throughout the manuscript, e.g. line 23, lines 90-91, line 93, line 97, line 119. The authors may use some language editing services to polish this manuscript.
3.	Line 96, line 98, line 100, line 102 and line 105 the parameters of these programs used in this study need to be provided.
4.	Line 116, since there are 40 conserved mitochondrial protein-coding genes in mosses, why only 31 of them were used for the phylogenomic analysis? The authors need to justify the selection criteria.
5.	Line 22, lines 137-141 and table 1 heading, the numbers were not adding up correctly.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Goruynov et al. sequenced and assembled the mitochondrial genome of the moss Mielichhoferia elongata. This mitochondrial genome was highly conserved in gene content, genome size and structure except a functional loss of the nad7 gene. Detailed exon structure comparison and phylogenetic analysis show the pseudolization of nad7 in M. elongata was different and independent of that in the two other mosses Buxbaumia aphylla and Tetraphis pellucida. Overall this study is mainly descriptive.


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: COMPLETE MITOCHONDRIAL GENOME SEQUENCE OF THE “COPPER MOSS” MIELICHHOFERIA ELONGATA REVEALS INDEPENDENT NAD7 GENE FUNCTIONALITY LOSS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The writing of the manuscript has been improved, I only have some minor comments below:

1. Line 87, typo？ “2 mkg DNA”.
2. Line 163, spelling error, “M. elongate” should be “M. elongata”.
3. Line 120-122, only 23 out of the 31 protein-coding genes were listed. And since nad7 is a pseudo-gene in some mosses, why it was used for the phylogenetic analysis?
4. Fig. 1 looks messy, I suggest the authors take a look at some mitochondrial genome maps in other publications.
5.Table 1 heading, typo,  “60 genes”.


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: MOLECULAR SYSTEMATICS OF THE SUBFAMILY LIMENITIDINAE (LEPIDOPTERA: NYMPHALIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an excellent study on the molecular systematics of the subfamily Limenitidinae, which is clearly of top standard, even using a large number of nuclear genes never used before in phylogenetic studies of butterflies.

The article is generally written in excellent English, with only a few minor mistakes, which are listed at the bottom.

Extensive background information on the taxonomy of the subfamily is provided including comprehensive referencing.

The article structure is professional and the tables and figures contain all important information in a readable way.

Raw data are shared, but the GenBank accession numbers for new sequences are still missing and need to be added before publication, both in the text (e.g. lines 274-277, 316-320, 383-385) as well as in the supplementary file.

Minor language issues:

line 21: "was" should read "were"
line 68: "Gruppe" means "group" in German and is not necessarily equivalent with a tribe. I suggest to place the group names in quotation marks: ... in three tribes ("Neptis-Gruppe", "Limenitis-Gruppe", and "Euthalia-Gruppe") based on ...
line 172: delete the word "and"
line 301: delete the word "the" before "Asia"
line 387: Change: "Here, the study" to "This study", and change "till date" into "to date"
line 388: change "Based on up to 18 genes regions" to "Based on regions of up to 18 genes"
line 389: add "clade" after "monophyletic"; change "and comprised" to "which comprises"
lines 394-396: revise sentence, e.g.: "At the genus level, our results showed some of the traditionally
recognized genera as either polyphyletic (Neptis and Euryphura) or paraphyletic (Pantoporia, Athyma,
Parasarpa, Limenitis, Adelpha)."
line 397: delete "of the para/polyphyletic nature of the"
Experimental design: The article contains original research and fills an important knowledge gap. Methods are sound, described with sufficient detail and are of very high standard.
Validity of the findings: Robustness of results is checked and taken into account for their interpretation. Conclusions are only drawn for significant findings supported by the results.
Additional comments: No additional comments


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

Input:
Title: MOLECULAR SYSTEMATICS OF THE SUBFAMILY LIMENITIDINAE (LEPIDOPTERA: NYMPHALIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article appears to be well-written, clearly articulated, and well-presented.
Experimental design: The primary limitation of this study is the patchiness of the available data for each species.  However, given the taxonomic breadth of the species sampled, and the heavy and necessary reliance upon previously published molecular data, this is unavoidable.  Overall, the authors have done an excellent job tackling an unusually difficult taxonomic quandary.
Validity of the findings: Suggestions for improvement.  #1) Include a verbal discussion of missing data in the methods and results section.  #2) Include a supplemental tree figure that includes only core taxa for which data is available for all gene regions.  Such a tree, if possible, would strengthen the confidence that the topological uncertain (especially among the Limenitidini) arises as a consequence of rapid divergence among these genera vs. a lack of phylogenetic resolution due to missing data.
Additional comments: This phylogenetic investigation of the subfamily Limenitidinae is long overdue.  The authors did an excellent job of describing both the previous history of taxonomic confusion related to this group but also placing their new results in a clear and well argued framework.  Although additional work will need to be done in the future to fully resolve the generic relationships among the Limenitidini, the current study represent a vast improvement of our understanding of the phylogenetic history of this diverse and complex butterfly lineage.


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 250 PLASTOME PHYLOGENY OF THE GRASS FAMILY (POACEAE): TOPOLOGICAL SUPPORT UNDER DIFFERENT DATA PARTITIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is clear and well written, but too long, especially the Discussion section. The aims of the paper are clear but maybe too general. Perhaps the authors could indicate what specific topological problems in the grasses they hope to resolve with this new analysis. This I think could help better focus the discussion, especially considering that most topological relationships recovered are totally or partially consistent with previous results from other publications (very often authored by researchers also included in this study).

Sufficient field context is provided, and the literature review is very complete, but perhaps too exhaustive (please see general comments). The article is well structured and figures and tables are very good. Supplemental files are informative and in line with PeerJ shared information policy. Results are relevant and in line with the established aims.

There are no clear hypotheses in the paper. This is understandable given the nature and the aims of the study, but perhaps (as said above) the authors could indicate what major topological problems they want to solve. They could also indicate what differential behavior they expect from databases including or excluding gaps, sites under positive selection, etc (please see general comments)
Experimental design: The paper is clearly within the aims and scope of the journal. The methods are rigorous and they are described clearly and with sufficient detail. Research questions could perhaps be better defined (please see general comments and the basic reporting section). Results are relevant and mostly consistent with previous research.
Validity of the findings: Nothing to say here. Suggestions on original research questions are included in general comments
Additional comments: Comments on general research questions and hypotheses.
The phylogenetic relationships obtained by the authors are relevant and interesting, and their results show increased support for a lot of relationships that heretofore were poorly resolved. In phylogenetic analyses such as this it is often difficult to establish clear research questions (or starting hypotheses). However, perhaps the authors could consider indicating what poorly or ambiguously supported relationships in the grass phylogeny they aim at resolving. Once they have established that, perhaps it would be convenient to focus the discussion on those nodes in particular.
The sections of the article that deal with the effect of positively selected or gapped sites in the topology and resolution of the trees are also interesting. However, again the research question on this topic is not clearly stated. What did the authors expect to obtain? They made a big effort analysing different partitions, so surely they had some expectations about the results. At least as regards gapped sites they certainly had prior information on the effect of these sites (treated as missing data) on Maximum Likelihood (ML) analyses (they add several very relevant references on the issue). Considering this latter aspect, it is not clear to me why they included gapped sites (as missing data) in their analyses with ML if there is such strong evidence against it. Were they trying to confirm it? If so, this should be included as an aim of the paper. In any case, in my view more information should be added on why they included gapped sites.

Materials and methods.
The methodology of the paper is clear and sound. Some things however could perhaps be further clarified. The authors only used ML analyses, and do not perform Maximum Parsimony (MP) or Bayesian Inference (BI). The authors indicate that “We conducted only maximum likelihood (ML) analyses, given the large size of our datasets, in terms of both numbers of taxa and nucleotides” (lines 215-216). It is not clear to me why the other methods were excluded by the size of the matrices. Actually, several of the articles they cite that deal with plastome phylogenies use BI or MP methods (e.g. Burke et al., 2014. American Journal of Botany 101: 886-891). It could even be interesting to know if some of the nodes that receive differential support in the different matrices used by the authors are also ambiguous using other phylogenetic inference methods.
The authors include a lot of partitions in the analyses, which are very complete. Did they consider using best-fit partitioning schemes and models such as the ones implemented in partitionfinder v.1.1.1 (Lanfear et al. 2012. Molecular Biology and Evolution 29: 1695-1701)? (it is just a suggestion, the number of partitions tried is quite high).
As regards the methods used to build the libraries for NGS, both Nextera and Nextera XT are used. According to the methods section (the authors refer the reader to Burke et al., 2016b), plastids were not extracted prior to the building of the libraries in any of the samples, so why using Nextera in some samples and Nextera XT in others? Did the authors consider the genome size of the different grasses? Perhaps the authors could give and explanation for this in the paper (although both methods are valid).
Finally regarding methodology, a reference should be added to acknowledge the authorship of the MEME model beyond the HyPhy software (Murrell et al., 2012. PLOS Genetics 8: e1002764).

Results and discussion.
The results of the paper are clearly described. The discussion is also relevant and interesting, but I think some changes should be made to make it easier to follow. Some of the changes have to do with the inclusion of clearer research questions (see above). Perhaps the number of references that the authors include to support some of the phylogenetic relationships that are more clearly supported in the literature is a bit overwhelming. In my view, the authors should select the most relevant ones.
The discussion has two very clearly separated parts, one analyses the support of the different clades in the different partitions in a general fashion and the other focuses on the phylogeny of the different groups. However, the discussion becomes a bit repetitive in some parts (e.g. lines 1052-1129) where the authors re-discuss the effect of gapped and positively selected sites on topologies (this time focused on one particular node or group of nodes). Perhaps the discussion could be re-organised to avoid this (and to reduce its extension). Also in the discussion there is a part (“Rooting the grass phylogenetic tree”) that could, in my view, be eliminated. It is interesting, but it does not actually discuss the results of the authors, they use this section to justify a decision they made in the materials and methods section (rooting the tree with the Anomochlooideae instead of with the Joinvilleaceae). This chapter could be moved (much reduced) to the Materials and Methods.
Tables, figures and supplemental files are relevant and interesting. I have just a couple of comments here. First, regarding Table 2, I think there are problems with the numbers of positions used in the table. For instances (if I did it correctly), matrix Z, including coding and non-coding regions (and excluding gapped sites and positively selected sites) includes 71140 bp. Matrices H and R, including coding and non-coding regions (but not gapped or positively selected sites) have 44975 and 26307 bp, respectively (overall 71282). If I understood the method correctly, there are 142 bp missing in matrix Z (maybe I made a mistake with the numbers, if so I apologize to the authors...).

Phrasing and language edits (and other minor changes) to clarify the text:
Lines 41-42. Is it necessary to refer to these specific clades? especially considering that the results are in agreement with current classifications
Lines 73-75. The authors indicate the putative age of the fungal sclerotium, but make no reference to the ages of the phytoliths used by Prasad (2005, 2011). It is not very important, but perhaps both ages should be mentioned (or none)
Line 86. The authors write “520 tribes” instead of “52 tribes”
Line 141. Given that voucher specimens were deposited in one Herbarium only (DEK), it would be a good idea to use the complete name of the institution (at least the first time it is mentioned)
Lines 167-168. The authors indicate that “A published reference for each new plastome was obtained from a closely related grass species”. Perhaps the reference used could be added to table 1
Line 184: The authors should explain the meaning of dN and dS (it is never explained in the text)
Lines 185-186. The authors indicate that: “Each sequence was then tested for positive or purifying selection using the codon-based Z test of selection on default parameters”. A bibliographic reference on the method should be added here
Lines 180-202. Two tests of selection were conducted, but it is not clear to me why. Would it not be enough to use the second test (MEME)? Did they compare the results of both tests? This should be better explained
Line 231. “Data” should be written instead of “Datataset”
Lines 241-243. Please rephrase this third point
Lines 243-246. Please include figure numbers here
Line 291. Please write “by both” instead of “byboth”
Lines 531-534. Please simplify this sentence
Lines 674-675. “This pattern is indicative of character conflict between these data partitions that may be attributable to selection effects” A reference here would be convenient
Line 951. It should read “supported in” instead of “supportedin”
Line 958. It should read “this two genera lineage” instead of “this two genus lineage”
Line 1319. Please revise this sentence
Line 1656. Maximally?
Lines 1725-1726. Please revise this sentence
Table 2.- Caption. It should be “in each of these” instead of “in each these”
Figure 1. The caption should be extended to better explain the contents of the figure
Figure 7. Caption. Please revise “Panicoideae Pooideae”; what does “.st” mean?


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 250 PLASTOME PHYLOGENY OF THE GRASS FAMILY (POACEAE): TOPOLOGICAL SUPPORT UNDER DIFFERENT DATA PARTITIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: line 68 – what is meant by "dates of divergence"?  Stem node or crown node?

Line 75 – there are some real questions about the validity of that "fungal sclerotium" and whether the floret is from a grass.  If you choose to cite it, I would express some caution.  Also most of the dating studies that you cite did not include that particular calibration point; if included it would make the grasses even older than the Indian phytoliths do.

Line 124 and Table S1.  I assume the paper by Teisher et al. came out too recently for the plastomes to be included in this analysis, but it would be good to say that here.

Line 133 – It is good to have this identification error corrected in such a prominent way.  Hopefully it will prevent future authors from being misled.

Line 260, discussion of positive selection – I'm surprised about the high number of positively selected codons in rpoC2.  This protein includes a variable number of repeat sequences that are difficult to align (see papers by Nigel Barker) and almost certainly lead to alignment gaps in this analysis, in which case they would be largely omitted I think.  Is it possible that the evidence for positive selection comes from the alignment problems?  Likewise, aligning matK across many taxa usually requires gaps and can be difficult.  Could the positive selection be an artifact here as well?

Line 277 and following – This paragraph is hard to read and some of the sentences are hard to follow.  Can it be shortened?  As an example of the confusion, the first sentence notes 242 clades with support ≥50 in tree X.  309 clades with support ≥50 in at least one tree.  The next sentence (line 279) says "of these"…  Are "these" the 309 clades?  82 have full support in all 14 trees but only 59 have full support in the 10 plastome trees.  Is this an additional 59?  Otherwise why is the number (59) fully supported in the plastome trees less than the number in all the trees? The rest of the paragraph is similarly confusing.

Line 291 – need space between "by" and "both"

Lines 299-300 – I don't understand why there is a standard deviation reported on both the maximum and minimum values.  Shouldn't it be reported as range, mean, and standard deviation?  Same issue on line 306.

Lines 300 and 303 – The number of lines for which support increases is listed as 11-46 and then later as 10-58.

Line 486  Gaoligongshania is misspelled.

Line 531-534 – I understand what the authors are trying to say here, but this sentence is somewhat awkward.  How about just saying "The deepest split in the PACMAD clade varies among the trees."  Or, "It is unclear whether Aristidoideae, Panicoideae, or both, is sister to the remaining PACMAD taxa."

Lines 534-539 – These sentences describe three possible topologies in 6 trees.  These are supposedly the "complete plastome" trees, but there are four of these, not 6.  If plastome coding and non-coding are included (which they seem to be since the paragraph includes tree R), then there are 10 trees.  Something's missing.

Line 591 – "and" should not be capitalized.

Lines 631-633 – The numbers of trees here do not make sense.  Triodiinae and Dactylocteniinae+Trichoneurinae form a clade in two trees, and Eleusininae and Datylo+Trichoneur form a clade in two other trees.  There are 14 trees, so what about the other 10?

Line 640 – by "included" here do you mean "combined"?

Line 643-646 – The first authors to place the early diverging grasses correctly were Clark et al. in 1995; they should be cited here.

Lines 694 and following – This discussion of gaps is fine but I'm sure it applies more to some gaps than others.  Is it possible to identify which specific genes or regions seem to be responsible for most of the conflicting signal?  This section would be a lot more useful if it focused on specific sets of gaps in specific genes or plastome regions.

Line 826 – Aren't all bamboos polyploid?  I don't think any diploids are known.

Line 951 – need a space between "supported" and "in"

Lines 964-965 – These sentences do not match the tree in Figure 5.  In that tree P. aurea + propinqua is sister to the clade of P. nigra + sulphurea, and then P. edulis sister to the other four.  Although the text here refers to five species only three are mentioned.

Line 1016 – Why is this topology likely an artifact?  In some cases the authors give equal weight to clades supported by non-coding data, but here it is dismissed.  Are there other non-molecular data that argue strongly for the other topology?

Lines 1193 and following – Much of the discussion here relies on unpublished data, in particular that of Saarela et al. (in review).  While it is probably OK to cite some unpublished data for a single point, here the authors seem to be trying to describe a set of trees that the reader has no access to.  I suggest removing most of the references to the unpublished Saarela paper, write the discussion as it pertains to the trees in this paper, and then insert a sentence somewhere to the effect that these results are extended and explored in more depth in the unpublished paper.

Line 1319 – remove open parentheses

Lines 1451-1453 – It is worth noting that Teisher et al. recovered all three possible topologies for the base of PACMAD, depending on assumptions. None was particularly well supported and they concluded that plastome data may be insufficient to resolve that particular set of relationships.  The conflicting topologies of Teisher et al. are cited here but not until several lines below.

Line 1469 – The words "ambiguously aligned" are included here, whereas in most other parts of the manuscript there is no particular value judgement applied to the sites with gaps.  There is also no documentation that the alignment is ambiguous – i.e., the fact that an alignment includes gaps does not make it ipso facto ambiguous.

Line 1498 and following – Teisher et al. (2017) should be cited in several places in this paragraph.  They found the same topology as recovered here, including the strongly supported sister relationship of Arundinoideae and Micrairoideae.

Line 1579  - Cyperochloeae is misspelled. Insert "and" before Steyermarkochloeae.

Line 1580 – Lecomtella is misspelled.

Line 1581 – Lecomtelleae is misspelled.

Line 1690 – "include" should be "includes"
Experimental design: Strengths:  The taxon sampling is comprehensive and the use of complete plastomes includes the maximum possible amount of sequence information.  The Results and Discussion are placed in a broad context and consider all currently available data.
The data analysis is exhaustive and explores all relevant methods.  Exploring the effect of including and excluding gapped sites and sites under positive selection is useful and gives confidence in the results.

Weaknesses:  No serious weaknesses.  My comments have to do with details and nuance and should be easy to address before publication.  My first main concern is lack of evaluation of the various trees; they are described in detail but the reader is left on her own to decide which topologies to consider the most plausible.  The Results section is a narrative description of the trees, duplicating what is shown in the figures.  The Discussion section continues this approach but adds comparisons with previously published trees.  These lengthy descriptions are presented as though all tree topologies have equal merit and as though there are no other biological characters involved.  The Results section would be easier to read if it focused on the most robust results and the ones of most importance for classification or the evolution of major characters.  The Discussion section would benefit from a few mentions of some characters that might be consistent with one or the other of the competing trees.

A second general point is that gapped sites are sometimes dismissed as being ambiguously aligned and sometimes they are accepted as being valid.  Since some gaps are unambiguous (e.g. a well documented indel in ndhf) and some are ambiguous (e.g. runs of As or Ts in non-coding regions), the blanket statement seems not to be fully justified.  Although I'm sure it is unintentional, the reader gets the sense (e.g. line 1469, line 1855-1857) that the gapped sites are being used to dismiss particular relationships on a somewhat ad hoc basis.  For example, on lines 44-45, the statement is made that inclusion of gapped sites 'might introduce false signal".  If the gapped sites are intrinsically unreliable, then they should be omitted throughout the paper.  Conversely if the authors consider that they do provide some signal in some cases, then perhaps the gaps need to be divided into ambiguous and unambiguous sets, or at least consider where and when gapped sites might provide useful information.  It is equally possible that exclusion of sites with obvious indels is misleading and reduces critical signal.  I'd be more comfortable if the authors either a) took a more neutral tone, stating simply that in a few cases tree topologies are sensitive to inclusion or exclusion of sites with gaps, or b) evaluated the gapped sites themselves as to how helpful they are.
Validity of the findings: Nothing to add to comments above.
Additional comments: Nothing to add to comments above.