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: ACCURACY OF DEEP LEARNING, A MACHINE LEARNING TECHNOLOGY, USING ULTRA-WIDE-FIELD FUNDUS OPHTHALMOSCOPY FOR DETECTING IDIOPATHIC MACULAR HOLES
Review round: 1
Reviewer: 3

Output:
Basic reporting: In the table, it is not clear what format and units the time is reported in.

The figure legends should allow the figure to be read without referring to the original article – they may need to be made slightly more descriptive.

I’m not sure ROC curve is necessary or helpful when the AUC is essentially 1.

The image preprocessing is not well described. The images appear to have a circular crop applied to the original image – this should be described.

Was any effort made to center the images, align the disc, or flip left/right eyes to make the images appear similar to the CNN?
Experimental design: no comment
Validity of the findings: no comment
Additional comments: From an image processing perspective, assuming a good quality fundus image, the detection of a macular hole (a small dark circle in a larger fairly homogenous image) is not that complicated, and thus it is not surprising the CNN works as well as it does, but the results are nonetheless impressive.

From a clinical utility perspective, it is not clear that this is a solution to an existing clinical problem since macular holes always cause visual loss in the stages included in this study, the rationale for creating a screening program to detect them is less compelling.  While perhaps not necessary for publication here, it may strengthen the paper to add some discussion as to how such a program might be used in the real world.


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: ACCURACY OF DEEP LEARNING, A MACHINE LEARNING TECHNOLOGY, USING ULTRA-WIDE-FIELD FUNDUS OPHTHALMOSCOPY FOR DETECTING IDIOPATHIC MACULAR HOLES
Review round: 1
Reviewer: 4

Output:
Basic reporting: Introduction
For me, the intro is far too short and doesn’t really describe the problem in enough detail. There is almost no clinical background, and the discussion around deep learning is too brief. I would suggest expanding the Introduction to cover the following topics:

- What is a macular hole? How does it appear in a fundus photo vs. OCT?
- What is the prevalence of macular holes? Some statistics might be helpful
- What are the complications associated with MH, if left undiagnosed?
- Deep learning is not a machine learning algorithm; it’s a sub-field of research within ML
- You state that DL is good generally, but you should give details of why DL is a good approach specifically to your problem. Have other methods been tried previously for MH? Are they inadequate?
- Please cite some other recent DL papers in the context of ophthalmology, especially this one: https://www.nature.com/articles/s41551-018-0195-0

Methods

- It probably makes more sense to describe the FC dropout layer in the section “Deep learning model”, rather than the “Training…” section.
- Lines 132-135 do not make sense - please revise these sentences to be more clear
- A citation is needed for the Grad-CAM method on line 141
- What cost function did you use? Cross-entropy, or something else?

Results

I am quite confused about the methods on page 9. Specifically, how (or why) is “deep-learning response time” calculated by the ophthalmologists (line 125)? The description on line 132-135 about data entry is also unclear, particularly the sentence: “In deep  learning,  a  series  of  tasks  was  performed  for  all  presented  numbers  as  follows…”. My best guess is that the authors are trying to fairly compare the DL computation time with the ophthalmologists’ time taken to record the same information. Please revise this section to be more clear.

Regarding the figures, I think there a few things that can be improved:

- In my opinion, the legends are too short. I personally try to provide enough information in the figures so that a reader could get the gist of the whole paper by reading the legends alone.
- For Figure 2, I’d suggest zooming in on the ROC curve figure, perhaps with the x and y axes at 0.5 or something. You really can’t make anything out otherwise. I’d suggest also including curves from several runs - perhaps the best, worst and average? It’ll give readers a better sense of the variability.
- Figure 3 showing the heat map is not all that informative without a colorbar. It also might be useful to include a few examples rather than just one.
- Table 2: “Accuracy” is a better term for “correct answer rate”. Also please state the unit of measurement time

Other points:

- What is the “first” curve? The first experiment you ran? Why not the best curve?
- On line 162, is this 13 minutes per image?

Conclusions

- There’s no need to repeat that deep learning is an ML technology.
- What are you going to do next?

Grammar, spelling and formatting
Overall the language is very good, though there are a few spelling/grammatical errors:
- Missing space after “macular holes” (line 19)
- Optus → Optos (line 61)
- Lots of unnecessary hyphens in the terms deep-learning and machine-learning (line 71, 88 and various other places)
- “...using a CNN” (line 88)
- “The rectified linear unit (ReLU) activation function…” (line 89)
- What is meant by a ‘tie layer’? Not sure what this means (line 92, 100)
- “The network weights were optimized using stochastic gradient descent (SGD) with momentum…“ (line 101-102)
- ROV → ROC, and various grammatical errors afterward (line 111 onwards)
- Background data (line 147)
- Probably better to describe the eye in terms of left/right or OD/OS (line 148)
- Resions → regions (line 201)
Experimental design: The research question is not all that well defined in the introduction. Ultimately, the goal was to evaluate the performance of DL algorithm for detecting MH. However, the authors also do a good job of comparing the algorithm to multiple experts; something many papers do not do. I would therefore suggest adding a couple of sentences at the end of the introduction to state that this was also part of the study.

My main issue with the overall experimental design relates to how the final model for evaluation was selected. You shouldn’t use test accuracy as the basis, but instead use a validation set. Later, in the “Statistical analysis” section, I don’t really understand the authors’ description of the ROC analysis. I get that there should be one curve per model (100 overall) but I do not understand what is meant by: “We created 100 ROC curves by making 100 patterns, and 10% were thinned out”. Some clarification is needed. The authors also state the model was fitted to only 90% of the test data. Presumably this is an error, and the authors mean training data. This would suggest that the authors did indeed use a 10% validation set, but this is unclear. Please revise this section to better describe how the model was tested and evaluated.

Some other points:

- It’s very common to pre-train networks on bigger datasets to boost performance and reduce the time needed to train. Did you try this out?
- Images from patients with various complications were excluded. How many? Why?
- What was the criteria for “clarity”?
- What is “stage 1” MH and why are they not included?
- You state that 100 models were trained - what was the variability over the 100 runs?
Validity of the findings: As described above, I am concerned about how the final model performance was evaluated. Running the algorithm 100 times and picking the best one based on testing accuracy is cheating a little bit, although it’s not clear from the methods whether this is how it was actually done. Furthermore, given the size of the dataset and near-perfect performance on the test set, I think that cross-validation is necessary to get true sense of algorithm generalizability. I think that given the authors can afford to do 100 repeats on the same data, performing K-fold cross validation should be feasible and would strengthen the reporting.

Given that the authors went to the effort of making an application to capture six experts’ gradings, it would be good if the authors could report metrics of interrater agreement (e.g. kappa coefficients). Furthermore, it’s important that the authors discuss the limitations of the reference standard used, especially if it was based on the diagnosis of a single grader. This paper gives some good insight into why this is important: https://research.google.com/pubs/pub46802.html
Additional comments: Overall, the paper is well written and demonstrates that DL is a powerful approach for classifying MH in wide-angle retinal photographs. The choice of metric is appropriate and the comparison with multiple raters is great to see. Some more background information about MH would be useful for readers outside of the discipline, and would help to contextualize why this work is important.

Ultimately, I am concerned that the results do not reflect the realistic real-world performance of the proposed method. With further clarification of how the model was tested and evaluated, I think that most of concerns will be addressed. However, I would maintain that cross-validation would be a more appropriate way of assessing the generalizabiltiy of the CNN.


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: ACCURACY OF DEEP LEARNING, A MACHINE LEARNING TECHNOLOGY, USING ULTRA-WIDE-FIELD FUNDUS OPHTHALMOSCOPY FOR DETECTING IDIOPATHIC MACULAR HOLES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The response to my question "What are the complications associated with MH, if left undiagnosed?" is missing the point somewhat. It might well be obvious in the field of ophthalmology... but this is not an ophthalmology journal. Non-experts should come away knowing *why* this work is important. Not a massive issue, but a tad dismissive in my opinion.

I also still have issue with the "Statistical analysis" section. This sentence makes no sense to me: "The model was fitted to only 90% of the test data. We created 100 ROC curves by making 100 patterns, and 10% were thinned out." You should not have fitted *anything* to the test data, please correct this typo or clarify what you mean.

"Correct answer rate" is still used in several places - to me this should be "accuracy".

Fully connection layers --> Fully connected layers

The remaining comments have been addressed satisfactorily.
Experimental design: The comments have been addressed satisfactorily.
Validity of the findings: The comments have been addressed satisfactorily.
Additional comments: Thank you for addressing the comments from the original review. With the exception of a few lingering issues from the original (and a few typos here and there) I think that it merits publication.


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

Input:
Title: CONVERSION OF SKELETAL SOCIETY OF RADIOLOGY ANNUAL MEETING ABSTRACTS TO PUBLICATIONS IN 2010–2015
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a well written report. The language is clear.
Experimental design: The methodology for this piece is excellent and superior to the majority of publications on this subject matter in other specailties.
Validity of the findings: The publication rates are higher than observed for other specialties. Could the authors explain why they would think that this might be the case.
Additional comments: is there data on the acceptance rates for abstract for this meeting, This might give context to the difficulty/competitiveness to gain acceptance and therefor may reflect upon the quality of research presented.

For line 177, an alternative term to manpower should be used. In 2018, this term is less acceptable and will likely be less acceptable in years to come. Perhaps say ‘lack of resources’.

For Figure 1, are there numbers for each of these boxes?


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: CONVERSION OF SKELETAL SOCIETY OF RADIOLOGY ANNUAL MEETING ABSTRACTS TO PUBLICATIONS IN 2010–2015
Review round: 1
Reviewer: 2

Output:
Basic reporting: Thank you for the opportunity to review this paper. It is well structured, and sufficiently referenced to justify the conclusions.
There are a few areas where I think the language could be improved, for example in the abstract  "research that has the potential to be...implanted" could be better stated.
Please use "mean" or "median" rather that "average" throughout the paper, as "average " does not have a precise statistical meaning.
The sentence "The shortest time to publication was in 2015 at 10 months, on average..." is quite confusing. I suggest starting by stating what the overall range of publication times is (over the entire time period), and then comparing years. I would give similar advice for the sentence starting in line 139 in the discussion.
Experimental design: The study used a robust method of gathering data, the research question was well- defined, original and meaningful.
Validity of the findings: The data are generally robust, and the conclusions well- founded.
I would suggest that you use Kaplan- Meier or similar techniques to correct for different and incomplete follow up times between the years- this will allow for more meaningful comparisons between the years that are studied.
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: CONVERSION OF SKELETAL SOCIETY OF RADIOLOGY ANNUAL MEETING ABSTRACTS TO PUBLICATIONS IN 2010–2015
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1.	Consider rewording second sentence of abstract (lines 11-13) as currently too broad a statement. Is publication of studies presented at conferences necessarily a sign of how it impacts upon clinical practice? Publication of conference material suggests it has successfully undergone further (usually more stringent) peer review and potentially of higher academic quality than that which isn’t, but this doesn’t necessarily translate into impact on clinical practice.
2.	First sentence in abstract results (line 21) – either use prose or numerical digits but don’t use both, particularly in the same sentence. This applies throughout the paper.
3.	Abstract discussion does not reflect abstract results (no mention in results of publication rates from other conferences for objective comparison).
4.	Sentence 41-44 needs a reference as it is describing (presumably published) evidence.
Experimental design: 1.	The authors should be commended for their thorough methodological design in determining if abstracts have been published, including contacting the presenting authors. However although Firgure.2 explains the method for determining publication, it is unclear from the text that if the situation occurred whereby no abstract was found with traditional search engines and the author failed to contact the study group (‘reply not received’ in the flowchart), whether the abstract was deemed non published (presumably so). Additionally in this flow chart, the initial figure after search engines is n=161, but the final ‘total publications’ is n=162. This number in the final box is inappropriate as various papers have been removed prior to this point.
2.	Lines 61-69 – the dates of the search period for published abstracts should be clearly described. Presumably it is all abstracts published between 2010-2017?
3.	Line 100 – how did the authors determine impact factor of journals?
4.	Lines 100-102 – it is unclear if the time to publication is from the original conference to the publication or from 2010 to the publication (eg if a conference abstract presented in 2013 was published in 2015, would the time to publication be 2 or 5 years?). However, see comment 3.2.
5.	On a similar note, it is unclear if each year of abstracts had a 2 year limit to publication, or were abstracts presented in 2010 given the same time window as abstracts from 2015 (i.e. an extra 5 years?). If the latter, this will bias results in favor of the earlier conferences in terms of publication percentage and should be described.
Validity of the findings: 1. Consider using the following three studies when comparing to publication rates from ECR;

•	Miguel-Dasit A, Martí-Bonmatí L, Aleixandre R, Sanfeliu P, Bautista D. Publication of material presented at radiologic meetings: authors’ country and international collaboration. Radiology 2006;239(2):521–528.
•	Miguel-Dasit A, Martí-Bonmatí L, Sanfeliu P, Aleixandre R. Scientific papers presented at the European Congress of Radiology 2000: Publication rates and characteristics during the period 2000-2004. Eur Radiol 2006;16(2):445–450.
•	Loughborough W, Dale H, Wareham JH, Youssef AH, Rodrigues MA, Rodrigues JCL. Characteristics and trends in publication of scientific papers presented at the European Congress of Radiology: a comparison between 2000 and 2010. Insights Imaging 2016;7(5):755–762.

2. Some of the discussion should be within methodology or results. For example, line 140-143 should be within results and effectively answers reviewers comments 2.4 and 2.5. Equally, 144-146 should be within the results section but comparison to the Canadian data is appropriately within discussion.

3. It is unclear what the numbers in brackets refer to in line 149 (37) and line 150 (35).

5.	Lines 154-158 – consider discussing the limitations of purely using impact factor of a publishing journal to determine the credibility of a study. Whilst in a study such as this, impact factor is a useful (arguably the best) binary, objective measure for assessing scientific quality of studies, there are limitations. For example the fact that it is estimated that the top 20% papers in a journal receive 80% citations (See - http://www.editage.com/insights/why-you-should-not-use-the-journal-impact-factor-to-evaluate-research), therefore publication in a high impact factor journal does not mean the paper will receive a high number of citations.
6.	Lines 162-175 – the discussion on limitations and lack of transparency in selecting abstracts for conferences is commendable.
7.	Lines 179-191 – the authors should be commended for the discussion around publication bias and their efforts in suggesting ways to overcome this.
8.	Lines 197-198 – it is unclear what ‘presented orally for all six years’ means? Was the same abstract presented orally for six years running? Or were oral abstracts presented online for six years following the conference? It currently reads like the former.
9.	Conclusion is overall well written but little is made of the binary results of publication rates. Even if not directly discussed, authors should consider alluding to publication rates vs other conferences, length of time to publication and publishing journals as this is a central part of 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: CONVERSION OF SKELETAL SOCIETY OF RADIOLOGY ANNUAL MEETING ABSTRACTS TO PUBLICATIONS IN 2010–2015
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have adequately addressed all reviewer comments
Experimental design: The authors have adequately addressed all reviewer comments
Validity of the findings: The authors have adequately addressed all reviewer comments
Additional comments: The authors have adequately addressed all reviewer 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: CONVERSION OF SKELETAL SOCIETY OF RADIOLOGY ANNUAL MEETING ABSTRACTS TO PUBLICATIONS IN 2010–2015
Review round: 2
Reviewer: 2

Output:
Basic reporting: Thank you,
All the concerns/ recommendations made on the previous review have been adequately addressed in the revised article.
Experimental design: Thank you,
All the concerns/ recommendations made on the previous review have been adequately addressed in the revised article.
Validity of the findings: Thank you,
All the concerns/ recommendations made on the previous review have been adequately addressed in the revised article.
Additional comments: Thank you,
All the concerns/ recommendations made on the previous review have been adequately addressed in the revised article.


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

Input:
Title: TOWARD AN INTEGRATED APPROACH TO CROP PRODUCTION AND POLLINATION ECOLOGY THROUGH THE APPLICATION OF REMOTE SENSING
Review round: 1
Reviewer: 1

Output:
Basic reporting: Introduction is clear, concise, highly relevant, and of cross-disciplinary interest.
Suggest adding several RST studies on pollination in urban settings, such as urban farms, community gardens, and green roofs to round out manuscript.
Suggest moving RST technology brief explanations up into introduction/background to accompany Figure 1 and expand for clarity versus in discussion section.
Experimental design: As suggested above, urban context appears to be missing. This will enhance the manuscript.
Validity of the findings: Suggest moving RST technology explanations up into introduction and expand, for reader clarity and orientation.
Lines 275 p 278: suggest expanding on the need for interdisciplinary, transdisciplinary benefits for academia as well as lay practitioners and other key stakeholders. This is an important point that cannot be overemphasized, as it is a current gap as well as future research opportunity.
Conclusion will benefit from further strengthening of final key points and the argument for RST.
Some of the study data (i.e. % of papers said X) might work well in a table for better
Additional comments: Much needed design paper for incorporating RST tools and methodologies into pollination services research.


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: TOWARD AN INTEGRATED APPROACH TO CROP PRODUCTION AND POLLINATION ECOLOGY THROUGH THE APPLICATION OF REMOTE SENSING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well written and well structured. The review is broad and raises some good points, but it is mainly a cursory survey of the literature.
Experimental design: The literature review was logically conducted, easily repeatable and the paper was well structured and easy to read.
Validity of the findings: The paper read as an introduction to something bigger rather than a stand-alone piece. Specifically, although the authors mention five types of remote sensing technologies (RST) that could be applied to pollination ecology and crop production, but the bulk of the paper was about the use of satellite imagery. The other RSTs were mentioned only briefly and it was not clear why such technologies would answer questions in the field better than current methods.
While I appreciated the call for "increased collaborative effort between remote sensing experts, crop production and pollination researchers" (lines 276-277), the paper would benefit from an expansion of this point. Such expansion will also likely aid in addressing how the mentioned RSTs would be better than current methods (see above).
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: TOWARD AN INTEGRATED APPROACH TO CROP PRODUCTION AND POLLINATION ECOLOGY THROUGH THE APPLICATION OF REMOTE SENSING
Review round: 1
Reviewer: 3

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

This manuscript presents the results of a literature review about how pollination research integrate remote sensing technologies (RST) to measure environmental variables that might influence pollinator and pollination or use RST to assess pollination success (yield). The authors discuss this results in terms of research potential that could result from a better integration of RST in future pollination research.

The article is nicely written and it is actually really interesting to have a summary about the use of RST in pollination studies. There is a need for the integration of environmental variables in pollination studies that actually match the ecology of insect pollinators, going beyond variables like “proportion of semi-natural habitats” (not all habitats are good for pollinators, and some patches of the same habitat types vary in the resource quality they provide). The authors managed to explain why this is important to measure and how to measure this.
However, I am less convinced by the part of the article dealing with fine-scale measurement of yields and environmental factors that can affect plant growth. The authors state that most of the pollination studies should not extrapolate their result at the field scale from measurement made at the plant scale or at the scale of a group of plants (quadrat or crop row for example), because there are many variations within crop fields that influence yield production such as water availability, soil quality and sun interception (for example). Several problems arise from this section:
-	The authors did not explore the relative benefit of measuring pollination on the whole field versus on some plant individuals. How the field-level yield is different from the yield measured at the scale of quadrats or plants? If the study design is well established, the quadrats or individual plants should be selected to be representative of the whole field. A better study design or an increase in sampling effort could be enough to overcome the within-field heterogeneity
-	The author do not mention that most of the studies exploring the effect of pollinator community on pollination are not primarily interested in this fine-scale abiotic factors that could influence the yield. Many studies actually use some techniques to avoid such confounding effects (comparing bagged versus open flowers from the same locations, using potted plants with the same soil and water availability, increasing sample size to remove possible correlation of those abiotic factors and the variables of interest, etc.). In the field of precision agriculture, I think that measuring those fine-scale abiotic factors and their impact on yield is really important, but I am not sure that those fine scale mechanisms actually put into questions the results of studies finding an “added” value of pollination on yields.
-	The authors recommend to use fine-scale measurement of abiotic and environmental factors using RST (such as nutrient or water availability) to unravel possible interactions between pollination success and those factors. However, the authors state in the text that field-based pollination assessment are not currently able to capture the within-field heterogeneity in pollination success. How to solve this problem? Can we scale-up pollination success measured on individuals or groups of individuals on large spatial scale? Are the studies exploring fine-scale ecological processes acting on pollination success such as species complementarity still valid at the field scale or at larger spatial scale? Could RST contribute to this upscaling? I think that the authors have not tackled those questions in the first place.

The authors should consider using some data to support their argument of spurious upscaling made by most of pollination studies, and show how RST could contribute to it.

Specific comments

Introduction

L 90-91: Andersson et al 2014 is not about pollinating insects but about pollination success of field bean. You might use another reference to illustrate your idea.
L 92-93: The first part of the sentence should be improved: ”habitat needs …dependent on specific habitats”.
L 95: ”variation to” --> ”variation in”
L 98: ” bee pollinators” --> ”bees”
L 98-99: You should rewrite this sentence because it gives the feeling that bees actually disperse from flowering crops, into the wider landscape. They only use them as food resources, and nest in some other habitat patches.
L 103-108: Some cited studies do no deal with pollination success but with pollinator communities (sampled in some habitats), so it is rather strange to use them to illustrate the extrapolation of results from plant scale to larger scales. And some article do not explicitely extrapolate their results: Holzschuh et al 2007 measured some explanatory variables at the landscape scale but still draw their conclusion at the field scale (scale of measurement of the response variable).

Discussion
L 220-221: ”precise scale” --> ”precise resolution”
L 232: ”these spatial and temporal fluctuations” --> ”the spatial and temporal fluctuations” because the previous paragraph refers to environmental variables measured through remote sensing tools, not to remote sensing tools used to infer pollinator community structure and pollination success.


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: TOWARD AN INTEGRATED APPROACH TO CROP PRODUCTION AND POLLINATION ECOLOGY THROUGH THE APPLICATION OF REMOTE SENSING
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 adequately addressed my issues with the initial version and this paper is now ready to be accepted for publication.


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

Input:
Title: CONTINENTAL-SCALE SUPPRESSION OF AN INVASIVE PEST BY A HOST-SPECIFIC PARASITOID UNDERLINES BOTH ENVIRONMENTAL AND ECONOMIC BENEFITS OF ARTHROPOD BIOLOGICAL CONTROL
Review round: 1
Reviewer: 1

Output:
Basic reporting: Please see "General comments for the author"
Experimental design: Please see "General comments for the author"
Validity of the findings: Please see "General comments for the author"
Additional comments: This study presents an impressive amount of data on an important invasive pest and its control using a classic biological control approach (i.e. introduction of the natural enemy from its origynal area of distribution). The authors have followed the dynamics of the insect pest and the parasitoid since the introduction of the natural enemy. These data are followed by experiments in which natural enemies are excluded to assess their impact in controlling the pest. Finally, the authors perform an economic model to assess the economic benefit associated to the introduction of the natural enemy. The paper is mostly well written and the topic suits the journal. Reports of these kind of "natural experiments" are less common than they ought to, and can provide important insights into the ecology of insects and their natural enemies and their applied benefits. Despite these merits I recommend a major revision as I have identified a series of serious concerns that I detail below. Given these concerns at the level of the experimental design, analyses and their interpretation I won't comment on the discussion section.

1. My main concern is about the parasitoid exclusion experiment (L235-236). If I understood it well, this experiment had four replicated plants per treatment (exclusion with cage, non exclusion with cage, non-exclusion without cage), which were enclosed in the same cage. If this is the case, I believe data is clearly pseudoreplicated (even if cage is included as random effect in the statistical model) as plants within the same cage cannot be considered as independent.

2. More details on the analyses performed are needed. In L203- L214, why was field included as random in one model and as a fixed effect in the other? In L203 sampling date was included as fixed factor, but it is not clear to me why. Usually fixed factors are included in models to test specific hypothesis. Was this the case, or was this variables included to correct for the non-independence of samples taken the same day? In L114, how are these models built, and which was the unit of replication?

I am not sure I understand the model described in L266-273: data on productivity per region was correlated with different environmental variables, and year was also included as explanatory variable. Then in 2011 and 2012 the categorical variable "parasitoid" was included as being present while from 2008 to 2010 the parasitoid was included as absent.  I can see the point behind this analysis, but I find a bit unrealistic that the authors consider that the parasitoid arrived exactly at the same time in all regions. Do the authors have more finely detailed data?

3. Many correlations between host density (or host population growth) and parasitism are performed to infer parasitoid control over its host (L175, L208-210, L313, ...). To my view these types of correlations do not represent parasitoid control over the host but whether the parasitoid responds to its host in a density-dependent manner.

Some minor comments follow:
1. In L218 the authors state "In August 2014, a field study was initiated at the Rayong Field Crops Research Center in Rayong, Thailand (Thancharoen et al., under review)". Does this imply that the results presented here are submitted elsewhere? Please clarify.

2. The title and the abstract should be toned down, I find that the sentence "... heralds a new era for
arthropod biological control" in the title overstates the results of this study.  The same applies to the abstract.

3. Although I am not a native English speaker, some sentences could be written in a more formal manner. Examples include L105 "One widely-acclaimed IBC program is the Africa-wide initiative targeting the invasive cassava mealybug", or L140 "We present a data-rich body".

4. L326 and Figure 2. I don't see the point in presenting here data from the population densities in Nigeria in 1982. This data should be used in the discussion section.


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

Input:
Title: CONTINENTAL-SCALE SUPPRESSION OF AN INVASIVE PEST BY A HOST-SPECIFIC PARASITOID UNDERLINES BOTH ENVIRONMENTAL AND ECONOMIC BENEFITS OF ARTHROPOD BIOLOGICAL CONTROL
Review round: 1
Reviewer: 2

Output:
Basic reporting: This research documents and quantifies the enormous beneficial impact an importation biological control program has had on suppressing populations of the invasive and highly destructive cassava mealybug in southeast Asia.

The work is very well done, the results are compelling, and the graphics clearly show the impact the introduced parasitoid A. lopezi had on suppressing pest populations and the concomitant increases in cassava yields.

Importantly, in addition to population impact monitoring/assessments, the authors have provided solid and credible economic estimates supporting the financial benefits of this program to agriculturists, the majority of whom are small landholders that suffer significant income reductions because of invasive pests.

I've made numerous editorial suggestions/edits/comments on the paper - including the title, which in my opinion is a little too grandiose!
Experimental design: Very well done, I don't have any significant criticisms. The authors have employed well accepted experimental designs and statistical analyses. These all appear appropriate to me.
Validity of the findings: The authors have reached well reasoned conclusions based on the experimental data that has been collected and analyzed. A major strength of this work is the vast distances over which it was conducted and the number of years over which data were collected. When combined with manipulative field experiments (i.e., the use of cages) and the estimated economic benefits these findings are strong and credible.
Additional comments: I have no additional comments to share. The work is very well done, the team is highly respected and renowned for the work they do on invasive pest management. This is an excellent piece of work this is a "classic" textbook example of the ability of upper trophic level organisms to suppress invasive pest population thereby supporting "enemy release" theory.


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: CONTINENTAL-SCALE SUPPRESSION OF AN INVASIVE PEST BY A HOST-SPECIFIC PARASITOID UNDERLINES BOTH ENVIRONMENTAL AND ECONOMIC BENEFITS OF ARTHROPOD BIOLOGICAL CONTROL
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article presents the results of field surveys and experiments well designed and executed. The introduction and discussion are clear and well written, with abundant and relevant references. The raw data is provided and the figures are generally clear (but see comments below). The main issue with the paper is the inappropriate/incomplete description of the statistical methods used and the results obtained, which prevents judging the validity of the conclusions of the study (see below details).
Experimental design: The experimental design is adequate, but there are several major issues on the way analysis are described and results are reported that need to be fixed before the article can be published, to properly judge the validity of the results presented. I list some below:
Figure 2 is confusing. Why are less columns in b than a? Are a and b based on different samplings, fields? Pleas clarify. Also, considered using the bars for the same variable, i.e. mealybug abundance in Vietnam in both a and b (currently in a is for Nigeria and in b is for Vietnam). Indicate in the graph (or graph caption) when A. lopezi was released in Nigeria and detected in Vietnam.
L332 – 334 and Figure 3. The statistical analysis on this data is very unclear. You state that field had not significant effect, but you corrected per field, why? Also, the figure suggests you fit models with different slopes per field, why? How do these models relate to the statistic presented in the text? Why did you report a chi square test? Please explain the statistic used to assess the correlation between mealybug growth rates and parasitism and how you arrive to 87 degrees of freedom. Please provide a more clear and detailed information in the methods section and describe appropriately in results. Remove significantly in Line 332.
L342 – 351 and Figure 4. Please clarify if the CMD in the figure reports final values or average across sampling dates. What is the rationale to analyzed CMD over time? Typically, I expect an analysis of mean abundance in each date interacting with time, but only the final date analyzed for a cumulative density (i.e. a cumulative density is constructed in a way that will interact with time and will involve analyzing the same counts multiple times…). Please indicate clearly the rationale for your analysis, clarify that the variable analyzed meet the assumptions of the statistical model and provide references of previous studies supporting this analytical approach. The large number of degrees of freedom (189) suggest pseudo-replication, how was the field effect accounted for? In traditional repeated measures models, the denominator df for the time terms is lower than for the main effects, please explain how you have the same df for time and treatment effects in your models. You indicate that full cage differ from sham and no cage, but there are no tests comparing means reported, please provide statistical support to these differences.
There are 3 df of freedom for treatments, yet there are 3 treatments described and presented in the results (full cage, sham cage and no cage. Only in L 352 you mentioned 4 treatments, but I can’t find any other reference to an additional treatment. Please clarify this crucial point.
L352-359. You provide a Kruskal-Wallis test, include description in the methods on the rationale of using this method. There are no mean tests to separate the 3 treatments; these tests need to be provided to compare treatments after ANOVA or KW overall significance tests.
L264. Please explain how weighted means were calculated.
L371-379. Multiple regression models don’t allow categorical variables (such as Presence / absence of the parasitoid), this must be a GLM; please clarify… The 3 df in L377 are difficult to understand, where 4 periods of time analyzed in that period?? The analysis is very unclear here, please provide more details and complete statistics for the models used in a supporting information.
Validity of the findings: The main claim in the in paper is that the introduction of A. lopezi resulted in a continental-scale reduction in P. manihoti damage and yield losses. The only empirical evidence supporting this claim is the negative correlation between mealybug growth rates and parasitism level, but this evidence is restricted to fields in Vietnam. The manipulative study with cages does not report parasitism levels, so precludes the authors to claim that parasitism caused the reduction on CMD. The third piece of information available is the multiple regression analysis that incorportate multiple factors to explain cassava yield, including presence/absence of A. lopezi. However, this analysis is poorly presented and it is difficult to judge if analyses were appropriate and to assess the importance of each factor tested. I suggest that the authors should improve the description of the models and their results presented in section iv to fully support the claims in the paper.
Additional comments: Minor comments:
Citations in the results section are usually inappropriate and belong to the discussion section of the paper (i.e. L 365)
L370. What is US$ FOB?


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: CONTINENTAL-SCALE SUPPRESSION OF AN INVASIVE PEST BY A HOST-SPECIFIC PARASITOID UNDERLINES BOTH ENVIRONMENTAL AND ECONOMIC BENEFITS OF ARTHROPOD BIOLOGICAL CONTROL
Review round: 2
Reviewer: 1

Output:
Basic reporting: see general comments
Experimental design: see general comments
Validity of the findings: see general comments
Additional comments: This is the second time I read this manuscript, and I appreciate the effort made by the authors to improve it. Most of my concerns have been addressed, but I recommend a minor revision based on the comments below.

Abstract, L 45 and 49 are a bit overstating what is tackled in this review. Please tone down these sentences a bit. I don't think biocontrol is the prime ecosystem service on Earth (think of for example oxygen provision by plants and algae). I also don't agree biocontrol needs a reform, it needs more interesting cases like the one presented here.

L81. "In tropical terrestrial ecosystems, these trends might be even more pronounced though they routinely remain undocumented". Can the authors explain why?

L234-238. Based on the main text, the unit of replication in the exclusion experiment is not yet clear, although in the rebuttal letter the authors clearly show that pseudoreplication is not an issue. Can the authors be more clear in the main text and specify that each treatment had four replicates, each consisting of one cage containing four plants?

L324-326. "In fields where A. lopezi had effectively established, mealybug pest pressure was significantly lower at increasing levels of parasitism". I'd say that mealybug density correlated with parasitism, the speculation that this is linked to lower pest suppression should be mentioned in the discussion section.

L337-339. Move these types of data interpretation to the discussion section.


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

Input:
Title: GENETIC AND MORPHOMETRIC DIVERGENCE IN THE GARNET-THROATED HUMMINGBIRD LAMPROLAIMA RHAMI (AVES: TROCHILIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Comments to the Authors
The authors, present a robust data set, including morphometric, Phylogeography and multilocus phylogeny, to describe patterns of dispersal, origin and taxonomic affinities. I applaud the authors for the vast geographic examination of specimens to provide a complete picture of the evolution and phylogeography of this group. I think the information provided in this manuscript will serve to provide further evidence to the role of the diversification of Mesoamerica biota.
I, nevertheless, found a series of weaknesses in the manuscript, which should be addressed upon before acceptance. The main problems of the manuscript are related to the morphometric analyzes. The absence of a map, which provides to the reader a notion of spatial distribution of morphometric samples and some methodological steps of morphometric analyzes that were not adequately addressed (detailed below). In addition, non-described details of the phylogenetic analysis and problems in the presentation of some figures, compromise the evaluation of the results and the understanding of the manuscript.
I think, addressing these problems, could set the paper in a more robust way.
Besides these major concerns, I have several comments:
Experimental design: Introduction:

Lines 70 – 73: The current phrasing makes comprehension difficult. Moreover, I don't believe that anthropogenic impacts have an influence on increasing the number of studies, as was suggested.

Line 93: The taxonomic review should be improved. If L. r occidentalis was described as a race, how does it have a subspecies name? This needs to be better defined.

Methods:

Line 124: Names of geographic regions should be carefully reviewed to avoid confusion. (i. e. on line 124 is “SMO&nSMS” and in the figures is “SMO&SMSn”).

Lines 196 – 200: The general ornithological literature has used independent runs, with larger numbers of generations and implemented alternative methods of convergence check (for instance ESS values). I recommend a full review of these settings.

Lines 204 – 207: As above, only one run and no convergence check method was implemented!

Lines 212 – 213: Why so many species within outgroup? This is entirely beyond the scope of the manuscript, and you make don't use these outgroup information in the discussion. I suggest to restrict the outgroup species to the genera Eugenes and Heliomaster.

Line 215: On a phylogenetic scale, such as the one you are using, the Beast manual indicates the Yule-process speciation model. Please explain why you used Birth-Death process speciation model.

Line 228: I think you mean: “four of the five”

Lines 242 – 252: I did not understand why to use two different statistical methods to test the differences between groups. ANOVA and DFA do the same thing differently, so why use both methods?
DFA and ANOVA are based on the normality of the data, you did not present any normality test (i.e. Kolmogorov test)
Zoological literature has extensively used data transformations in order to obtain a better fit. I indicate that you make exploratory tests with these transformations (i.e. log-transformation or square-root transformation).

Line 251: Provide the correct citation to the R software (See indication on the own program)
Validity of the findings: Results:

Line 290 and 292: Cite the acronyms of the geographical locations consistently; omissions of letters may cause confusion in the reader.

The scales used in the trees of Figures 3 and 4 make it impossible to visualize the details of the branches of the tree and compromise the interpretation of the results. It is necessary modify the presentation of these figures!

 Line 313: In fact 0.61 Mya, refers to the date of the first split in L. rhami Complex, not to the estimated date for the origin of the clade.

Discussion:
Line 343: I suggest you replace the word phenotypic by morphometric, since you only evaluate a very specific aspect of the phenotype. In the paper, very important aspects of the phenotype, such as plumage and voice, are not considered. This suggestion also applies to the title of the paper.

Line 385 - 386: Which result supports this idea? You should expand the explanation.

Line 397 – 400: This paragraph is speculative; you have no evidence of this in your results. The speculative character of the statement must be explicit. It would be interesting to include some literature that supports this idea.

Line 423: You should change the sentence: “ Provides the existence of occidentalis”. I suggest: “ Supports the taxonomic validity of occidentalis”

Conclusion:

Your conclusions should be expanded and improved. I suggest that you add the taxonomic findings at the conclusion.
Additional comments: The keywords are almost identical to those of the title; you could improve the index by replacing some of those keywords.

I suggest the use of a species delimitation program (i.e. BPP)

Legend Table 1: There is no P in this table!

Trees 3 and 4 need to be redone!

The color schemes, in the morphological and molecular analyzes, could be identical to facilitate the identification by the reader!

Dear Authors, I did enjoy reading your manuscript and thank you guys for your effort to bring novel information on this interesting Hummingbird. Please, read my comments considering that I have a constructive intention to your ideas.
Regards,


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: GENETIC AND MORPHOMETRIC DIVERGENCE IN THE GARNET-THROATED HUMMINGBIRD LAMPROLAIMA RHAMI (AVES: TROCHILIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The basic structure of the submission meets basic standards. However, the English - though professional - has grammatical and style insufficiencies. As I note in my comments to the authors below, I appreciate that the authors do not speak English as a first language. I would be willing to help if asked to review again, but only if given access to a Word document.
Experimental design: Most of the experimental design is appropriate but I have suggestions for additional analyses that I believe would improve the study and I note sections where insufficient methodological detail was provided.
Validity of the findings: I'm confused by the two phylogenetic estimates that disagree with one another, but the general findings are valid. I make suggestions for improvement in this regard in my General Comments below.
Additional comments: In this manuscript, the authors collect multilocus genetic data and morphometric data to assess levels of genetic and phenotypic divergence in the hummingbird species, Lamprolaima rhami. The genus and species are monotypic, though races (occidentalis and saturatior) were previously designated. Schuchmann (in Handbook of Birds of the World) argued that these races are based on clinal or age-related features and were not suitable for subspecific recognition. Although it would be nice to see these arguments addressed in the Intro, I certainly see the value of a species delimitation study that tests these prior hypotheses as well as the possibility of genetic and phenotypic structure matching the allopatric populations (that evidently don't align perfectly with the ranges of the races).

The data collected for this study are appropriate and sufficient for a paper in PeerJ, however, this manuscript is not quite ready for prime time (in other words, publication). In addition to the technical issues that I will discuss below, the MS requires a fair amount of stylistic and grammatical improvement. I sympathize with the authors, who are not writing in their mother tongue, but there were more stylistic and grammatical changes needed than I could handle while working off of a pdf doc. With a Word document version, I would be willing to roll up my sleeves and help, but it is simply unwieldy to make such corrections on a pdf.

In terms of major issues, I think the largest issue is that authors should consider adding a BPP analysis to the study. Given their interest in species delimitation, they should employ a method that will allow them to assess lineage status in a coalescent framework. I found the description of the *BEAST analysis to be inadequate. The authors did not prove relevant details about the analysis that they did undertake. For example, did they run just one analysis with 3 a priori designated species? If so, why only three? Shouldn’t all combinations of possible numbers of species been under consideration? BPP allows for a simultaneous assessment of species/lineage status as well as relationships.  They also provided no basic information about the assumptions of the *BEAST analysis such as models of nucleotide substitution, how many individuals were considered per a priori designated species, etc.

Another issue in the MS is the presentation of two alternative phylogenetic trees. In Figure 3, none of the putative lineages are monophyletic. In the Figure 4 time-tree, two of the three groups are indicated as monophyletic and this tree is then used as the basis for lineage status discussion as well as age estimation for divergences. Why do these two Bayesian trees, presumably based on the same data, differ in such important ways? Minimally, this discrepancy must be addressed before I could envision this manuscript being ready for publication. Also, it seems like a *BEAST time tree is the way to go once the number of lineages is settled upon.

The morphology/phenotype analysis also is poorly elaborated upon in both the Results and Discussion. In addition to the basic problem that there is no key to the letters used to reflect biogeographical regions, it is not clear how we should interpret overlap or lack thereof on the graphs. I was confused by these analyses and I’m sure other readers would be as well.

The Discussion indicates that there is evidence for three genetic lineages. I don’t see it. Depends on whether the tree in figure 3 or figure 4 is assumed. The morph results are not described well enough to interpret lineage status on the basis of phenotype.

Finally, the authors did not come to a decision on the correct number of species for this group. I also thought that they didn’t really spend much time discussing the implications of their findings for cloud forest habitats and their role in speciation. Granted, they mentioned cloud forests in the Discussion, but not to the extent that I think could be warranted depending on how the genetic data sort themselves out. I find that there remains uncertainty about the lineage status of these hummingbird populations and that resolving that uncertainty will allow this study to have a larger impact.

Custom checks:

1) I did not see a data deposition statement

2) I don’t see that they have deposited data on GenBank or plan to do so..

3) I saw no reference to an ethical approval statement

4) I saw no reference to field study permits


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: GENETIC AND MORPHOMETRIC DIVERGENCE IN THE GARNET-THROATED HUMMINGBIRD LAMPROLAIMA RHAMI (AVES: TROCHILIDAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: The English is good, but not great. It is obvious that the authors took great care to write professional, easy-to-read English, however, it is also clear that English is not their first language. As someone who has to write professionally at times in another language that is not my native English, I sympathize. It is hard.

I tried to make as many comments, suggestions, etc. as possible in my in-one comments. However, I would recommend that the manuscript get one more pass from a professional style editor.

Otherwise, the paper's reporting is fine. References and background are sufficient. Figures and tables are attractive and legible.  The authors made attempts to make raw data available. However, unedited sequence data should be submitted to Genbank (not to FigShare); alignments (e.g. Nexus files) are best placed on FigShare. This is mandatory for the paper to be published.
Experimental design: The experimental design is solid. It is not cutting edge (which would be a more comprehensive genome-wide assessment of diversity), but it is solid and would have been state of the art a few years ago. The technical details are sound and the methods would allow replication.

However, Table S1 is insufficient and outside standards in our field. Actual museum voucher numbers (or tissue numbers) should be provided, rather than a summary of samples. And again, these should be provided with the Genbank accession by individual sample.  Likewise, it would be nice to list the museum voucher numbers in a Table S2 for all specimens used in the morphological study. I realize it is a lot, but it helps for reproducibility. And it demonstrates value for scientific collections. This is perhaps more optional. Fixing Table S1 is not optional.
Validity of the findings: The findings are valid. However, I wish that the Discussion was more exciting. Simply talking about the role of the Pleistocene on bird diversification seems a little vanilla in 2018.

In general, I find that the Discussion lacks "hard thinking". It is as if the authors would prefer that the reader do all the cognitive work. Many papers take that approach, but better papers do not.

For example: what are the implications for the authors' findings for taxonomic limits in this group? The authors briefly bring this up, but do provide any guidance. Should the American Ornithological Society split this species? If so, where? If not, why?

Likewise, I wish that the authors would take more time to consider comparative biogeography. Why does this lineage has this pattern of isolation, but other co-distributed bird groups have other patterns of diversification across this space. Is there a role for ecology in explaining this pattern? Discussion of the importance of the Isthmus of Tehuantepec for highland birds (in the Discussion) is lacking.

Finally, what do you think that the L rhami group was doing between 10.5 MYA, which the lineage split from ancestors, and 600 kYA, when the current lineages diversified? It is speculation, but it would be valuable as a thought exercise for considering the conservation value of these lineages? If the pattern is that isolated groups are periodically formed, but also periodically go extinct, what should the conservation goal be? And if dispersal limitation drives diversification in this group, how did the ancestral taxon get to all these isolated ranges?
Additional comments: The abbreviations SMO, SMSn, SMS, and EITn are confusing. They take a lot of time to figure out. I would recommend using other abbreviations, even if it takes additional letters.

I have made many comments directly on the PDF. They are mostly about improving the readability of the manuscript.

Also, a minor note. Since 1983, the AOS no longer considers any subspecies. So line 96 is incorrect in that AOS doesn't consider geographic variation. The current AOS position on geographic races is that they refer you to Peters (1945). I would modify the spatement in line 96.


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: GENETIC AND MORPHOMETRIC DIVERGENCE IN THE GARNET-THROATED HUMMINGBIRD LAMPROLAIMA RHAMI (AVES: TROCHILIDAE)
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have re-evaluated the revised version of the paper “Genetic and morphometric divergence in the Garnet-Throated Hummingbird Lamprolaima rhami (Aves: Trochilidae)” and I consider this new version improved substantially from the previous one.
The authors have made a number of positive changes to the paper to deal with my comments. These included rewriting several key sections and reworking Figures to add clarity. The flow of the paper is much clearer now and I believe it will be easily understood by readers.
Experimental design: The authors have made all the necessary changes to the paper to deal with my comments.
Validity of the findings: The authors have made all the necessary changes to the paper to deal with my comments.
Additional comments: I think the information provided in this manuscript will serve to provide further evidence to the role of the diversification of Mesoamerica biota. I am satisfied with the changes made by the authors and I consider the article more robust and clear.


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: GENETIC AND MORPHOMETRIC DIVERGENCE IN THE GARNET-THROATED HUMMINGBIRD LAMPROLAIMA RHAMI (AVES: TROCHILIDAE)
Review round: 2
Reviewer: 2

Output:
Basic reporting: I initially reviewed this manuscript as reviewer 3. In that review I found the findings sound, but identified areas where the interpretation could be improved, and also found the English quite difficult to follow. I consider this the most improved manuscript that I have ever re-reviewed. The authors have taken extraordinary care to improve their manuscript and should be commended. I believe that this manuscript is acceptable for publication. Below I highlight a few areas where I think that the manuscript could be improved, but I would consider these suggestions rather than mandates.
Experimental design: No concerns.
Validity of the findings: No concerns.
Additional comments: All these are suggestions, and quite minor. I do not need to re-review this manuscript. All these issues can be addressed editorially:

1. The abstract is a bit long. The authors should focus on what is most important from their work.

2. Perhaps the biggest issue for the paper: the authors seem to to conflate a checklist's decision to not consider subspecies with those authors considering that there is no geographical variation in the species. The AOU (now AOS) expanded from North America to North and Middle America (i.e West Indies and Central America) in 1983. When they did that, they decided to no longer consider subspecies across the board. So their decision isn't really a statement that Lamprolaima rhami doesn't not have subspecies. The situation with Gill and Donsker is less clear. They mention a few subspecies, but are inconsistent. So, in general, I would revisit the sentences on lines 99 and 463-464.

3. Line 399: perhaps "is better considered a hard rather than soft barrier...."

4. Lines 478-483 could be written with more impact. The authors seem to pull their punches afraid of (some) contemporary ornithologists dislike for subspecies. This is an opportunity to be more bold. The authors have done some great analyses to demonstrate a lack of meaningful gene flow and evolutionary distinctiveness of populations within the species. These three lineages may be species (the authors haven't really done a test one way or another) and even if they are not, they are evolutionarily-distinctive and deserve to be recognized as such. Since speciation begins with allopatric divergence, these three lineages have the potential to be future species; the authors should say that.

Kudos on a great revision.


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: DISTRIBUTED BAYESIAN NETWORKS RECONSTRUCTION ON THE WHOLE GENOME SCALE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Bayesian networks are useful models for inferring regulatory interactions in biological systems. The authors present an improved version of BNFinder (Wilczyński and Dojer, 2009), a tool to learn Bayesian networks in polynomial time (as opposed to being an NP-hard problem) if external constrains are applied. Specifically, previous implementations of parallelisation were vulnerable in cases where the node degree is highly variable, leading to uneven thread load (Dojer et al., 2013). This is common is biological networks, which typically exhibit scale-free topologies, meaning that the performance gain in the previous version of the tool was limited. Thus, the application of BNFinder on genome-wide datasets was not feasible. In this paper, the authors present a more sophisticated parallelisation algorithm, which they claim dramatically increases computational efficiency and will allow Bayesian network construction on a genome-wide scale.

However, I have several comments and concerns which I believe should be addressed by the authors before publication. In general, I found the paper was poorly structured, there was not a sufficient explanation of how the tool works, and the paper did not sufficiently explain how this tool could be useful to biologists. I believe that this paper is only interpretable to someone who already has a comprehensive understanding of the tool, and that new users will struggle to understand the tool (as was the case for me) unless significant improvements are made to the paper.

Most critically, I found it difficult to assess the tool’s utility because there was not sufficient explanation of how it works nor what data is required to run the tool. For example, I particularly struggled with what external constraints must be placed in order to ensure the acyclicity of the graph. As I could understand from the paper and the online tutorials provided for BNFinder, an expected layout structure must be provided for the network (lines 108-113), with the authors also stating that BNFinder is particularly suited to cases where prior knowledge on the network is provided (line 323). It would be greatly appreciated if the authors could elaborate on what kind of input is required by BNFinder, and how BNFinder works differently depending on the different types of inputs (this is briefly mentioned in lines 262-265, but much more description is required, and should appear earlier in the paper). In addition, if it is true that an expected layout is required, this should be explicitly stated by the authors, as well as explaining how they derived the expected layout for the Sachs et al., 2005 dataset (lines 108-113), in addition to the expected layouts for all other networks constructed. Furthermore, in the case that this tool is used for genome-wide network construction, I struggle to understand what the expected layout would look like (other than a network itself), which would suggest that this tool cannot be used in de novo network construction. Again, if this is the case, this should be explicitly stated by the authors. Furthermore, the authors claim that their method for constructing Bayesian networks is superior to heuristic search methods as they can find the optimal network. However, if the tool is only capable of finding the optimal solution for a given set of constraints in order to ensure acyclicity, then this is not the optimal network either and the comparison is unfair.

On a similar point, I believe that non-computational biologists will have particular difficulty in understanding how this tool works and how to apply it to their data. Given that –omics datasets are becoming more commonplace in labs without a strong computational background, there is a growing need for tools which can analyse these datasets without the need to be a specialist. As the authors acknowledge (line 34), Bayesian networks are ideal for this, as the networks are concise and easily interpretable. Thus, it would greatly increase the utility of the tool and the readership of this paper if part of the introduction were targeted towards non-computational biologists.

I found that the paper was littered with minor grammatical errors. In general, the paper needs to be more thoroughly checked for grammatical correctness. For example, the following corrections are suggested (although there are many other mistakes):
Line 69: It is possible to consider different possible parent sets in parallel, as is the case for the set-wise algorithm.
Line 72: The set-wise algorithm,
Line 73: in comparison with the variable-wise.
Line 101: There is no regulators list for this network, so BNFinder constructed a dynamic Bayesian network.
Line 262: with BNFinder one can use a number of inputs
Experimental design: I had some difficulties in understanding the differences in the parallelisation algorithms employed. Firstly, I did not find the python pseudocode (Figures 1-3) helpful, as this still required knowledge of what each variable is and the custom functions used by the algorithm. I would suggest flow diagrams as a more appropriate way to convey this information, although in either case, it is not appropriate to simply give the names of custom functions used by the tool without providing any guidance as to what they do. Furthermore, it is not explained how the set-wise algorithm was capable of grouping genes into sets (singleton parents, two-set parents etc., lines 69-77), which seems to be the critical step in efficient parallelisation. Further clarification on this is required.

I appreciated the extensive tests and benchmarking exercises which were conducted by the authors. Furthermore, they were very open about the difficulties in using benchmarking exercises to evaluate algorithm performance, and that BNFinder only performed best for some datasets. This is rare in papers describing novel computational tools, and it will prove useful to potential users in deciding which tool to use for their data. It would be particularly helpful if it is stated in the abstract that BNFinder is particularly suited to constructing networks from static gene expression data (lines 246-247).
Validity of the findings: I also have some concerns about the conclusions derived from the performance testing of the new algorithm. In particular, the authors show in Figures 4 and 5 that the performance of their new algorithm is better than the previous version. However, this is only tested on datasets with 20 and 11 genes respectively, so does not support their conclusion that their new algorithm will facilitate genome-wide network construction. It would improve the scientific robustness of the paper if comparison of parallelisation algorithms were performed on appropriately sized datasets. Furthermore, I question the authors assertion that their novel algorithm will facilitate genome-wide network construction. According the Table 1, it took over 12 years of CPU time in order to construct a network a network with ~3500 genes, with each gene limited to 3 parents. Whilst lowering the maximum number of parent genes means that the network could be constructed in a more reasonable time (although still requiring high-performance computing), I am concerned that limiting the number of parents will result in networks which do not exhibit scale-free topology, and thus whether the networks provided by BNFinder will recapitulate the real network structure. I would be interested to hear the authors opinions on this issue.
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: DISTRIBUTED BAYESIAN NETWORKS RECONSTRUCTION ON THE WHOLE GENOME SCALE
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper considers new parallelised algorithms designed for multi-core and distributed systems for the problem of Bayesian Network Reconstruction. The authors have worked in the past on an algorithm and associated software tool (BNfinder) for this. Here, they explore how to scale this algorithm up to much larger networks. They have implemented and added their new schemes to the BNFinder and they have tested this on several simulated and real datasets. Overall, the paper has very good basic reporting, there is sufficient explanation of the  background and context. Also the results are clearly  and professionally presented.

- One area that presentation can improve is the captions of the figures. Currently, they are very short and do not provide sufficient information on what is shown at times. For example, speedup and efficiency need to be described clearly in the caption of Figure 4. How are the methods ranked in Figures 7-10?
Experimental design: This article develops new computational statistical methodology with direct application to global biological data such as transcriptomics  as illustrated in the application of the tool on read data. There is a clear aim here regarding new schemes and this is regorously investigated. I have the following comment to improve the presentation of experimental design.

- Is the idea of hybrid method novel, if so clearly state this and if not please cite a relevant paper. As they argue by the equation on page 15, it is theoretically expected the hybrid method to do worse than the set-wise. Could they explain why in practice hybrid method could have advantage in certain situations.
Validity of the findings: This is a computational project and difficult to assess directly the validity of the results. But, the approach and methodology used is sound and claims are well supported by the results. A bit longer discussion of the comparisons with other methods would be welcome.
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: EFFECTIVE POPULATION SIZES AND ADAPTIVE GENETIC VARIATION IN A CAPTIVE BIRD POPULATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is well written and meets the PeerJ requirements for basic reporting.

One suggestion:
Page 6- the description of the introduction is clear and well described, but it might helpful for the reader for this description to be also supported by a flow diagram, to summarising the population history, estimated population size, and generations in captivity?
Experimental design: The experiment is well defined and executed. I have a few requests for more detail about the methodology, but the approach and implementation is sound.

Page 8- “Longmire Buffer” – can you please provide a reference or supplier for this buffer, or clarify its constituents.

Page 8- “For microsatellite genotyping, a total of 18 microsatellite markers were randomly selected”. Please clarify this statement. Randomly selected from a suite of previously characterized chicken markers? Wouldn’t it have been better to strategically select unlinked markers from across the genome to ensure an unbiased representation of the genome? Please justify why you chose this approach to select markers. I could not find Table S1 that had the list of microsatellite markers- referred to on line 1 of page 8? Please check if this has been accidentally omitted during submission?  If it has not already been done, please include the physical location in the genome of all markers in Table S1. You later state on page 9 that “microsatellite loci came from multiple chromosomes”- it would be better to know exactly where each marker is.

Page 9 first paragraph, please include the details of your PCR reaction conditions and PCR cycling conditions. There is currently insufficient detail to replicate the exact methodology.

Page 9- please clarify if the microsatellite markers were amplified singly and then pooled for fragment length analysis (I think this is what you mean); as opposed to being multiplexed, which means many loci amplified simultaneously in a single PCR. If the latter, please provide multiplex PCR conditions. You mention this later, but it would be helpful to also have this made clear early on.

Page 11- Analysis of linked MHC markers. Please clarify if the MHC SNPs were analysed as a single haplotype or as individual SNPs? The former approach would be appropriate, but the latter approach clearly violates the assumption that markers are unlinked.
Validity of the findings: In general the results are well described and supported by the data, but there are a few instances where this is less true. The authors could improve the following areas:

Page 13- “ranging from 0.359 to 0.371 to 0.379” consider re-phrasing this sentence, it makes it seem as if you only genotyped 3 loci, which is not what you did. Your meaning is not clear here.

Page 13- “The Ne  estimates were in the low single digits for the microsatellite marker dataset, except for the heterozygote excess method.” This sounds too colloquial, please re-phrase to be more specific.

Page 14,-add “As expected”... analysis of linkage disequilibrium based on the SNP loci on chromosome 16 revealed very high D’ values across all pairwise comparisons. They are all physically linked, and thus should show high LD?

Page 15- first line “SNP loci.” Specify, that the SNP loci are MHC linked SNPs – otherwise when read in isolation a reader could mis-interpret this statement and assume they are genome-wide unlinked SNPs.

Page 16- I disagree with the statement “While it is difficult in our study to determine how the SNP loci may be representative of whole genome diversity, there is no particular reason to believe that chromosome 16 would be experiencing selection or drift in ways that are inconsistent with the rest of the genome.” MHC loci could very easily be experiencing differential selection strengths or different modes of selection than the genome as a whole, particularly if the loci are all located on a microchromosome. Please clarify why you think there is no difference? Without further explanation, I don’t think the following discussion statement if supported by the data: “Therefore, we believe that the measures of genomic diversity based on the SNP panel to be more informative about genome-wide patterns of diversity, while the microsatellite-based estimates are consistent with and relevant to our understanding of neutral diversity.” Maybe the authors should consider a discussion of whether it is more important to manage neutral variation or genetic diversity of regions that may underpin adaptive traits?

Page 16- again I don’t think your data support this statement: “If high microsatellite variability does not correlate positively with genome-wide diversity…”. Clarify if this is intended to be speculation or a conclusion.

Page19 – “We found that the demographic history corresponds to a great extent with the genetic estimates.”.. but different Ne estimators were reflecting different historical demographic events? Please clarify?
Additional comments: In general the discussion is a bit long, and it is not obvious what the main result is and why it is important? Can the authors please consider streamlining the discussion in general (reduce word count) and more clearly articulating the main result in the first paragraph of the discussion.

I have a few other suggestions for additional analysis or interpretation that the authors could consider to improve the manuscript:

Page 17 – I think this is very interesting: “Therefore, for both the LD and MC methods, we believe that the estimates obtained here represent the founding event of the Texas population in 2016.” And might be what makes your study unusual, you can comment on the temporal uncertainty of Ne estimators, and that often it isn’t really clear WHEN the estimate generated is relevant to? You could make more of this point and compare what each estimator is doing, what are their strengths and weaknesses? It also means you can highlight how you are not comparing apples to apples when comparing “Ne” using different methods, if they are taking different temporal snapshots of the populations? Can we use this knowledge to our advantage and can you suggest a strategy to get a better picture of population history in terms of Ne? If possible, this would increase the impact and utility of your findings. Could you incorporate this information in the flow chart I suggested earlier about the population history? You are in a fairly unique position having genotyped 100% of the population and knowing so much about the population history, please make the most of this!

Page 18- If you want to talk about the impact of domestication, you will need to include a new analysis comparing MHC SNP variation in your Red Jungle fowl to that of domestic chicken strain, specifically. This could be a nice addition, and there may be sufficient publicly available chicken data (at least from the published genome if not more) to implement this.

Minor typographical errors:
Page 18- remove double reference to Wright “Wright et al.  (Wright et al., 2010)”

Supplemental files:
Table S1 with full list of primers appears to be missing?
Typo in the genotypes file, in the tab name: “Microsatellite Genptypes”


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: EFFECTIVE POPULATION SIZES AND ADAPTIVE GENETIC VARIATION IN A CAPTIVE BIRD POPULATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript is well written with professional English.
Experimental design: Microsatellite information
Manuscript stated that microsatellites would be listed with their primer sequences in S1, but this is not the case. It is important for reproducibility that primer names are listed and primer sequences and references included. The genomic location/coordinates of the microsatellite markers will also be very informative to assess the genomic coverage of this study's genetic diversity. I strongly recommend the authors include microsatellite names, references, and genomic locations.

Using a chr16 specific SNP chip
Focusing on chr16 (SNPs only present on chromosome 16) introduces certain limitations and biases to the study. Chromosome 16 contains the MHC, which is mentioned in the manuscript, but the consequences of this is not adequately appreciated. The MHC is often a target of natural selection, as it has a crucial role in pathogen recognition and immune surveillance, and it's diversity is shaped by host-pathogen co-evolution. The MHC often exhibits strong linkage disequilibrium, so the results herein of strong linkage among SNP markers is not at all surprising, given the proximity to the MHC. It is also not surprising given the historically small population sizes of founders and indeed the small founder size of the studied population, as mentioned by the authors. Nevertheless, it would be extremely difficult in this population to disentangle the linkage observed to be as a result of founder effect, small population size, or positive selection. For example, a historical exposure to disease could result in positive selection for one particular protective MHC haplotype, greatly increasing its frequency in the historical population, and consequently resulting in a major haplotype in this subsequent population. It is therefore difficult to directly compare results from microsatellites to those from these SNPs. I would believe that the microsatellite markers provide a better insight into the wider genomic trend, while the chr16 SNPs provide an insight into the immunogenetic diversity present in the population.

The authors could use the SNP information from this population to compare to SNP diversity present in other chicken populations (domestic chickens, hyrbid RJF/chicken, pure RJF) - much data are available online. Understanding the relationship between the chr16 in this population and that in others could be extremely informative. For example, is the major MHC haplotype on chr16 associated with resistance to any particular poultry disease?

I would also be interested in seeing a generation by generation breakdown of microsatellite and haplotype frequencies. Indeed, the genotypic information in the founders provides a clear insight into the founding genetics.
Validity of the findings: As mentioned in the previous section, the consequences of focusing on a region including the MHC requires much greater appreciation and discussion in the manuscript. Indeed, I believe that the following sentence in the discussion: "there is no particular reason to believe that chromosome 16 would be experiencing selection or drift in ways that are inconsistent with the rest of the genome" is wrong in every way possible. There is EVERY reason to believe that chr16 in particular would experience selection in ways different to the genome. MHC can be shaped by pathogen-mediated selection and also can be shaped by MHC-driven mate choice. Authors should make themselves aware of the selective forces that influence the MHC and therefore will influence chicken chrs16, which is likely to change interpretation of results.

In the conclusion, authors state that they have "showed the dynamics of genetic diversity and effective population sizes" - I would argue they have not investigated any dynamics. Authors have assessed metrics of genetic diversity and effectively population size in one single population at one given time point. This does not represent dynamics. Dynamics could be inferred using multiple time points across populations of varying size but such data that is not available in this study.
Additional comments: This paper is well-written but requires further work to appropriately and accurately interpret results. It is particularly difficult to accept that chr16 is a neutrally evolving genomic region, since decades of research in the MHC across multiple taxa consistently find the MHC is affected by selection. In many studies, MHC is compared to microsatellite markers in order to capture different evolutionary forces that impact genetic diversity in populations. This study would greatly benefit from the use of genome-wide SNP panels, but in the absence of this, I believe a better integration of previous results and publicly accessible genotype data of other chicken populations will greatly improve this manuscript.


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

Input:
Title: WHAT IS AN ARCHAEON AND ARE THE ARCHAEA REALLY UNIQUE?
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is somewhat out of my direct area of expertise, though I consider it a topic of broad interest that is likely to generate very wide readership.  It is well written and takes on an issue that has much relevance for understanding phylogenetic patterns in the tree of life at the grand scale.  I particularly liked how the author revisited some of the core issues and debates about the potential problems with a 3 branched tree of life that were originally brought up by Jim Lake.  The 3 branched view of the tree of life stood in constradistinction to the 2 branched tree of life (TOL) that recognized the “Eocytes” (that Lake propounded).  The result and conclusions the author puts forward are likely to be somewhat controversial (I’m not saying they’re wrong, just that others may disagree), but that is okay.  I think the paper will stimulate discussion and it represents a useful addition to the larger debate about the existence of Archaea and major patterns in the TOL, the data and methods supporting the grouping, etc.

There are a couple of sections, towards the end of the paper, for which I might recommend some changes.  Nothing major, but I think these might tighten up and better focus the paper.  First, in the “Sorting Vertical Evolution (Signal) from Horizontal Evolution (Noise)” section.  Initially, with that title, I thought the author was going to mention horizontal gene transfer.  Perhaps here it might be worth mentioning what impact, if any, that phenomenon could have on phylogenetic relationships.  Also, I think I’d just change the title of this section to “Sorting Evolutionary Signal from Noise”.

Then, for the next section, I found the discussion of “Vertical and Horizontal Classification” a bit confusing, partly because those are terms that I am not familiar with, at least in this context. I’d recommend changing the title of this section to: “Additional Thoughts on Rooting the TOL”.  Then the Simpson (1945) reference is very out of date, and I don’t think most readers will be familiar with it, nor the vertical and horizontal terminology that comes from there.  I’m also not sure if phylogenetically minded folks will agree with all of the statements pertaining to the first paragraph of that section, such that it could detract from the overall message of the paper.  Thus, I’d also recommend deleting the first paragraph in that section.  Instead, just begin with “The classical rooting of the … “.

In the first paragraph of the Conclusions section, I’d cite Lake (1986) instead of, or in addition to, Mayr (1988).

Also, a couple of very minor comments:
Add the word “to” between “Due” and “a” on line 172.
Line 432, change to- Depend on “the” notion
Experimental design: All looked good to me, no other comment.
Validity of the findings: All looked good to me, no other comment.
Additional comments: An excellent publication that I think will make a very worthy addition to PeerJ.


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

Input:
Title: WHAT IS AN ARCHAEON AND ARE THE ARCHAEA REALLY UNIQUE?
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English is good and overall the paper is well-written. I see some mistakes in English in a few places, but nothing stood out terribly.

Introduction, Methods and Result are quite clear and detailed. I have more concerned with the discussion where even if I see myself agreeing with some parts (especially with the importance of the quality of the data), I am not quite sure to have fully understand some others, especially "Vertical and Horizontal Classification" and "Untangling Data Bias, Model Bias and Investigator Bias (Prior Beliefs)"  (see general comments for additionnal comments).
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Abstract: I have some questions mark on my end (line : I find that the uncertainty is primarily due to a
scarcity of information in standard datasets ? universal core genes datasets ? to reliably resolve the
conflicts.). Is this normal ? If it is, I am not quite sure to understand this part of the abstract.

663-667: I have trouble understanding these part. I'm under the impression something is missing there so I would rephrase it.


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: WHAT IS AN ARCHAEON AND ARE THE ARCHAEA REALLY UNIQUE?
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper is fairly clear, though a long-winded and repetitive in places. I found the analysis of the alternative rootings confusing (root-R1 etc). It is also unclear whether this paper represents much of an advance over prior work by the same author, who seems to have been plugging this basic outlook since at least 2013. The paper would be much improved by being halved in length.
Experimental design: On the positive I do believe that the idea of using directional characters to root the tree of life is an important and worthwhile insight, and agree that conserved protein domains have built in directionality, being hard to gain in parallel but easy to be lost in parallel. However, there is a major problem with the approach that the author does not seem to acknowledge: eukaryotes are pretty clear chimeric representing a merger of both an archaeal and bacterial proteome. This is quite devastating in that this predicts that eukaryotes will have a greater diversity of protein domains than either bacteria or archaea, which will tend to pull eukaryotes to the root of the tree (because any parallel gains can be "saved" by placing them on the root lineage). I would consider the paper to be unpublishable unless the author can find a way to properly handle the chimeric nature of eukaryotes.

In order to overcome this issue it night be possible to split eukaryotes into 2 pseudo taxa, one containing domains that probably came from proteobacteria (or cyanobacteria in the case of archaeplastida) and one containing domains of archaeal (Asgardian?) origins. However, without some such correction I cannot see how this work could help support the three-domains topology. Indeed, when I reanalyzed the larger data set using asymmetric step matrices and a parsimony criterion after deleting all eukaryotes (a pain since they were not clearly grouped in the dataset), the resulting trees were rooted with a paraphyletic bacteria, which is incompatible with a three-domains topology regardless of where eukaryotes fit.  (Also, when I created and chimeric taxon that was about half bacterial and half archaeal it dropped down towards root.)

The author draws a distinction between CSRH models with different number of categories used to discretize the gamma distribution. It should be noted that these all entail the same number of parameters and that, empirically, there is rarely any effect of going above 4 rate categories.

The author notes: "...complex features — including molecular, biochemical and phenotypic characters, as well as ecological adaptations —support the uniqueness of the Archaea." However, this is misleading in that these traits could all be plesiomorphic for an archaeal+eukaryotic clade, with subsequent modification in eukaryotes.

I do not find the splitstree analyses useful and recommend that they be dropped.
Validity of the findings: I believe that the analyses are done well but that the fundamental flaw in the experimental design invalidates the conclusions.
Additional comments: I am not especially committed to any one rooting of the universal tree, so my criticism here is not based on any allegiance to the eocyte tree beyond my sense that it has support that is not easy to discount as being due to a particular driving artifact.

I will check "major revision" but you should be aware that unless you can effectively deal with the core problem of eukaryotic chimerism, this might as well be considered a "reject."


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: WHAT IS AN ARCHAEON AND ARE THE ARCHAEA REALLY UNIQUE?
Review round: 2
Reviewer: 1

Output:
Basic reporting: The author has made all of the changes I've requested, and it looks like he's done a good job addressing the changes that others have requested as well.  Thus in my view the paper is ready to move on to the next phase of production and be published.
Experimental design: No comment
Validity of the findings: The paper is a very strong one in all respects.
Additional comments: Nice job addressing my comments.