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: COCCOLITH ARRANGEMENT FOLLOWS EULERIAN MATHEMATICS IN THE COCCOLITHOPHORE EMILIANIA HUXLEYI
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English is clear and unambiguous throughout. I've noted a few minor grammar issues under minor edits below.

The literature references are largely sufficient, although I'm not an expert in coccolith and coccosphere morphology. I have heard the idea advacned in lines 203-204 before, so I would encourage the authors to seek a reference for this idea.

The raw data are shared as part of this manuscript. The data presentation could be improved, for example by ensuring all columns have clear headings and providing a text-document summarizing the content of the data file.

The paper is self-contained and relevant to the hypotheses.
Experimental design: Within the scope of the journal.

Research question defined and meaningful. Methods well described. Some improved clarity in the research questions and flow of reasoning would improve the manuscript. See comments to the authors below.
Validity of the findings: Data robust and controlled.

Conclusions are mostly well stated -- the real conclusion is that the data support the hypothesis of interlocking liths forming polyhedra. Analysis of polyhedra topology using Euler's formula is consistent with this hypothesis. Some improvement of the exposition is required.
Additional comments: I'm not an expert in cocclithophorid biology, lith formation, or evolutionary history. My primary interest in the manuscript is from the perspective of mathematical modeling and data analysis.

The authors use a database, previously collected and described, of coccolith and coccosphere morphology in E. huxleyi, to develop a conjecture regarding the geometry of interlocking liths on the surface of the cell. Geometric constraints (encapsulated in Euler's formula for polyhedra) combined with the requirement that liths overlap in such a way to create polyhedra, imposes some constraints on how the liths are arranged on the cell surface. For example, if a particularly small cell divides with fewer than 12 liths, there will not be enough liths to form a complete coccosphere for both daughter cells. The analysis is clear, and the result is a interesting curiousity, but I'm not convinced this will provide much insight into coccolithophorid biology and coccosphere formuation.

Line 59, 60, 71. These various claims about the liths comprising a coccosphere are a bit confusing. I think you are saying that athough it is common to have "extra" liths in a second layer, you are analyzing liths in the primary coccosphere, which consists of one layer with all liths interlocking. I'm not sure if this is an assumption, but it sounds like it is supported by your data. Some reorganization of these ideas would be welcome.

Line 61. "two times the number of coccoliths with visible central area" -- given the curvature of the coccosphere, this seems like it would be an underestimate of the number of coccoliths. Liths on the outer circumference of the projected image seen by an SEM will be hard to count. For example, in the SEM labeled "6" in Fig 2. (right column, second from the top) there are two liths, one each on the left and right side of the image, that are clearly part of the coccosphere, but neither has a visible central area. Which is counted? Neither according to your description, but probably one should be counted if you are going to double the visible number to get a total number of liths per sphere. I don't know how many liths are in that coccoshpere, but I don't believe it is 14 (2 x 7). Possibly 16, or maybe a bit more. There are some partially visible ones at the bottom of the projected image as well.

line 80-81. I don't think these sentences belong with the rest of the paragraph.

I would suggest you restructure the material describing the interlocking patterns of coccoliths (lines 89-169 or so). The flow of ideas is not clear. The general argument appears to be, or perhaps should be, the following: (1) liths appear to be interlocked in the best-formed coccospheres, (2) these interlocking liths form polyhedra, (3) we can analyze the geometry of these polyhedra using Euler's formula and the CaGe software, (4) these observations yield several constraints on coccosphere morphology -- there can't be fewer than 6 liths per sphere, there can't be more than 6 liths interlocking around a central lith, a diving cell should have at least 12 liths, the topology of the sphere must (?) change when the cell divides if both daughter cells are to have well-formed coccosphere, etc.

line 91-92. I'm a bit puzzled that the average coccolith area is 5.9 µm2, coccosphere area is 120.76 µm2, which suggests about 20.5 non-overlapping coccoliths per sphere & thus presumably more liths per sphere in reality, but the average number of liths per sphere is in fact 15. Is there some postive correlation between lith size and sphere size? Or some other explanation?

line 98-100. Not well described.

line 104 and surrounding. This point is not well described.

What is the distribution of the number of interlocking coccoliths? (e.g. relative numbers of 4, 5, 6). Is this consistent with the distribution of sizes and the geometrical calculations you've done? This would be an important test to convice me that the data all hang together and are consistent with your claims.

line 112. "assumption" - this was not clearly stated earlier. The flow of ideas needs work.

line 115-117: gaps ... indicates .. efficient and fault-tolerant. Not clear what you are saying -- fault-tolerant means what in this case (what would you expect to go wrong if the coccosphere was malformed?). What does efficient mean in this case?

line 126. A proof or citation for this reformulation of the standard form of Euler's polyhedral formula would be appreciated.

lines 144-151. What is the coccolith number of a coccosphere? how does this differ from the coccolith numbers which are consecutive positive integers? I didn't understand any of this paragraph.

line 152-3. Is division of small coccospheres an observed problem?
line 153. It's unlikely that cells count liths! Other mechanisms could surely be cell size / quota.
line 152-158. This paragraph does not hang together well. Your main point is not clear and the material is not well connected.

line 162-169. This needs to be rewritten. It's not clear what you are saying.

line 185-186. "the reason why cell size... limiting light intensities" -- this is quite a different claim from the first half of the sentence. It's not clear what your argument is. Expand?

line 203-4. I've heard this claim made by others -- but I don't have a reference -- and the reasoning was different (not based on your geometric ideas). It would be worth looking to see if anyone else has published this suggestion, even with different reasoning.

Conclusions

Delete lines 230-236. Not conclusions from your work. Perhaps integrate some of this material into the introduction.

Minor edits

Abstract. Methods.
Replace "analyses" with "analyse"
Replace "arrange" with "arrangement"

Introduction.
Line 30. Split into two sentences following the citation to Young.

Materials & Methods
line 46. "Aquil" medium?

Results and Discussion
line 69. Delete "of"
line 77. Try "which will result in the outer layers not fully covering the surface"
line 140. Delete "of"
line 154. "more than" -- what? incomplete sentence.
line 156. "mechanisms" - for what process? incomplete sentence
line 160-1. This is not a complete sentence.
line 176. "full" not "fully"
line 216. Swap "mechanisms" and "behind"

Fig 2 caption
6-22: 22?

Fig 3 caption.
The claims in (a) and (e) are not at all clear. Perhaps remove these to the revised main text.

Fig 6.
Not too surprising.
What about coccolith area and coccosphere area? Do larger spheres have larger liths? Or is lith size independent of sphere size?


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: COCCOLITH ARRANGEMENT FOLLOWS EULERIAN MATHEMATICS IN THE COCCOLITHOPHORE EMILIANIA HUXLEYI
Review round: 1
Reviewer: 2

Output:
Basic reporting: “Clear and unambiguous, professional English used throughout” -
Overall, the manuscript is generally clearly written although there are a few minor instances of grammatical/word-choice errors and a few passages that could be re-phrased to improve clarity and avoid repetition. The manuscript would benefit from being proof-read by a native English speaker, as there are minor language, grammatical and tense errors throughout.
Accessibility to readers of different expertise would be improved by defining the geometry mathematical terms used in their first instance -  L37, “topology” (particularly as topology means something quite different in phylogenetic tree studies), L62, “polyhedral”, L96, “inscribed polygon”

“Literature references, sufficient field background/context provided.” -
I have a few suggestions for additional references that could be added to provide specific experimental or field results that support the authors more mathematical approach in addition to their own observations.
In general, I feel that the Introduction should provide some justification for this study, as none is provided. I have made some suggestions that the authors could include in comments under 2. Experimental Design.
I think that the discussion around the Results and Discussion section “Coccosphere contain only a single layer of coccoliths in this study” assumed the reader is well aware of the processes of cell division and its relationship with coccolithogenesis. However, not all readers will be and these processes are quite different from division cycles in other phytoplankton groups. For example, stating “The changing surface area due to photosynthesis, cell division and respiration” L75-76 is really too concise. To improve the clarity of the discussion, I think it would be worth the authors writing a few clear sentences that describe the cell division cycle, or to ‘pad out’ lines 74-79 with some additional linking sentences that would improve understanding. For example, the line I pulled out above could be precede by something like “Cell volume will increase during the course of the cell division cycle, initially cells are at their smallest immediately following cell division, then increase in diameter as organic carbon is fixed. During this time, each cell is sequentially producing coccoliths that join the coccosphere before cell division occurs again.” And then continue to say L74 “The changing surface area……”. To be honest, I think starting the Results and Discussion with this section is a little odd given that this is not the focus of your paper. If you adjusted the perspective, you could simplify your ideas into a few sentences and move it to the methods around L58-59 to say “Whilst E. huxleyi  is well-documented for producing multi-layer coccospheres (references), we assume that the coccospheres in this study were comprised of just a single layer for the following reasons: 1…..2….3…..4….”

“Professional article structure, figs, tables. Raw data shared.”
The structure of the article is suitable and the figures are relevant and of sufficient quality for publication.
The authors have provided their raw data in the form of an excel file, which appears to include all of the raw data. However, the sheets should be more clearly labelled so that the reader know explicitly what every column contains rather than having to infer it from the equations in the sheet in many cases.
Experimental design: “Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap” -
The study states (L36-37) that the knowledge gap is “….the coccolith topology of coccosphere and the arrange mechanism remain unknown.” and their research question is stated as a result, that “(we) propose that cells arrange each of the coccoliths to interlock with 4-6 others to keep pace with cell growth and cell division”. Given this, I think that the authors should more explicitly state their research question, something along the lines of “to investigate the mathematical constraints that might underpin the arrangement of coccoliths around the cell surface in Emiliania huxleyi ”. Furthermore, the introduction would benefit greatly from a brief statement of why answering this question is of importance or general interest.  I would suggest that understanding mathematical constraints on the arrangement of coccoliths around the cell surface would be interesting/important for (1) providing a theoretical context for empirical studies that have investigated the placement of coccoliths exuded to the cell surface, (2) understanding the maximum and minimum arrangements and their mathematical controls and limits would be extremely useful when trying to model the architecture of extinct species that we have only seen as loose coccoliths and never as intact coccospheres, which are rarely preserved in the fossil record, (3) some insight might be provided on the links between the rate of calcification, the duration of the cell division cycle and cell volume, (4) interesting insights using this approach may arise as to why certain species produce coccosphere of few, large coccoliths compared to coccospheres of many, small coccoliths. The authors might want to incorporate some or all of these aspects into their introduction, or other ideas they have, particularly as some aspects are introduced as discussion later on.

Throughout the Results and Discussion section, there is repeated reference to changes in cell size related to the cell division cycle. This is often poorly integrated or linked to previous or proceeding ideas and, as the cell division cycle is not really explicitly described for the reader in the first instance, can be confusing. Might I suggest that the Results and Discussion section might be more logical to following if there was a section specifically on ‘Size changes during the cell division cycle and its impact on the coccosphere’ that could neatly draw together the ideas in a coherent matter and replace the section “Changing surface area” that is difficult to see what the key messages are and doesn’t really fit.

“Methods described with sufficient detail and information to replicate” –
I have a few more specific comments relevant to the description of the methods:
The authors should add the growth rate that the cultures were growing at and state that their filters were taken during exponential phase of growth (as taking them during stationary would likely affect the amount of ‘malformed’ morphologies observed.
Were the filters taken at the same points in the cell division cycle, so as to minimize the spread of coccosphere geometries observed due to differences in what point of the division cycle cells were generally in, i.e., recently divided or due to divide imminently?
The authors should list in the methods section which ‘geometric parameters’ were measured and then refer to Figure 1. Also, was just a single coccolith measured on each coccosphere, or were multiple coccoliths measured? If so, how did the authors account for the curvature of the sphere/coccolith when measuring a 2D image if the coccolith was not lying flat on the upper surface?
L46 – I believe that “Aqual” should be “Aquil” as the medium name?
L46 – The Price et al. paper was published in 1989
L47-48 – could the authors please add the irradiance levels and light:dark cycle durations experienced under the two light conditions.
L63 – The authors should state what Euler’s polyhedral formula is here instead of or as well as later in the discussion, and a brief worded description that is not too technical would be advantageous to improve accessibility.
L64 – please also include the weblink URL where this software can be found, as requested by under “How to cite CeGe” on their webpage - https://www.math.uni-bielefeld.de/CaGe/
It is unclear to me how the measurements of the coccolith in cross-section illustrated in Figure 1b could have been measured from the SEM images, as you would have required an edge-orientated coccolith connected with the sphere but not interlocked with anything. Could the authors please clarify how these measurements were taken using the SEM, particularly the angles that would have been obscured by the curvature of the distal shields anyway?
Validity of the findings: No comment, all conditions are met.
Additional comments: These general comments are ordered by line, in addition to comments previously mentioned:

L34 – This sentence would benefit by expressing that E. huxleyi  coccoliths vary in size between morphotypes, strains, within strain-specific populations, and even on individual cells.
L37 – Please define ‘topology’ in its first usage.
L37 – This sentence should read “…the coccolith topology of the coccosphere and the arrangement mechanism remains unknown”
L67 – this should be ‘Coccospheres contain….’
L68 – the addition of references to Hoffmann et al. (2015) and Sviben et al. (2016) would be appropriate here, as both studies use imaging technique that show ‘cut-throughs’ of the coccosphere, showing the layering.
L82 – this sentence should end “….found in the medium when culturing E. huxleyi ”
L67 -87 – in general, I felt that this whole discussion section was poorly structured and one idea did not flow smoothly or logically into another, with instances of repetition. The concepts are all there, but I think it would be expressed much more clearly with a degree of re-structuring of these idea and, as mentioned previously, additional sentences describing the cell division cycle. Or re-structuring and moving to the methods section.
L90 – As previously highlighted, I am unclear how you could measure everything shown in Figure 1b using the SEM. Please clarify in the Methods section.
L90-94 – can the authors provide a statement on how these values compare to other reported for E. huxleyi ?
L96 – please define ‘inscribed polygon’
L96-98 – you say “Due to the difference of coccolith size, it is obvious that the outer shields were only partly overlapped to interlock neighboring coccoliths”. However, many of the SEM images you show do have fully interlocked coccoliths and so this is not obvious to me. Also, I think that you would be more accurate to say “Due to the range of coccolith sizes…”. Can you report the range in coccoliths sizes observed on single coccospheres to give an idea of how much variability is observed?
L98-100 – I assume that this uses the means reported in Table 1? - did you test all of the coccolith length-width and central area combinations that were measured? Or can you calculate the actual proportions that would be required to result in an inscribed triangle existing in the area of the shield and then confirm that these measurement combinations were not observed? This might give an indication of whether inscribed triangles would exist in other mophotypes of E. huxleyi  or only in other species, or only in circular-coccolithed species etc. It would seem to me that circular coccoliths with small tube cycles and wide shield widths would be able to have inscribed triangles.
L103 – could you express these as a percentage i.e., the 90th percentile is only 23% larger than the mean. It might better express that the variation is small.
L105 – add “need to be” between coccoliths would…..be much smaller”
L110 – Change to “Using these assumptions, the greatest possible number of edges…..”
L112 – replace ‘results’ with ‘SEM images’ and add theoretical between above and assumption and add an ‘s’ onto assumption.
L118 – finish this sentence with ‘…..or compromise its defensive abilities.”?
L121 – its interesting to note that the maximum number of coccoliths per cell that you observed was 30. Given a minimum of around 6, this would suggest that some cells have more than double the number of coccoliths that would be needed to fully cover two daughter cells following cell division (around 12). Do you have any ideas about this and whether these cells are still a single layer? I see from the data supplement that only 5 of 156 coccospheres had >20 coccoliths per cell so it might be worth mentioning this.
L141 – Interestingly, quite a few other extant and extinct species also have minimum numbers of coccoliths per cell at around 5-7 and coccospheres of 6 coccoliths forming cubic shapes have been reported in Helicosphaera carteri and extinct Toweius pertusus, an ancestor of E. huxleyi  (http://www.mikrotax.org/Nannotax3/index.php?taxon=Toweius%20pertusus&module=Coccolithophores for images) and Umbilicosphaera bramletti – see the PhD Thesis of Sheward (2016) University of Southampton and the dataset of Gibbs et al. 2013 and Sheward et al. 2017.
L146-150 – I’m afraid that I don’t really understand what you’re trying to say in these lines, referring to removing coccoliths and then having them produced again one by one indicating that the coccosphere must have 4-6-edged faces. Please try to clarify this idea in a different way?
L160-161 – “Since the edge number of a coccolith must fall in the range of 4 to 6.” Is not a complete sentence.
L161 – remove the ‘, which’ and just write “Assuming a mother cell covered…” and continue on L162 “…..interlocked coccoliths that have divided into….”
L162-166 – Again, this discussion would be aided by a description of the cell division cycle earlier on.
L174 – also supported by data collected from modern and fossil coccolithophores in Gibbs et al. 2013, Sheward et al. 2017 and the thesis of Sheward (2016).
L171-204 – This whole section of the discussion, in its current form, doesn’t really fit well in the manuscript or make clear points. There is quite a bit of repetition of ideas and I’m really not sure what you are trying to tell the reader. It is confusing that you suddenly jump to discussing Braarudosphaera, which does has a fascinating coccosphere architecture, but is also completely different from E. huxleyi  in the fact that it is an extracellular calcifyer and produces nannoliths not interlocking placoliths. The statement on L198 “….and thus pentaliths counld not interlock with others like the coccoliths or E. huxleyi ” is therefore completely redundant. I presume that the inclusion of Braarudosphaera in this section in “Changing surface area” is due to the difficulty of linking its coccosphere architecture with size changes relating to the cell division cycle?
L218 – ‘interlock’ should be ‘interlocking’
L224 – ‘arrange’ should be ‘arrangement’
L227 – should state somewhere that these ‘interlocking taxa’ are called ‘placolith’. Wuold be nice to add how many extant placolith species there are.
L227-228 – the genus names are mixed up here.
L230 – change ‘studied’ to ‘studies’
L235 – change ‘studies’ to ‘investigation’

Referenced additional studies:

Gibbs et al. (2013) Species-specific growth response of coccolithophores to Palaeocene–Eocene environmental change, Nature Geoscience
Sheward (2016) Cell size, coccosphere geometry and growth in modern and fossil coccolithophores, PhD Thesis, University of Southampton.
Sheward et al. (2017) Physiology regulates the relationship between coccosphere geometry and growth phase in coccolithophores, Biogeosciences
Sviben et al. (2016) A vacuole-like compartment concentrates a disordered calcium phase in a key coccolithophorid alga, Nature Communications.


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: COCCOLITH ARRANGEMENT FOLLOWS EULERIAN MATHEMATICS IN THE COCCOLITHOPHORE EMILIANIA HUXLEYI
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article explores an interesting subject – the geometry of coccolith arrangement. The English in the article could use work throughout; there are numerous grammatical errors, especially relating to the presence/absence of 'a' and 'the'. The citations are sufficient, the article is reasonably well structured, and the data is accessible, but there is very little explanation of what the reader is supposed to have learned that she could not have figured out from looking at some photographs of E. huxleyi, and very little explanation of what motivated the study and what interesting or useful results came from it.
Experimental design: It appears that the authors were careful in their methods, and the research falls within the aims and scope of the journal. However, it is very difficult to gather what is the research question the paper is addressing. Why are the results interesting? Why are the results not trivial? What was the hypothesis being tested?
Validity of the findings: The different software packages used in the manuscript should be described in much better detail so that the reader knows what is being done and how it relates to the question being investigated. Euler's polyhedral formula should also be described in much greater detail because it features prominently in the manuscript but is never properly introduced. I would not say that the study is described in enough detail to be reproducible. More importantly, though, I would say it's hard to determine what new information the authors were trying to show.
Additional comments: I think you can make this into an interesting paper but I think the writing needs a lot of work. To me it seems possible that you analysed many pictures of E. huxleyi and ended up with conclusions that had to be true and that are apparent just from looking at pictures of coccoliths. I think you need to do a lot more writing so that you can explain to the reader what exactly you did (so they could reproduce it if they wanted to) and why you did it, and what you learned about E. huxleyi that isn't already known.


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: COCCOLITH ARRANGEMENT FOLLOWS EULERIAN MATHEMATICS IN THE COCCOLITHOPHORE EMILIANIA HUXLEYI
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The revised version is much clearer; I feel that all of my comments have been addressed satisfactorily.


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: BAREFOOT RUNNING DOES NOT AFFECT SIMPLE REACTION TIME: AN EXPLORATORY STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.	Basic Reporting
A.	Clear and unambiguous, professional English used throughout.
Meets criteria.
B.	Literature references, sufficient field background/context provided.
Introduction provides sufficient connectivity to the current literature with adequate references.
C.	Professional article structure, figs, tables. Raw data shared.
Resolution of Figures 1, 2, and 3 are fuzzy (noting this maybe an artifact of converting to a PDF file). Resolution of figure 4 is acceptable. Data is available and readable.
D.	Self-contained with relevant results to hypotheses.
Yes.
Experimental design: 2.	Experimental design
A.	Original primary research within Aims and Scope of the journal.
Yes.
B.	Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap.
Yes and does so in a compelling fashion.
C.	Rigorous investigation performed to a high technical & ethical standard.
Study conducted with permission from Interdisciplinary Committee on Ethics in Human Research at the Memorial University of Newfoundland (ethics approval number: 20130246-HK).
D.	Methods described with sufficient detail & information to replicate.
The authors did an outstanding job in this regard.
Validity of the findings: 3.	Validity of the findings
A.	Impact and novelty not assessed. Negative/inconclusive results accepted. Meaningful replication encouraged where rationale & benefit to literature is clearly stated.
Novelty was accessed, negative results were reported and related to existing literature. Replication was discussed within meaningful parameters.
B.	Data is robust, statistically sound, & controlled.
Statistical and data analysis are appropriate to answer the research question and supported the research design employed.
C.	Conclusion are well stated, linked to original research question & limited to supporting results.
Yes.
D.	Speculation is welcome, but should be identified as such.
I did not detect any unwarranted speculation.
Additional comments: 4.	General comments
I have been reviewing papers for over 15 year now. I must say, this is in the top 95% of well written papers I have come across! Cheers to the authors!
	With that said, there are some minor comments embedded in the manuscript via the tracker function. Most of the comments are typos and such. There are a couple of content comments that should be addressed and/or included prior to publication.
5.	Confidential notes to the editor
See tracker comments embedded in 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: BAREFOOT RUNNING DOES NOT AFFECT SIMPLE REACTION TIME: AN EXPLORATORY STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: This study was very well written and thorough. Literature review was complete and provided strong basis for the study and sound explanation of results.

Figures 1, 2, and 3 seemed a bit blurred but content was relevant.
Experimental design: The research question was clearly articulated.  The research design was especially strong, especially in light of controlling for confounding variables.  The methods were very well detailed. The only potential downsides were the small subject number but as an exploratory study, this was explained. Also, only males were used and no explanation was provided as to why the subject population was limited to one gender (Line 125). Additional justification would be appropriate here.
Validity of the findings: The results were well presented and the subsequent discussion was very sound. The discussion was well referenced and clear. This was a strong suit of the paper.
Additional comments: This was a very well designed and well written study. It would be good to expand and include females, if possible but overall this was a strong paper.


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

Input:
Title: PATHWAYS OF TOPOLOGICAL RANK ANALYSIS (POTRA): A NOVEL METHOD TO DETECT PATHWAYS INVOLVED IN HEPATOCELLULAR CARCINOMA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clearly structured and easy to understand. An introduction to the field and literature references are provided; however, when discussing previous network analysis methods, the authors mainly present classical Gene Set Enrichment Analysis (GSEA) and approaches to identify differential co-regulation and co-expression of genes in biological networks, but previous topological network analysis methods that may provide an alternative to the authors' PoTRA approach are not mentioned (a very comprehensive review of these approaches has been provided by Mitrea et al., Frontiers Physiol., 2013, https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3794382/). Some of the representative approaches for topology-based network and pathway analysis should be briefly discussed to enable the reader to make a comparison (currently, only approaches are mentioned which according to the authors "are limited by the fact that they
ignore the topology of the gene networks and sets that they investigate" (line 89), but this does not apply to all previous methods).
Apart from this, the descriptions in the text, and the figures, code and data provided are sufficient to understand and reproduce the methodology proposed by the authors.
Experimental design: The aim, scope and research question are well defined and the topic is relevant to the field. The hypothesis that the previously observed reduced network connectivity in cancer may result from a reduced number of hub genes that disrupts the scale-free structure of the network is interesting, and in principle, the proposed topological analysis is a logical approach to test the hypothesis and identify pathways with corresponding topological changes.
However, my main concern is the construction of the gene network: The authors do not use a experimentally confirmed gene regulatory or protein-protein interaction networks, but instead build correlation networks that are purely derived from Pearson correlations between gene expression values from public cancer transcriptomics datasets. High correlations between the expression values of thousands of genes in transcriptomics datasets can easily occur by chance or reflect indirect relationships rather than physical interactions - using a significance cut-off of 0.05 is not sufficient to ensure that the correlations reflect biologically meaningful functional associations in cancer or normal cells (moreover, the authors do not state whether the computed p-value has been adjusted for multiple hypothesis testing).
Importantly, the loss of hub nodes in the correlation network observed by the authors does not necessarily need to reflect the loss of a hub gene/protein in a real biological interaction network, but may instead only reflect an increased variance in the cancer gene expression data as compared to healthy samples.
Increased variance in transcriptomics datasets will nearly always result in lower Pearson correlations between genes, and therefore also in a lower number of hub genes in correlation networks, but this does not mean that a loss of hub nodes occurs in real biological interaction networks.
The hub count changes identified in genes from certain pathways using the authors' PoTRA approach may therefore reflect an increase of variance in the corresponding cancer pathways, but not necessarily a real change in hub nodes in the underlying molecular networks. To test this, the authors should also investigate whether there is a change of variance in the expression across all genes in a pathway, when comparing cancer vs. controls, and they should assess statistically, whether altered correlations between pairs of relevant genes also match with known direct regulatory or protein-protein interactions between corresponding genes/proteins, in order to check whether a hypothesized topological change in a network of real biological interactions is plausible (this cannot replace an experimental validation, but the reviewer understands that an experimental evaluation may not be feasible for the authors - therefore, additional in-silico analyses, such as the ones suggested above, should be provided and the limitations of correlation-based network analysis highlighted in the manuscript).
Validity of the findings: The overall approach is logical and described in a reproducible fashion; however, the issues associated with purely correlation-based gene networks (see Experimental design section) may also negatively affect the validity of the findings. If higher variance in the cancer gene expression data as compared to the tumor-free controls results in lower Pearson correlations between the genes in the cancer samples, then this would also explain the reduced numbers of hub nodes in the cancer correlation networks. In this case, the proposed algorithm/software would not detect new cancer-associated pathways with changes in hub nodes in a real biological network, but only changes in variance, which can also be identified by statistical variance analyses without additional network information (i.e. the same or very similar pathways would be identified by already existing tools that score changes in the variance of expression levels within pathways).
If a correlation-based network construction approach is used, then the authors need to check that the loss of hub nodes does not simply result from increased expression variance in cancer. Moreover, a more reliable correlation measure than the Pearson correlation should be considered for network construction, e.g. the biweight mid-correlation which is more robust to outliers (see Zheng et al., 2014, https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4271563) or indirect and spurious correlations could partly be filtered out by using the partial correlation for network construction. If significance scores are used to define the cut-off for representing a correlation as an edge in the network, then these significance scores should be adjusted for multiple hypothesis testing (the authors use an FDR-adustment for the pathway analysis, but it is not clear whether they also apply it for the network construction).
Finally, the example applications presented by the authors are interesting, but the authors should be careful to interpret the fact that the identified pathways are cancer-associated as a validation of their approach: Generic pathways such as the discussed MAPK signalling pathway have many functions, and almost all pathways with a similarly broad involvement in many cellular processes have been implicated either directly or indirectly in cancer diseases. The fact that these pathways are identified as significant by the authors' approach does not prove that the method specifically identifies cancer-associated pathways. To assess this statistically, one possible approach could be to define a priori two lists of known cancer-associated and non-cancer associated pathways, and then evaluated statistically, whether cancer-associated pathways are over-represented among those identified by PoTRA in relation to non-cancer associated pathways.
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: PATHWAYS OF TOPOLOGICAL RANK ANALYSIS (POTRA): A NOVEL METHOD TO DETECT PATHWAYS INVOLVED IN HEPATOCELLULAR CARCINOMA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well-written and the implemented methodology is clearly described in a step-by-step style. Some parts of the text appears redundant between separate sections, but the degree of overlap is not too much.

The references to the related works in Introduction (lines 103-118) are rather old. The authors should add more recent works on the topics of differential co-expression analysis and differential network topology analysis.

The method is based on the assumption that biological networks are scale-free, but no results to support this are shown. The scale-free property does not always hold in practice (PMID:15767579, 15284103, 16003372,16706727).

The figures are of sufficient quality, but Figure 3 remains very uninformative. The gene names are not shown at all, and most of the nodes and edges are overlapping, making it impossible to get any biological  insights.
Experimental design: The topic of the paper is withing the scope of the journal. The research question is well-defined, and meaningful for cancer biology; however, there are already a plenty of methods available based on the same concepts and PageRank algorithm. It remains unclear what is the added value of this method beyond the existing ones, and why the researchers should use the proposed method? Rigorous comparative investigation against the related methods and software is required to convince the readers about its added value and performance.

Choosing only one cancer type from TCGA cannot really demonstrate the general applicability of the method. The authors should apply their method to several cancer types (and sub-types, see below), and also compare the results across various cancers and tissue origins, to investigate how cancer (sub-type)-specific or selective the findings really are.

The methodology is clearly described in a step-by-step manner, and the sources codes have been made available to allow for replication of the results. Some parts of the methods, however, lack rationale or motivation, and should be described in more detailed manner. The authors should also investigate the robustness of their results to parameter changes:

- Why KEGG databases was chosen to define pathway gene sets; have the authors evaluated how much the results change if some other pathway databases was used instead (e.g. Reactome or MSigDB)? Why the pathway interactions were not used to define the network topology, instead or in addition to the co-expression gene-gene links?

- Why Pearson's correlation was chosen to define gene co-expression interactions; have the authors evaluated how much the results change if some other metric (e.g. MI or MIC, see PMID: 23217028) was used instead? Why p<0.05 was chosen as cutoff; was this corrected p-value (FDR) or not, and what was the test (permutation or large sample assumption)?

- The Fisher's exact test requires a cut-off for testing the differences in hub genes between normal and cancer groups. Why 95th percentile was chosen, and how much would the results change if one uses some other cut-off instead? Could the Kolmogorov–Smirnov test be used alternatively, similar to GSEA, which avoids the need of introducing any cut-offs?
Validity of the findings: The current results are not very convincing as these are presented at a very general level; for instance, "Pathways in cancer" is too broad to learn any selective mechanisms for HCC or other cancer types. It remains also unclear whether the users can identify any novel, potentially cancer-specific genes or pathways using the proposed method?

The cancer sub-type-specific findings are most relevant and interesting, as most of the cancer types cannot be treated as a one entity, rather they contain various sub-types with distinct genomic or epigenetic backgrounds. The authors should follow-up these findings, and make more rigorous investigation of the relevance of pathways for various sub-types.

In the sub-type-specific analyses, the number of samples may become quite small, when going into smaller and smaller sub-types (e.g., precision medicine approach). It remains unclear how the correlation calculation deals with such small sample sizes (and what are the sample sizes), when estimating the statistical significance of co-expression interactions?
Additional comments: The method is based on an established concept that cancer processes are characterized by the loss of network connectivity (sometimes cancer processes lead also to new connections and re-wiring, which could be studied as well). However, The other assumption of scale-free property of co-expression networks is not so straightforward (e.g. one can impose the property by changing the correlation cut-off, seen PMID 17553854). Therefore, all the current results related to the scale-free property or its changes (e.g. lines 313-317) are speculative only, and should be accompanied by rigorous statistical analysis of the property in the networks constructed based on the TCGA data (see e.g. 16706727).


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: PATHWAYS OF TOPOLOGICAL RANK ANALYSIS (POTRA): A NOVEL METHOD TO DETECT PATHWAYS INVOLVED IN HEPATOCELLULAR CARCINOMA
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 addressed my comments and their revisions have improved the manuscript. Most importantly, they acknowledge now that the cancer-associated changes in correlation networks most likely result from increased variance in the cancer gene expression data as compared to healthy samples rather than from a topological change in real molecular networks, which will help to prevent a misinterpretation of the results generated by the authors' approach.


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: PATHWAYS OF TOPOLOGICAL RANK ANALYSIS (POTRA): A NOVEL METHOD TO DETECT PATHWAYS INVOLVED IN HEPATOCELLULAR CARCINOMA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The scale free property was not statistically tested in the revised paper, or did I miss it? The authors should follow the formal statistical testing procedures described in the previous papers cited in my comments, to show that their scale free assumption holds in the analyzed datasets; and if not, how this affects the operation of their approach. I do not see this as very critical assumption of the approach, but since the authors mention that many times, it should be also statistically tested.
Experimental design: If this manuscript is the first (methodological) work about the approach, I would still add the explanations of the methodological issues I asked in my original review section, rather than providing the answers in the response letter only. Please add to the Methods your answers answers to my comment: “Some parts of the methods, however, lack rationale or motivation, and should be described in more detailed manner.

The authors should also investigate the robustness of their results to parameter changes, e.g., how much their finding change if the pre-defined parameters were altered.
Validity of the findings: The current biological results are still not too convincing; rather, the current results and tables seem like lists of already known findings (which is just fine as for positive controls, but they should be described as such), or potential hypotheses that someone could follow-up (perhaps in separate papers), but making more detailed “story” for selected cases would make the results more concrete. Regarding other datasets, the authors’ response to my original comment was quite surprising:

Original comment: Choosing only one cancer type from TCGA cannot really demonstrate the general applicability of the method. The authors should apply their method to several cancer types (and sub-types, see below), and also compare the results across various cancers and tissue origins, to investigate how cancer (sub-type)-specific or selective the findings really are.

Author’s response: We are currently working on the analysis of breast cancer data and pediatric desmoplastic round cell tumor (DSRCT) cancer data using PoTRA. These data sets are still being analyzed and manuscripts are under preparation.  Also, we are planning to analyze the entire TCGA data set (33 cancer types currently in GDC) and publish the results separately.

Could a few of these ongoing analyses in other cancer types be included into this work, to support the wider applicability of the method, rather than published separately? Further, the sub-type specificity of the findings is very important issue to address, like argued in my original comments, as these cancers cannot be treated as one entity. The authors should follow-up their findings, and make more rigorous investigation of the relevance of the pathways for various sub-types.
Additional comments: The authors have partly addressed my original comments. However, there still remain important concerns that were not addressed in the revised version (as described in the boxed above).


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

Input:
Title: SURFACE DISPLAY FOR METABOLIC ENGINEERING OF INDUSTRIALLY IMPORTANT ACETIC ACID BACTERIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, the authors provide convincing evidence with statistical support that their surface display system is sufficient in producing recombinant enzymes at the outer membrane of Gluconobacter oxydans. This is of particular interest in the field, because of the difficulties associated with engineering G. oxydans membranes to produce useful proteins that can directly interact with the surrounding environment. It is my opinion, this manuscript is acceptable for publication with a few minor changes, which are listed below.

Minor concerns:
Both lines 35-37 of abstract and lines 80-83 state (I paraphrase here) that the expression of extracytoplasmic enzymes is difficult in the inner membrane because the membrane is crowded with proteins. This statement underlines the importance of their work and why the development of a surface display system in Gluconobacter oxydans is a potential bioengineering solution. It would help their case to cite the “crowdedness of the membrane.” For example, see Guigas and Weiss 2016 Biochim Biophys Acta (PMID: 26724385).

Line 198: Samples were incubated at 23 C for how long?

Line 248: I would remove the word “significantly.” Although the t-test shows a clear difference, there is an apparent overlap between samples in Fig. 3, and this is reflected in their ANOVA analysis.

Line 336: The same comment for line 248, remove “significantly.”

Lines 416-418: Although it is not required for this manuscript, I am curious if the authors have tried adding more phosphate to the media and measured the growth. Does additional phosphate rescue the slowed growth they observed when producing PhoA?

Figures 1-5 legends: It would be helpful if the units (deltaA405/hxOD600) for the phosphatase activity were included in the legend.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No comment


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

Input:
Title: SURFACE DISPLAY FOR METABOLIC ENGINEERING OF INDUSTRIALLY IMPORTANT ACETIC ACID BACTERIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are minor comments to the writing, detailed in the general comments to the author section.
Experimental design: No comment
Validity of the findings: Some discussion might be required, see general comments section.
Additional comments: This is an interesting piece of work where the authors make a proof of concept for surface display in an effort to potentiate the abilities of Gluconobacter oxydans as producer of industrial metabolites. The authors fuse a N-terminal of OprF from Pseudomonas aeruginosa to a alkaline phosphatase (PhoA) from E. coli under the control of strong and moderate promoters. The authors also assay the contribution of flexible and rigid linkers. They make supernatant phosphatase assays in E. coli and G. oxydans. Concluding that for G. oxydans the genetic construction that works better includes the use of the strong promoter and a short rigid linker fused to OprF and PhoA.
I think the work could be of interest for the readers of the journal and recommend their publications, I just suggest the authors could attend the following points:
1.	The abstract could be improved stating that for G. oxydans the strong promoter is better, and resuming how is the whole genetic construction that works better.
2.	In the discussion section the authors could argue why the phosphatase activity in E. coli is superior than the best achieved in G. oxydans.
3.	On line 114, there is repeated the word “in”. On lines 324-326 please revise the words promotor-promotors.


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

Input:
Title: THE NEGLECTED BEE TREES: EUROPEAN BEECH FORESTS AS A HOME FOR FERAL HONEY BEE COLONIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.  Basic reporting.   Excellent.  Authors introduce well the aims and rationale for their investigation:  to initiate the study of wild honey bee colonies in European hardwood forests by determining minimum estimates of colony density.   They also explain that although Apis mellifera is native to Europe, there is almost nothing known about the wild colonies of this species within Europe, hence this is a path-breaking investigation.   The writing is clear and precise and grammatically correct.
Experimental design: 2.  Experimental design:  Clear.  The authors have adapted methods used in North America to locate honey bee colonies living in forests, and they have applied these methods to their study sites with skill.   Also, they have set up artificial swarms properly and taken meaningful data from them by reading the waggle dances of nest-site scouts.   They did well to feed these artificial swarms with sugar water  while they were house hunting, to eliminate the possibility that the dances they observed were advertising flower patches, not potential nest sites.
Validity of the findings: 3.  Results and Discussion:  Generally excellent, with super graphics, but I have some suggestions for improvement.

Line 67:  The references cited here are Seeley and Morse 1976 and Seeley 1985.  It would be better to cite Visscher and Seeley 1982, Seeley 2017, and Seeley et al. 2015, for these three papers provide clearer evidence that in nature colonies nest in widely spaced tree cavities.

Line 69:  Besides being smaller and swarming more frequently, wild colonies have less brood; these are all things that make them less susceptible to varroa mites.

Line 77-78:  Recent work, about to be submitted, has revealed that the honey bees living in the Arnot Forest possess multiple behavioral mechanisms of resistance to varroa.  These include intense hygienic behavior (99% of infested cells are cleaned out within 48 h) and good biting behavior (ca. 40% of phoretic mites are killed by having legs bitten off).   So I recommend changing this sentence, and giving as the reference the following:
"Peck and Seeley, personal communication."

Line 85:  Yes, it is very good to begin to gather information from European forests.

Line 95-97:    I agree with the view that the conclusions by Moritz et al. 2007 and Jaffe et al. 2010 (that wild colonies were not present in their study sites) are weakly supported.  The method used in these studies to estimate colony density require making many, many assumptions (e.g. about drone and queen flight distances, etc) so the estimates of colony density that were reported are very imprecise.

Line 156: Replace "are quite site fidel" with "have high site fidelity."

Line 216:  Replace "swiped" with "swept".

Fig. 4, right side:   It would be good to relate the results shown here to the results on dispersal distance reported in Seeley and Morse 1977.  In this study, the modal distance to prospective nest sites was 450 m.

Line 314.  It is stated here that Visscher and Seeley (1982) reported a density of wild colonies of only 0.67/km2.   This is true; they found 11 wild colonies within the 16 km2 Arnot Forest.  However, they should have taken into account the fact that not all 16 km2 of this forest were searched.  Actually, only about 67% of the forest was searched, so a better estimate of the density of wild colonies in this forest is 1.00 colonies per km2.   This estimate is supported by the findings of later studies; they have consistently yielded estimates of colony density of 1 colony/km2.  See Seeley (2007) and Seeley et al. (2015).

In the references, all the references to Seeley should indicate Seeley, T.D.   At present, it sometimes says Seeley, T. and sometimes Seeley T.D., but they are the same person, and he goes by T.D. Seeley.
Additional comments: You have done an excellent job of collecting your data and in presenting your findings.

Your graphics are first rate, and I like the use of the yellow footprints to denote the track along which you moved during your bee hunting.

Thank you for conducting this pioneering work!


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

Input:
Title: THE NEGLECTED BEE TREES: EUROPEAN BEECH FORESTS AS A HOME FOR FERAL HONEY BEE COLONIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Kohl & Rutschmann led an excellent study that characterizes the densities of feral honey bees in forested areas in Germany. In the introduction, the authors give an informative and well-written background section with detailed citations, which gives the reader the necessary information to understand the relevance of the study and the need for the data that they collected. The language used and structure of the paper is clear.

The goal of the study was to estimate the density of feral honey bee colonies in forested areas using two different methods and understanding more about the role of swarming in the dynamics of these feral colonies. The authors clearly report their results about the 3 aspects of the study.

We only have minor comments that may help clarify some points throughout.
Experimental design: Robust experimental design. Methods are explained in a clear manner for the most part. Please see comments below about some aspects of the figures requiring clarification.
Validity of the findings: Conclusions are well stated. Results are extremely valuable as baseline data for monitoring feral European honey bee colonies in their native range. This study challenges the notion that feral honey bees disappeared in Europe after the introduction of varroa mites.
Additional comments: Some minor comments:

* L13-14: Authors should note and cite the study by Thompson et al 2014 that report virus levels on feral colonies in the UK.

* L19-20: This sentence is unclear. We suggest: “Further, we estimated flight distances of scout bees from swarms after decoding dances near forest edges”.

* L92-94: Microsatellite genotyping for colony density estimation requires markers that are unlinked.

* L96-98: Besides the possible lack of ability to detect low colony densities, the problem of using genetics for these estimates is that managed and feral bees are not necessarily isolated populations. Therefore, the power to detect colony densities as if these were separate “populations” is probably low.

* L103: What do you mean by legal status?

* L156: Consider rephrasing to “foraging honey bees exhibit site fidelity”

* Figure 2. It is unclear why figure 1 and 2 were included. Please clarify these two versions of the results of beelining in Hainich.

* L300 - Please clarify low densities compared to what.

Margarita López-Uribe
Chauncy Hinshaw


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: 2D VERSUS 3D REAL TIME ULTRASOUND WITH LIVE XPLANE IMAGING TO VISUALIZE AORTIC AND DUCTAL ARCHES: COMPARISON BETWEEN METHODS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a prospective observational study evaluating the feasibility of using 3D Real Time Ultrasound with live xPlane imaging for visualization of the aortic and ductal arches during fetal echocardiography and comparing this technique to the standard 2D approach.

Main issues:
1-	Manuscript needs professional English editing
2- 	Avoid using the term cardiac malformations thoughtout the text. “cardiac anomalies” would be a better fit.
Experimental design: 1-	Feasibility of 3D real time ultrasound with live xPlane imaging for visualization of aortic and ductal arches was established by Xiong et al. This article mainly added the analysis of various factors (fetal position, movements, operator experience) affecting successful acquisition of arches views and the difference in time needed between 2D and Xplane imaging.
This needs to be stressed in the objectives of the study.

“Xiong Y, Chen M, Chan LW, Ting YH, Fung TY, Leung TY, and Lau TKA 2012aA A novel way of
visualizing the ductal and aortic arches by real-time three-dimensional ultrasound with live xPlane
imaging. Ultrasound Obstet Gynecol 39:316-321A 10A1002/uogA9081”

2-	The authors mentioned that the study was conducted between March 2015 and December 2016 and included all pregnant women at time of fetal anatomic survey with no indication for fetal echo. My question is how was these 114 women selected?
During almost 22 months only 114 women scanned? Please explain in methodology section.

3-	Discussion section of the abstract is a repeat of what was already mentioned in the introduction. This section should focus on value of your results.
Validity of the findings: The findings are useful in understanding the limitations and various factors affecting (fetal position, movements, operator experience) affecting successful acquisition of arches views and the difference in time needed between 2D and Xplane imaging.
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: 2D VERSUS 3D REAL TIME ULTRASOUND WITH LIVE XPLANE IMAGING TO VISUALIZE AORTIC AND DUCTAL ARCHES: COMPARISON BETWEEN METHODS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Comments on the paper “2D versus 3D Real Time Ultrasound with live xPlane imaging to visualize aortic and ductal arches: comparison between methods” by Stefania Dell'Oro et al.
The authors evaluated 114 patients between 18+1 to 21+6 weeks of gestation using normal 2D ultrasound and a commercially available technique based on live 3D ultrasound (XPlane)
•	No significant differences were observed, significantly longer period of time to obtain the required planes with XPlane .
Experimental design: •	No abnormal cases were included.
•	The potential benefits of the new technique cannot be assessed in this study
Validity of the findings: •	No real benefit with the new technique can be achieved
•
•	The potential benefits of the new technique cannot be assessed in this study
Additional comments: •	No significant differences were observed, significantly longer period of time to obtain the required planes with XPlane .
•	No real benefit with the new technique can be achieved
•	No abnormal cases were included.
•	The potential benefits of the new technique cannot be assessed in this study
•	The results showed that in normal pregnancies  for operators level 1 and 2 2D ultrasound is still the standard for cardiac evaluation


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: INCLUDING AUTAPOMORPHIES IS IMPORTANT FOR PALEONTOLOGICAL TIP-DATING WITH CLOCKLIKE DATA, BUT NOT WITH NON-CLOCK DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: See General Comments Below
Experimental design: See General Comments Below
Validity of the findings: See General Comments Below
Additional comments: This is a fine, succinct discussion of an important issue (whether morphological characters should be "filtered" before phylogenetic analysis).  It should be publishable in PeerJ after the following minor comments are addressed.

OTUs - Recommend inserting (=terminal taxa) on first use of term OTU.

>These corrections are options in MrBayes and can be implemented in Beast2 XML
Can also be done in BEAST 1.

>Linear regression of tip age against the root-to-tip distance in a parsimony analysis (the number of morphological steps on all branches leading to a tip) indicated that time and parsimony branchlengths were not correlated.

This approach has been used before, e.g. in Path-o-gen / Tempest by Rambaut, which probably would be good to cite here.

>tested on MrBayes versions 3.1.2 through 3.2.6
Might be fair to point out that “coding=informative” is now no longer listed in the command manual (though the code is still there) - perhaps in recognition of potential issues.

Useful reference to cite: "Why remove autapomorphies?" by Yeates in Cladistics 1992


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: INCLUDING AUTAPOMORPHIES IS IMPORTANT FOR PALEONTOLOGICAL TIP-DATING WITH CLOCKLIKE DATA, BUT NOT WITH NON-CLOCK DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well-written (I've picked up a few minor typos) and the analyses are well-documented in the Main Text and extensive supplementary materials.
Experimental design: The paper is restricted to a single "real world" dataset, plus simulated datasets - to what extent other "real datasets" would behave similarly is an interesting, open question. However, I think the detailed analyses of the eureptile dataset are sufficient to cover the issues of concern.
Validity of the findings: As above, it would be interesting to see how other datasets would behave, but the results presented are certainly valid for the datasets being analysed.
Additional comments: I have made quite a few comments/suggested changes on the marked up pdfs (main text and supplementary info) that I would like the authors to address, but these are relatively minor. Otherwise, I think this is an interesting, timely paper that will be of broad interest to systematists, palaeontologists etc.


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

Input:
Title: INCLUDING AUTAPOMORPHIES IS IMPORTANT FOR PALEONTOLOGICAL TIP-DATING WITH CLOCKLIKE DATA, BUT NOT WITH NON-CLOCK DATA
Review round: 1
Reviewer: 3

Output:
Basic reporting: No Comments
Experimental design: No Comments
Validity of the findings: No Comments
Additional comments: This is a brief, but important and consequential paper on the behavior of various tip-dating methods in the presence of autapomorphies. It is very important to demonstrate the effect on estimated clock-rates and relative lack thereof for estimated dates. Similarly evaluating the Mk_parsinf correction is a necessary advancement for researchers using these techniques. I have essentially no revisions needed 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: VARIATION IN THE DIVERSITY AND RICHNESS OF PARASITOID WASPS BASED ON SAMPLING EFFORT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clear on the main questions that are being answered by this study, and although the writing is a little clunky in places, the paper is quite concise overall.
One section that I would like to have more detail on is where the barcoded material was submitted, as these should be linked to this publication, and direct other users to identify the morpho-species in the same manner.
Experimental design: The study largely describes the outcomes of an exploratory pilot study, in a very poorly studied system so I believe the sampling design was suitable.
Validity of the findings: The value here is clarity on the significant effort that would be required to characterize biodiversity of this group. Given that despite substantial effort,  sampling was still inadequate to compare sites or seasons there is little more that can be said, and indeed the authors do not overly speculate.
Additional comments: I think this kind of information is valuable to help any future studies calibrate their expectations when designing studies, especially if they wish to target specialist groups like this study did. On the other hand, of course, given how incomplete the records appeared to be, its difficult to guess how much more time sampling is needed.
The only main flaw I felt the paper has is that it focuses on species rarity as the reason for species richness accumulating so slowly. However, the total number of individuals caught was very low as acknowledged, and therefore this is actually an issue of "detectability" (see reviews like Guillera-Arroita, 2016). Whilst Malaise traps may have been more successful elsewhere, they may not in fact be well-suited to capturing these species, and you acknowledge that other kinds of traps may have increased the rate of species' recovery. The proportion of species that are then hard to observe because they are rare can only really be judged in light of that. This distinction doesn't really alter the study's finding or conclusions, but I would still recommend the authors consider updating a few sections of the discussion to reflect these differing perspectives.


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: VARIATION IN THE DIVERSITY AND RICHNESS OF PARASITOID WASPS BASED ON SAMPLING EFFORT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written and clear (or rather, what is presented is clear; there are significant gaps (see below).  Figures are well designed, and data were easy to access.
Experimental design: The research question is well thought out and presented.  The work appears to have been well executed.  As to methods: PeerJ wants “Methods described with sufficient detail to replicate”.  That is not done here; but that doesn’t matter, because that is not actually how scientists write, or should write.  (Replication detail belongs in online supplements, or at protocols.io, etc; it doesn’t belong in papers where it makes readers suffer.  Of course, I realize that not all will agree with me on this.)  What *does* matter is enough detail for readers to understand and interpret the results; and here, this manuscript falls short.  See under “General comments” for specific examples of where we need to know more.
Validity of the findings: I believe the results are robust and well analyzed, although given shortcomings in the Methods I’m unable to be completely sure.  The Discussion fell flat, to me; there was absolutely nothing said about why the diversity estimators behaved so differently, or about whether power constraints account for the lack of effects of environment.  The paper would be much more useful with that; the current version essentially ends with “we didn’t find many of the species and aren’t sure by what fraction we underestimate diversity”.  It’s possible to do more.
Additional comments: By line number:

57 “numerous impediments block” – a bit awkward. What about “there are numerous impediments to”?

67 Is this known global diversity or likely global diversity?  Seems very low for the latter; make clear.  And I’d be tempted to say “much more diverse” than vertebrates, or maybe give a vertebrate diversity number, to make a stronger point here (vertebrates ~50,000 max, I think?)

117ff I would encourage the authors to rewrite the Methods (at least) in the active voice.  It’s shorter, more engaging, clearer; we are moving past our passive-voice convention.

125 I’d like to see coordinates for the two study sites, not just for the broader study area.

133 What were the other traps, what differences were there between trap types, and did you take this into account in the analysis? Were trap types assigned randomly to sites/locations?

135 I doubt that trap placement was “random”; I suspect it was actually “haphazard”.  This is fine; just describe it as such!  If I’m wrong and it actually was random – how was randomization accomplished?  Randomly generated coordinates?

136 What is a “flight path” for a parasitoid wasp, and how were such identified?

137 I find this a bit unsatisfying without knowing anything about the microhabitats in question.  What were they, how were they identified, how many traps in each, etc?

152 No methods for DNA barcoding?  How was it done, was it done for every specimen or just for ones where they was doubt, did you always find a database match, what did you do with the sequences, etc etc?

158-160 This is a little superficial.  What is Nikau?  Why is number of CWD the right metric, not estimated total volume (two short pieces aren’t twice as much CWD as one long piece)?  If none of the cover types involve living plants, then why did you also need to identify the plant species present?  Did you identify all plants present or just dominants?

171 I think it would be worth specifying what the software does with this parameter – does it mean that anything with fewer than 10 observations is ignored?  That would have a huge effect.  Does it mean something else?

182 I don’t understand this – the environmental data weren’t factors, so how were they involved?  I assume they were, since you standardized them. Ah, I see in the next paragraph, some kind of “Euclidean distance to environmental data” – but I don’t understand that.  Also note, you can’t standardize environmental variable (iii) because “the plant species present” doesn’t have a mean or standard deviation – unless you mean the *number* of plant species present?

193 I’m not familiar with this technical sense of “denuded” and I wonder if other readers might be like me.

199 I’m not sure what relationship this has to 187. Are they redundant?

208 I assume you mean morphospecies?  Otherwise, “only 10% of the species were identified to the species level” doesn’t make much sense.  In the Discussion, you should probably comment on the likelihood that the true diversity is higher than the number of morphospecies, since there are cryptic species in parasitoids.

209 If you are reporting a correlation, you want the correlation coefficient (r), not the coefficient of determination (R2).

220-221 How many of these were singletons and doubletons?  I don’t think it means much if some species were caught at only one site, if there were only a few captures of them – in other words, a site X captures G-test would not be significant.

225 (Figs 1-2). I don’t know enough about the estimators, I guess, because I don’t understand how they can be other than strictly increasing as you add more samples.  ICE seems especially problematic in this sense.  I hope in the Discussion this is something that will be addressed.

229 I don’t understand this.  From which two traps?  Random pairs of traps?  For all pairs of traps, as at 198?

236 If this means what it seems to, isn’t this result completely trivial?  Of course individuals for Jan + individuals for Feb > individuals for Jan; mathematically it can only be equal or greater.  I would simply delete this, unless I’m missing its meaning (in which case, rephrase).

266 The differences among estimators need much more discussion.  For the same data, there was a two-fold difference among estimators. Not only that: at least one (ICE) gave counterintuitive results in which, for some sampling intensities, adding more samples led to *lower* diversity estimates.  So: what is known about the different performance of these estimators?  Is one known to be most conservative?  How do their assumptions differ, and does the assumption set of one estimator fit your situation better?  How might one proceed to gather further, or different, data to resolve these differences?  I would see this one phrase, “and the statistical estimator used”, expanded to at least one long-ish paragraph, if not more.

269 It would be interesting to know a bit more about the power you had to detect such effects if they were present.  This is phrased appropriately – you can’t reject the null – but it would be useful to know whether you can place any bounds on the effect sizes.  You may not be able to do a lot here, but I suspect given the very high inter-trap variability, power is low.  Which is part of your point!  Can you, for example, estimate variability for the traps that are most similar in terms of environment, and use that to suggest how strong an environmental effect would have to be to stand out against that background?

302 Since there were still many singletons, and thus many unsampled species, the inventory was not “exhaustive” (although it was probably exhausting!).

314 I don’t think this follows at all.  Just because a species is native to NZ does not mean that it will be resident in every habitat type.  In fact, if you thought this was true, you would not have attempted to estimate effects of environment on diversity or species representation in your trapping data!  I would simply delete this sentence.  Your singletons could very well be “tourists”.


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: VARIATION IN THE DIVERSITY AND RICHNESS OF PARASITOID WASPS BASED ON SAMPLING EFFORT
Review round: 1
Reviewer: 3

Output:
Basic reporting: All metrics of "basic reporting" meet high quality standards.
Experimental design: The research reported answers a well defined research question that has relevant and meaningful impacts on our understanding of (what is likely to be) perhaps one of the most diverse families of Metazoans in the world.

 I found that the experimental design, statistical analyses and overall questions were all performed very capably.
Validity of the findings: I found that the experimental design, statistical analyses and overall questions were all performed very capably.

One suggestion I would make is that the authors elaborate briefly in the Conclusions and Recommendations on the importance that the continued deployment of Malaise traps has for the communities understanding of ichneumonid diversity (if, they in fact feel this way).  To me, I worry that a cursory reading or reporting of this study once published might be that, “Malaise traps don’t work” when in fact, MORE Malaise trapping is needed (and people to sort their contents, if we are ever to more fully understand this diverse family!
Additional comments: The authors investigated how variation in sampling effort affected the observed and estimated species richness of Ichneumonid parasitoid wasps.  While it is “well known” that ichneumonids are both diverse and often captured in Malaise sampling, there is a lack of a synthetic analysis of how well the common use of this common trap type actually captures the diversity of organisms present.  Turns out, not well.

I have a couple of minor suggestions that I would suggest they deal with prior top publication.

SPECIFIC SUGGESTIONS

Line 249 – “3-month summer period”.  To someone unfamiliar with a New Zealand summer – what proportion of the “flight period” might this be?

Line 260 – “Our aim….” Rather than “the aim of this paper. “

Line 270 (ish) – perhaps useful to insert some comment here regarding the likely even greater under-representation of total diversity in the tropics.

Line 270 ish – We recently (https://doi.org/10.1139/facets-2016-0061) used Malaise trapped parasitoids to test for anomalous latitudinal patterns of diversity in parasitic Hymenoptera.  We noted that in no single site, did any of the diversity and sampling relationships reach an asymptote.

Line 302 – “14 years” rather than “many”.

Line 152: “DNA barcoding was utilised to ensure females and males were correctly associated.” –I have two further suggestions regarding this sentence.  The first is that you report the number of times that this strategy was completed/necessary.  Readers outside of the immediate taxonomic community would likely be unaware of how frequently such information is unknown and that such a strategy would be required.  The second recommendation I have is to report the DNA barcode BIN (Barcode Index Numbers) associated with the species you including your matrix.  These BINS serve as interim species name proxies until (and if) the morphospecies you delineate here are formally described.  The frequency of interim species epithets is unavoidable in many arthropod groups (and in parasitoids specifically).  However, I would strongly urge you to avoid the use of “sp.1” as it conveys no information outside of the current study.  The unique BIN names can serve this purpose.  If not all “species” have been barcoded and have BIN details, then I would suggest using the surname of the taxonomist to create an alpha numeric (NAME001).  This will at least permit future readers and users of your data to consider and contextualise your findings.  Otherwise, they join the long queue of locally specific and incomparable “sp.1” ‘s in the 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: SERPIN FUNCTIONS IN HOST-PATHOGEN INTERACTIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The review article by Bao et al. is a timely and comprehensive summary on the serine protease inhibitor family of serpins. The authors particularly focus on the functions of these molecules in host-pathogen interactions, which make this review unique and interesting for the field.
However, prior publication some issues should be addressed.
Experimental design: n.a.
Validity of the findings: n.a.
Additional comments: -	A phylogenetic tree of different serpins from different species reported in this manuscript should be presented.
-	The cartoon in Fig. 2A should be improved. Besides the rather simple scheme a more sophisticated presentation of molecular structures explaining the inhibitory mechanism is needed.
-	The text contains many errors and typos, which should be corrected (e.g. line 94: delete ‘of’; line 103: ‘A’ study by …; line 125: ‘bacterial’; line 150: ‘Cucurbita’; line 154 ‘found to’; line 156 ‘thaliana serpins’; line 160: ‘and Inflammation’; line 178: ‘may be able’; etc. etc..


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

Input:
Title: SERPIN FUNCTIONS IN HOST-PATHOGEN INTERACTIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article by Bao et al. is clear and well written. The subject of the article is rather interesting and it provides an interesting overview of the role of serpins in immunity of both vertebrates and invertebrates. Overall, the article is well-referenced. The article contains only one figure illustrating a common serpin 3D structure from the archetype a1-Antitrypsin. I suggest to replace this structure by a figure showing the interaction of the serpin with its targeted protease and the authors should also mentioned that serpin can either acts as a substrate (resulting in a cleaved inactive serpin) or a covalent inhibitor (refer to Silverman et al., JBC 2001). The author should provide a graphical representation that summarizes serpins’ functions in immunity separating the host on one hand and the infectious agents on the other hand.
Minor comments: I haven’t noticed major grammatical errors but many spaces between two adjacent words are missing (line 80 aresult, line 154, foundto, line 160, serpinsin andinflammation etc.). I do not known whether these errors are in the initial version or only in the uploaded version.
Experimental design: The authors used Pubmed and Google scholar tools and serpin, serine protease, host-pathogen interaction infection and inflammation as keywords. They might have missed some interesting data that should be found using antibacterial or antimicrobial as additional keywords. Indeed, this review is mainly focused on how serpins can regulate host or on the other hand, pathogen proteolytic activities but some serpins have been described to have antibacterial activities independently of their inhibitory site.
Validity of the findings: The finding are rather interesting but as mentioned in 1., the clarity of the message would be improved with a figure summarizing major findings. Some information is still missing (see below).
Additional comments: Mechanism of serpin inhibition:
Please indicate the presence of a noninhibitory pathway that may influence the stoichiometry of inhibition and that depends on the couple serpin/protease considered. Please indicate that some serpins are secreted and some are intracellular which may also have some impact on their targeted proteases and depending on the mechanisms underlying the pathogenicity of infectious agents. Also, indicate that some co-factors are sometimes needed such as glycosaminoglycans including heparin for HCII, PCI, ATIII for example, knowing that heparin is secreted by mastocytes, which are involved in response to infection and inflammation.  Please indicate that the mechanism of action of host serpins against pathogens is usually indirect (through the inhibition of microbial proteases which are major virulent factors that trigger dissemination and invasiveness of pathogens) but it can also have a direct effect (interaction and subsequent lysis of pathogens).
Please include a paragraph in this section on other effects (induction of expression of host antimicrobial peptides, cytokines)
Below are some suggested articles:
-Serpin-14 negatively regulates prophenoloxidase activation and expression of antimicrobial peptides in Chinese oak silkworm Antheraea pernyi. Kausar S, Abbas MN, Qian C, Zhu B, Sun Y, Sun Y, Wang L, Wei G, Maqsood I, Liu CL Dev Comp Immunol. 2017 Nov;76:45-55. doi: 10.1016/j.dci.2017.05.017. Epub 2017 May 22.
-Antibacterial activity of serine protease inhibitor 1 from kuruma shrimp Marsupenaeus japonicus. Zhao YR, Xu YH, Jiang HS, Xu S, Zhao XF, Wang JX. Dev Comp Immunol. 2014 Jun;44(2):261-9. doi: 10.1016/j.dci.2014.01.002. Epub 2014 Jan 9.
-Protein C inhibitor--a novel antimicrobial agent. Malmström E, Mörgelin M, Malmsten M, Johansson L, Norrby-Teglund A, Shannon O, Schmidtchen A, Meijers JC, Herwald H. PLoS Pathog. 2009 Dec;5
-Ovalbumin-related protein X is a heparin-binding ov-serpin exhibiting antimicrobial activities.
Réhault-Godbert S1, Labas V, Helloin E, Hervé-Grépinet V, Slugocki C, Berges M, Bourin MC, Brionne A, Poirier JC, Gautron J, Coste F, Nys Y. J Biol Chem. 2013 Jun 14;288(24):17285-95. doi: 10.1074/jbc.M113.469759. Epub 2013 Apr 24.

Conclusion
Please include one or two sentences about functions related to peptides derived from serpin RCL and others that may have some additional bioactivities including some related to the modulation of the response to infections (antibacterial peptides and immunomodulatory activities). Indeed, the interaction of the serpin with its targeted protease leads to a covalent bipartite complex together with the release of a peptide of about 50 amino-acid residues resulting from the cleavage of the RCL and the activities of these peptides have been poorly explored.
Reactive Center Loop (RCL) Peptides Derived from Serpins Display Independent Coagulation and Immune Modulating Activities. Ambadapadi S, Munuswamy-Ramanujam G, Zheng D, Sullivan C, Dai E, Morshed S, McFadden B, Feldman E, Pinard M, McKenna R, Tibbetts S, Lucas A. J Biol Chem. 2016 Feb 5;291(6):2874-87. doi: 10.1074/jbc.M115.704841. Epub 2015 Nov 30.
Antimicrobial activities of heparin-binding peptides. Andersson E, Rydengård V, Sonesson A, Mörgelin M, Björck L, Schmidtchen A. Eur J Biochem. 2004 Mar;271(6):1219-26.


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: PREDICTING PINUS MONOPHYLLA FOREST COVER IN THE BAJA CALIFORNIA DESERT BY REMOTE SENSING
Review round: 1
Reviewer: 1

Output:
Basic reporting: All issues are satisfactory.
Experimental design: The sampling design for the reference data is not reported.  Failure to use a probability sampling design invalidates all the analyses.

The prediction/classification techniques must be described in much greater detail and some justification with references for data characteristic of this study must be included.

The apparent “pixel counting” method for estimating areas is a biased procedure because it does not account for classification error.  Uncertainties associated with the area estimates should be included.
Validity of the findings: Until the methods are described in more detail, the sampling design for the reference data is provided, and an unbiased procedure for estimating area is used, the validity of all results are questionable.
Additional comments: GENERAL COMMENT:
The overall topic of the paper is timely and relevant, and a well-written paper using statistically rigorous methods would make an appropriate contribution to the literature.  However, the paper in its current form lacks rigor and suffers from considerable incorrect and inappropriate use of terminology.

Because remotely sensed spectral data measure only the intensity of reflected light at different frequencies, these data do not “detect” or “establish” any ground conditions.  However, variables based on these intensities have been shown to be good PREDICTORS of ground conditions.  This is not just a subtle, semantic issue, because terms such as “detect” and “establish” fail to connote the uncertainty associated with the predictions.  Further, if there were no such uncertainty, then assessment of accuracies based on confusion matrices would not be necessary.  Lines 22, 26, 39, 91, 06, 100, 104, 198, 242.  In nearly all these cases, either “predict” or “estimate” would be more correct terms.

All of the prediction and/or classification techniques must be described in greater detail and supported with appropriate references.

The authors must describe their methods for assessing areas.  In particular, constructing a map and adding the areas of pixels classified into a particular class, a practice characterized as pixel counting, is biased because it does not take into account classification error.  See Olofsson et al, 2013, Remote Sensing of Environment 129: 122-131.   In particular, what is the uncertainty associated with the authors’ area estimates?  Lines 37, 196.

The “real values” to which the authors refer at line 164 are more generally characterized as “reference data.”  What sampling design was used to acquire these data?  In particular, if a probability sampling design was not used, then all the results based on the confusion matrix analyses are incorrect.  See the previous Olofsson et al, 2013 reference.

The first dictionary definitions of terms such as “high”, “low”, “over”, “under”, etc, refer to height, altitude, or vertical position, whereas the first dictionary definitions of terms such as “large”, “small”, “greater”, “less”, etc, refer to size or amount.  Despite widespread use to the contrary in the applied literature, perhaps the latter terms can be used in scientific papers to refer to size or amount.  In particular, if terms such as “higher” or “lower” are used to refer to altitude, they should not also be used to refer to amounts or spatial resolution of imagery.  Lines 95, 104, 145, 200, 202, 224, 266, 282,

Avoid the use of subjective terms such as “best” whose criteria are not given.  Lines 218, 221,

SPECIFIC COMMENTS:
Line 37:  What is meant by “probably”?

Line 73:  What is meant by “generalized”?

Line 104:  Change “higher” to “finer.”

Lines 150, 198:  Clarify these statements.  For someone unfamiliar with the technique, these statements are meaningless.

Line 169:  In a paper with statistical content, the term “significant” should be reserved for reporting the results of a formal statistical test of significance in which case both the name of the test and either the P-value or the alpha-level should also be reported.

Lines 183, 185:   What is a “significant variable”?  Is it that the mean of the variable is statistically significantly different from 0?

Line 196:   What is meant by “potential”?

Line 228:  This is a very small R2.

Line 235:  What is meant by “efficient” and what is the evidence to support the assertion?

Line 278:  How can temperature be “wide” or “narrow”?


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: PREDICTING PINUS MONOPHYLLA FOREST COVER IN THE BAJA CALIFORNIA DESERT BY REMOTE SENSING
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please see attached PDF.
Experimental design: Please see attached PDF.
Validity of the findings: Please see attached PDF.
Additional comments: Please see attached PDF.


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

Input:
Title: PREDICTING PINUS MONOPHYLLA FOREST COVER IN THE BAJA CALIFORNIA DESERT BY REMOTE SENSING
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: The stratified random sampling design is appropriate, but stratified rather that simple random estimators must be used with the acquired sample data.
Validity of the findings: The accuracies and the area estimates are not correct.
Additional comments: GENERAL COMMENTS:
The paper is much improved, although several wording revisions are necessary and one technical error must be corrected.

The technical error is that the authors used stratified random sampling to acquire their reference data, but they used simple random sampling estimators to assess the confusion matrix data.  For each map class used as a stratum, the proportion of the study area in stratum must be calculated as the proportion of pixels assigned to the class/stratum and used as a stratum weight.  The authors should carefully read and follow the examples in the Olofsson papers already cited.

Figures 4, 5, and 6 are not very meaningful when all the response variables are 0 and 1.  An alternative is to order/sort all the data by the predicted probability.  Then aggregate the pairs of observations and predictions into groups of a selected size, perhaps 15-20.  Calculate the mean of the observations and the mean of the predictions in each group and graph mean observations versus mean predictions.  If the predictions are good, the graph should fall along the 1:1 line.  Although the study is quite different, see Figure 2 in Remote Sensing of Environment 114: 1017-1025.

The first dictionary definitions of terms such as “high”, “low”, “over”, “under”, etc, refer to height, altitude, or vertical position, whereas the first dictionary definitions of terms such as “large”, “small”, “greater”, “less”, etc, refer to size or amount.  Despite widespread use to the contrary in the applied literature, perhaps the latter terms can be used in scientific papers to refer to size or amount.  Technical writing consultants strongly recommend using terms with only one meaning or definition, or if a term with multiple definitions is necessary, then the use the first definition.  A recently submitted paper used the terms “high resolution”, “high biomass”, and “high altitude” all in the same sentence.  That might be extremely confusing for a reader with limited English language expertise.  Lines 27, 235, 260, 292, elsewhere.  This comment was provided for the previous version of the paper.

When uncertainty is involved, used terms such as “predict” or “estimate” rather than “determined” (139, 191, 208, 306), “obtained” (140), “identified” (163), “calculated” (194, 199), “measured” (212), elsewhere.

SPECIFIC COMMENTS:
Line 29:  Change “proved” to something like “demonstrated” because rarely is anything actually proven in science.

Line 79:  Perhaps “three times finer resolution.”

Line 145:  Is “indices” the plural of “index”?

Line 173:  Should “data” be “predictions.”

Line 292:  Perhaps, “very large accuracies.”


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: PREDICTING PINUS MONOPHYLLA FOREST COVER IN THE BAJA CALIFORNIA DESERT BY REMOTE SENSING
Review round: 2
Reviewer: 2

Output:
Basic reporting: Please see attached document.
Experimental design: Please see attached document.
Validity of the findings: Please see attached document.
Additional comments: Please see attached document.