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: COMPARISON OF COMPLEX NETWORKS AND TREE-BASED METHODS OF PHYLOGENETIC ANALYSIS AND PROPOSAL OF A BOOTSTRAP METHOD
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall the English was clear and unambiguous. However, there were many terms that I was unfamiliar with that need in-text explanation (beyond citation to a reference), specifically: "betweeness", "assortativity", "auto-similarity", “removed edges”, and "modularity". This is an interesting and new method, and therefore the authors need to take cognisance that this will be interesting and new to many readers - please help us with explanations readily at hand in the text.

There are many many different types of networks. I strongly encourage the authors to briefly set-out in the Introduction how this type relates to the other types - even if it is to say that this is completely different (then how is it different). There is a lot of confusion out there about networks, and so you want to highlight to the reader that this is a new type (not some knock-off adjustment of, for example, NeighbourNet). This does not need to be an extensive review of network types, but just an alert to the reader about how your method is different.

Another angle on this is why and when should researchers use this method over the others - it strikes me that this method is good at picking up groups when there are very deep phylogenetic divergences. Other methods, like NeighbourNet, usually fall apart (or rather descend into spider-web black hole) when there are deep divergences and homoplasies are present. This point bugged me for quite a while reading the manuscript - it was only when I ran a few additional network analyses did the benefits of your method become clear (I do have to put a proviso that my analyses were handicapped by the use of the similarity matrix, and I'm not entirely clear as to how this was calculated).

The raw data has been shared, although the similarity matrix lacks taxon labels - this makes it difficult to assess the results of this study with other analyses (for example, I ran a NeighbourNet on the distance matrix but could not relate it to the final figures as there were no labels). In addition, the phylogenetic tree analyses (tree and bootstrap tree sample) have not been included – please add.
Experimental design: I have a few concerns that need to be addressed.
1. Similarity Calculation
The authors use a protein sequences to establish the relationships between sub-phyla of Basidiomycota fungi. I have not used protein sequences before, but it seems that there has been substantial variation in the selected region/s across the lineages. The alignment of these protein sequences is very messy - for example, the protein sequences range from 519 to 2066 amino acids residues. I have a concern about how this affects the calculation of the similarity matrix. The first step of the complex networks approach is the construction of a similarity matrix and this is the basis for all subsequent steps. The authors state that the used a BLAST search. This does not explain how gaps are dealt with, are similarities calculated pairwise or  across all samples (i.e. gaps are deleted across the entire alignment). As the way that the distances are caculated can dramatically influence the distance values, this needs to be clearly explained.
For example, the distance matrix calculated by PAUP for the NJ analyses was likely very different fom the distance matrix produced for the first step of the complex network calculation. I am pretty sure of this as when I generate a NJ tree based on the author-supplied distance matrix, it does not have the three clear clades as shown in Fig. 3b. Thus, is comparing the NJ tree and the network results a fair comparison as it is not an algorithm superiority, but rather how gaps are dealt with between the different methods.

2. Lack of support for clade C in phylogenetic analyses: a rerooting artefact
Trees were rerooted in FigTree. This is a common mistake and should NEVER be done. Support values are for branches, but in the NEWICK format are stored at nodes. By rerooting the relationship between nodes and branches is changed and thus the support values can be shifted up or down onto a different branch! Given the very long branch leading to clade C in all analyses, it should be well-supported (just from eye-balling, but medium levels of homoplasy could also be driving this). Rooting has to be done on each bootstrap sample and on the representative tree before combining this information. I am against rooting in this setting anyway – it is unlikely to actually capture the correct ancestor-descendent relationship. Rather pesent unrooted trees. Even better would be to show the consenses networks of the bootstap sample (Holland et al. 2004 - Using consensus networks to visualize contradictory evidence for species phylogeny) – although most phylogeneticist still seem to find this heretical.
3. Software
What software was used to conduct the complex network analyses – i.e. if I wanted to use this analysis, I don’t think I could use you methods to figure out how to do this.
4. Complex networks testing
Something for the authors to consider for another paper – simulate some data under a range of scenarios, from tree-like to non-tree-like datasets, and demonstrate how the algorithm performs. Even better would be  to use datasets developed for testing other networks.
Validity of the findings: The complex network approach detects the same clades as found in the phylogenetic trees. As I suspect that once the rerooting issue is sorted, all clades will have high phylogenetic support, then the authors have demonstrated that the method detects the same clades. What now? How is this an improvement on the current state? The power of networks is that they can show non-bifurcating patterns for further explanation of evolution (or conflicting pattern in the dataset). However, the authors do not address the intra-community connections – what do these connections mean? How should we interpret them? The lines between taxa seem to simply indicate a relationship – but what kind of relationship? This needs to be discussed.
Additional comments: This is an interesting manuscript, but I was at times scratching my head – not through any error in the manuscript, but through my reasonable ignorance (it is a “new” approach afterall). Please make some effort to provide more “road signs” explaining the terms and reasoning that you followed.
Some minor in-text comments:
Line 39: “disclosure” - this does not seem to be the right word.
L44: Remove “have”
L46: Remove “have”
L90: Please explain “evidence of existence”
L94-101: I found this section very confusing – please include a short introduction as to why you did this.
L95: “smallest, largest, mean values” of what?
L133-137: What was the threshold criterion?
L152: The symbols for the math notation have been removed and replaced with squares.
L160: Please describe the “community detection” a little bit more.
L190: This concept of “removed edges” is used fairly often, but I don’t get it. Please find somewhere to provide a brief explanation of the thinking behind this.
L282: What is a “symmetric” matrix of aligned sequences?
L282: Previous stated max length of sequences was ~2000, now the alignment is ~5000. Dealing with gaps, yes? Please make this clear...
L288-290: What is the point in reporting this information – it is in the Figure.
L313: Odd sentence, meaning unclear.
L398-406: This is the only section on network interpretation, and it is quite vague. Please expand and make relevant in light of your network results.
L416: Is this method actually bootstrapping. It strikes me to more along the lines of Monte Carlo resampling.
L430: A range of alpha values is selected to compare network support values with those of the trees. The alpha values affect the network support values – so how would one go about selecting an alpha value in the absence of tree information...
Table 3: Again, I don’t understand this concept of “removed edges”
Fig 2: The qualiquantitative analysis seems to be a loose thread in the manuscript – it is not clearly related back to the phylogenetic or network results. Please highlight more clearly to the reader why this was an important analysis.
Fig 5&6: As these share the same x-axis, consider merging into Fig 5a and 5b.


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: COMPARISON OF COMPLEX NETWORKS AND TREE-BASED METHODS OF PHYLOGENETIC ANALYSIS AND PROPOSAL OF A BOOTSTRAP METHOD
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this manuscript, Goes-Neto and collaborators apply network methods they have been developing over the past few years to a dataset of 42 chitin synthases from Fungi, in order to produce a phylogeny of these sequences, and then compare this phylogeny to ones built with more classical methods (parsimony, NJ, ML and Bayesian). They also improve their previous protocol and implement robustness measures by ‘rewiring’ the adjacency matrices that are used for their networks.  Professional English is used throughout the text, and introduction and background are sufficient. Literature could be improved in some parts though. Especially, using networks to infer phylogenies has been suggested by others researchers before 2010, for instance by Atkinson et al. (doi: 10.1371/journal.pone.0004345). Manuscript structure conforms to PeerJ standards, raw data are adequately supplied, and figures are generally good (although resolution should be improved on Fig 7).
Experimental design: My main concern with this manuscript lies with the research question that is being investigated. In this paper. The authors show that network methods seem (see next paragraph) to be able to reconstruct phylogenies with results that are comparable to more standard (and time-consuming) methods. But their results only concern one dataset (chitin synthases) with relatively low phylogenetic diversity (Fungi), and there is absolutely no reason to believe that their methods will perform as well on other datasets. As much as I am convinced that network methods should definitely be more used by the evolutionist community (and especially the phylogeneticists), I strongly doubt that this paper will convince an already somehow reluctant audience. In order to do so (and again, I’d really like to see that happen), one would need a very thorough benchmarking of the method on simulated data, so that at least the true tree is known, which is not the case here. Chitin synthases evolution within Fungi is actively investigated, and the authors should definitely compare their results with published results (see for instance Goncalves et al., 2016, doi:  10.1186/s12862-016-0815-9). Moreover, benchmarking should be performed under conditions that are notoriously difficult for more classical phylogenetic methods: different tree shapes (balanced/unbalanced), different evolutionary rates (slow/fast), different sequence lengths (short/long), different sequence composition (unbiased/biased), and most of all varying relative rates (molecular clock evolution/non molecular clock evolution). From my experience, fungal chitin synthases are not even an especially difficult dataset for phylogenetic methods, which somehow renders the results less convincing. I understand this is a whole research program in itself, but, as is, I’m afraid this manuscript will not convince evolutionary biologists to use network methods for inferring phylogenies.
Unfortunately, the Materials and Methods part is very difficult to read, partly because it relies on notions that were previously published by the same team, but are not explained in the present manuscript. More problematically, some explanations are also missing. The only equation (line 152) somehow didn’t make it to the PDF I received, so I cannot assess what it means. Also, the network distance delta (line 155) is not explained. Network properties (lines 162-168) are given as is, and surely will not mean anything to the average evolutionist. Finally, the most prominent problem is that the actual method to build the phylogeny from the networks (lines 180-195) is hardly explained (but only provided as a reference to a previous article from the team), as is the newest part of the method (rewiring of the matrices).
Validity of the findings: As explained before, my main concern lies within the experimental design, but sadly the findings are not without flaws either. The authors chose to root their trees using midpoint rooting, but such a method only works with ultrametric distances, which biologically translates to sequences evolving under molecular clock (i.e. all sequences have accumulated the same amount of substitutions). Molecular clock however is generally not achieved for large time scales (such as the timespan elapsed since the ancestor of Basidiomycota for instance). Sadly, since the authors chose not to display branch lengths on their trees, one cannot know whether their data are actually under molecular clock, although it’s very likely they are not (again, see Goncalves et al.). As a result, rootings (and hence clades) are most likely devoid of biological meaning, which renders the following analyses much less relevant. Besides, there are much better ways to compare trees than just comparing whether the major ’clades’ actually correspond or not. Robinson-Foulds distances are classically used for such a purpose and it would be nice to actually have that kind of measures in the manuscript.
Additional comments: Again, I’d like to state that I’d really like for the authors to publish their methods, but in order to do so they’ll have to convince the phylogeneticists community, which for the moment is a bit wary of networks. For this reason, the authors might want to be a bit more thorough on the phylogenetic analyses and on the biological terms they use. For instance, building an NJ tree from mean BLAST distances (line 110) is definitely not the canonical method. Lots of more biological distances are available for such purposes (see the choice that is offered by any phylogenetic software for instance). Also, the term ‘midterm’ rooting’ (line 119) is never used, as is ‘terminals’ (line 288). Similarly, branch support values in Bayesian analyses are posterior probabilities, not bootstrap values (line 334). More generally, bootstrap has a very precise meaning in phylogenetics (i.e. building replicates of the initial character matrix by resampling sites), so the rewiring method that the authors propose should probably not be called ‘bootstrap’, but rather ‘robustness measures’. Finally, the manuscript is overly long in many places, and should be trimmed down in order to be more legible.
As a conclusion, I’m afraid I cannot recommend publication for this manuscript in PeerJ.


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

Input:
Title: COMPARISON OF COMPLEX NETWORKS AND TREE-BASED METHODS OF PHYLOGENETIC ANALYSIS AND PROPOSAL OF A BOOTSTRAP METHOD
Review round: 1
Reviewer: 3

Output:
Basic reporting: line 110 - was there any correction for multiple hits appplied?

line 136 - does this simply mean m_ij = 1 if S_ij > some threshold? If so, what is the threshold? Ooops nevermind, this is answered in step 3. It seems like steps 2 and 3 should be merged in the description.

line 152 is not intelligible in my pdf of the manuscript

page 13 "calculus" -> "calculation"

"These aforementioned characteristics strongly difficult the protein crystallization processs, which is a mandatory step before X-ray diffraction analysis." ->
"These characteristics make the protein crystallization process difficult"
Experimental design: The procedure for producing the sequence alignment needs to be described.
Validity of the findings: No comment
Additional comments: My background is in phylogenetics rather than machine learning. So perhaps, I am biased. Nevertheless, I have a hard time viewing this paper as an advance. The authors show that for the case of a hand-chosen chitin synthase dataset. Their method of building complex networks with random rewiring is able to recover the 3 major genealogical groups that are recovered by phylogenetic methods. However, the groups were recoverable using a very simple PCA analysis, so this does not seem to be a challenging task.

But the paper fails to explain why this is an advance. It is not clear at all how general the result is, and it is not clear to the reader why we need another method to identify the features of the data that seem to be easy to detect using any phylogenetic method.

I just didn't understand the point of the paper.  The method (including the new form of bootstrapping) seems to lack any statistical interpretation. So it is very unclear to me why someone would use this method.


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: INTER-DOMAIN MICROBIAL DIVERSITY WITHIN THE CORAL HOLOBIONT SIDERASTREA SIDEREA FROM TWO DEPTH HABITATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: see detailed comments
Validity of the findings: see detailed comments
Additional comments: This study investigates the Symbiodinium, bacterial and fungal diversity of 14 Siderastrea sidera coral colonies sampled from one reef across two depths using amplicon sequencing approaches. The study is interesting in many aspects; though it also needs extensive revision in many areas.  There are a number of points listed below that should be addressed in a revised manuscript, mainly focused on streamlining and shortening which will help to remove much of the speculation. It is recommended to focus on the novel aspects of the study, namely the combined analysis across the multiple components of the coral holobiont.  However care should be taken to not over-interpret the results and where there are limitations these should be highlighted.  The comments below are hoped to help in a revised manuscript.

Major Points:
•	The manuscripts is very long for what is actually presented; i.e. amplicon data across 14 sampled colonies.  While the combination of Symbiodinium, bacterial and fungal diversity metrics is a nice approach, and combined with network analysis brings in aspects of co-occurrence patterns, caution should be taken in interpretation of the patterns.  There is a lot of speculation on adaption and functional roles of the associated microbial community without any actual functional evidence. This speculation contributes somewhat to the length of the paper and could be reduced to help streamline the main messages.
•	It would be good to provide more details about the local conditions and habitat from which the corals were sampled from.  It is stated that the samples are derived from 1 reef and 2 depths @ 17m and 27 m; however I find it difficult to see how just a 10 m depth difference can be driving many of the patterns and shifts in the microbes and how they are contributing to adaption of coral colonies as is stated in the manuscript.  More information regarding the individual location of colonies on the reef would be advantageous and also importantly if possible any local habitat conditions and microenvironment water quality parameters that maybe influencing the 17 vs. 27 m coral colonies;
•	The groupings postulated for the two depths in the Symbiodinium community as highlighted in the MDS plots (figure 2) seems not to be supported – as the Symbiodinium community for colony 2 is closer to that of Colony 12 than the other corals in this deeper cluster.  Hence while there may be weak statistical support; based on the level of replication and inherent biases of amplicon approaches it is questioned how robust these conclusions are.  One aspect not considered that may have an even greater influence on all microbial partners including the Symbiodinium populations is the coral host genotype.   This should at least be discussed if no data is obtained for these genotypic differences.
•	Inherent biases associated with the technology exist; i.e. sample to sample variation is in part a result of library prep and amplification efficiency.   Duplicate or replicate samples from each individual colony would help identify the bias associated with these approaches.  While this may be a hindsight detail – it is kind of important to provide greater rigor around if there is a real difference (for Symbiodinium) or lack thereof (for bacteria, fungi etc.)   across the individual colonies at the two sampling depths.

Other points:
•	Abstract – last sentence:  How is local adaption assessed; There is no information in the manuscript around adaption or traits associated with adaption or functional information for the microbial associates.  Hence unless some information is provided on different conditions the coral colonies experience at the two depths; inference to adaption should be removed.
•	Line 51: This sentence starting “ Most well studies…..” is reads strange – perhaps rephrase
•	Line 58 – provide a reference for “host flexibility”
•	Sentence starting line 64 can be removed – adds little and “significant impact” is a strange way to refer to microbial associations with important functions to the coral holobiont.
•	Line 77:   Update other recent papers in this space; Agree there are not many but more are coming; i.e. Ainsworth eta l 2017;
•	Line 81;   This paragraph could fit better as the first paragraph of the introduction in some respects: It goes very broad again;
•	Line 94: Sentence starting “ In addition….”  Is repetitive – remove
•	Line 126: remove “over the last two weeks”
•	Line 128-132:  Were coral colonies washed to remove loosely attached microbial associates and even microbes derived from the water column?  What is the carry-over of contaminating microbes especially as corals were collected by what seems to be divers focused on other tasks as well?  This is relevant to the dominant bacterial OTUs i.e. a SAR116 and Synechococcales affiliated OTUs.  Both these OTUs also prevalent in water surrounding corals and more commonly documented from these water habitats. This needs to be discussed in the manuscript.
•	 Overall the discussion seems very long and could be cut back extensively to make the manuscript more focused.
•	Line 316:  The use of the term “subcomponents’ to describe the Symbiodinium, bacterial and fungal communities seems confusing to me; from my point of view this could also refer to different microhabitats of corals.  Hence I would rephrase;  i.e. the Different microbial populations
•	Line 335:  It could be questioned what is the relevance of depth to Symbiodinium diversity; in my mind such a narrow environmental difference may have limited influence;  The other studies of Bongaerts et al for example are over much bigger depth gradients.  Again the question of genotype seems more relevant here and needs discussion.
•	Line 382:  Very weak sentence here?  Remove?
•	Line 388 – remove remarkable?   Avoid over descriptive language.
•	Throughout the section discussing bacteria – i.e. lines 385 onwards;   much of it is based on inferring potential functional roles of identified OTUs;  This is very speculative and should be reduced where possible;
•	Line 406 Sentence starting : The high abundance…” does not add much;
•	Line 410:  Certain OTUs can be signs for concern of the data; for example Ralstonia is a common contaminant in Bacterial amplicon sequencing studies.  Were any negative controls included in the analysis; to provide a based line for contaminant sequences that are prevalent in all amplicon studies?
•	Line 441:  This sentence is not clear to me; what is it trying to say?  Again much of the fungal discussion from line 421 can be reduced.
•	Line 480-484: Is this paragraph providing anything?  Remove?
•	Line 526:  remove – there is no data to support local adaption and so this conclusion cannot be supported.
•	Much of the conclusion is repeating aspects of the paper rather than providing a summation of the major conclusions.  For example lines 535-541 can be removed.


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: INTER-DOMAIN MICROBIAL DIVERSITY WITHIN THE CORAL HOLOBIONT SIDERASTREA SIDEREA FROM TWO DEPTH HABITATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. The manuscript is mostly clear, but there are a few occasions where meaning was obscured due to the lack of sentence structure. I have provided several examples of this and I recommend that the authors re-structure or break-up these sentences so that they are easier to read and interpret. See lines 157-158, 198-202, 236-238, 289-291, 339-343, 359-361, and 530-532. I would also recommend that the authors read over the manuscript closely- I noticed grammatical errors throughout the text.
2. The manuscript needs a conclusion paragraph within the discussion to tie everything together. Currently, the discussion ends abruptly with a paragraph concerning the abundant bOTUs.
3. The sentence “However, these hypotheses are poorly explored (lines 90-91)” needs to be revisited. This sentence suggests that very little to no research has been conducted concerning how shifts in the microbiome by depth may contribute to the ecological success of corals, but there are a number of articles that have attempted to address this. Some of these citations are already included in the paper.
4. The authors offer a Mothur script and other files within their supplementary materials (line 168, line 174), but I cannot see these files uploaded. Was this submitted with the manuscript?
5. When an object (i.e. reference database, software, resource) is introduced for the first time in the manuscript, the complete name of the object should be spelled out. There are several instances where the authors refer to the tool or resource with just the acronym (see lines 173, 184, and 186 for examples – this is not a comprehensive list and the authors should amend this if they revise the manuscript).
6. The abbreviation sOTU is not introduced with the term it is referring to (line 227) and this is confusing.
7. The use of the Basic Local Alignment Search Tool (BLAST) server should also be cited.
8. Adding more background about the physiology and life history (i.e. mode of reproduction, symbiont vertical transmission) of S. siderea would improve the manuscript (perhaps within the introduction?). Also, was there an ecological reason as to why S. siderea was selected for this study? If so, please provide this justification within the manuscript. Perhaps this information can also be used within the discussion to explain and interpret the results. Could this information also explain differences that are observed in Symbiodinium by depth?
9. Table 1: the table description should be written in complete sentences and references Deep (D), Middle (M), and Shallow (S) depths that are not within the table. The sentence “When types, fOTUS or bacterial families . . .” tells the reader that somehow information from the network analysis is included in the table, but this information is not in the table. The word “ Symbiodinium” is missing from this sentence as well.
10. The authors should be consistent with how they refer to the different microbial communities throughout the text. This is easier for the reader to interpret.
11. Figure 2: Please indicate how these polygons were drawn. Is this a statistical procedure?
12. Figure 3: Please add information about what the emboldened line represents and what the edges of the box represent (i.e. first or third quartiles).
Experimental design: 1. The authors mention a number of times that differences in the environment may drive differences in the Symbiodinium community between depths, but no information about the environment is given at either depth, other than the location. To improve the strength of the study, the authors should provide this data (if they can) and its analysis and use this to develop clearer and more meaningful conclusions about their results and some of the influences that potentially drive differences in the Symbiodinium community.
2. Was the DMSO-EDTA solution used to collect the corals sterile (line 130)? How was it sterilized?
3. Was the seawater decanted from the initial collection tube immediately after ascent?
4. How were the coral pieces stored until they could be preserved?
5. I commend the authors for justifying their choice of reference database!
Validity of the findings: In reference to the indicator species analysis, the results stated in the text (lines 289-290) do not match the results in table 1; 3 bacterial OTUs were identified for either of the 2 depths. Reading from table 1, it appears that RSB-22 was only an indicator at 27m while the unclassified Alphaproteobacterium-III and Desulfovibrio were indicators at 17 m.
Additional comments: The manuscript “Interdomain microbial diversity within the coral holobiont Siderastrea siderea from two depth habitats” by Bonthond and colleagues describes the diversity and composition of the Symbiodinim, bacterial, and fungal communities associated with Siderastrea siderea corals over a narrow depth gradient (17 and 27 m). This study also introduces and provides new information to the field of coral microbiology in a number of ways. First of all, this manuscript provides information about the microbiome of S. siderea, which is an abundant Caribbean coral that has been relatively understudied with regard to its microbiome. Secondly, the manuscript characterizes the fungal community associated with these corals using amplicon sequencing and by doing so, provides methods that other researchers can use to target these communities as well as outlines limitations related to non-specific priming and database coverage that need to be addressed to advance research in this area. Thirdly, the manuscript attempts to look at co-occurrence patterns between Symbiodinium, bacteria, and fungi using network analysis to reveal potentially meaningful associations between microorganisms within S. siderea.
	While the manuscript contains information, methods, and insight that will be useful to the field, the manuscript requires significant revisions. Overall, the manuscript lacks synthesis of the results within the context of what we already know about Symbiodinium and their importance within the coral host and this is most obvious within the discussion of the results. For example, the discussion never revisits the content stated within the conclusion sentence that is offered in the abstract “In terms of differences in microbial composition between the studied depth habitats, our data suggest that local adaptation of the S. siderea holobiont is achieved in parallel with a shift in the endosymbiotic Symbiodinium community while bacterial and fungal community compositions undergo little change.” After reading this discussion and seeing the results, I am not convinced that local adaptation (to what: depth? light availability? temperature?) is the cause for shifts in the Symbiodinium community. I have also provided several examples of this in the other comment sections.


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: INTER-DOMAIN MICROBIAL DIVERSITY WITHIN THE CORAL HOLOBIONT SIDERASTREA SIDEREA FROM TWO DEPTH HABITATS
Review round: 2
Reviewer: 1

Output:
Basic reporting: These aspects of the manuscript are OK (though scripts files missing in Supplementary Material)
Experimental design: Adequate with limitations highlighted below
Validity of the findings: Satisfactory though some qualifications are required
Additional comments: This revised manuscript details the Symbiodinium, bacterial and fungal diversity of 14 Siderastrea sidera coral colonies sampled from one reef across two depths using amplicon sequencing approaches. The revision has improved the manuscript and while most concerns have been addresses adequately, there are still some issues raised and some additional edits that would aid the manuscript when published.  Overall I think the manuscript is acceptable for publication though it is limited in some aspects, though also it is acknowledged that most studies have some limitations.
The limitations include;

1.	The limited number of samples in the study and the absences of within sample replicates to assess variation and biases that are inherent in the amplicon sequencing approaches.
2.	The lack of any physio-chemical measurements of the environmental conditions (including light) but which are inferred to be structuring the Symbiodinium shifts.
3.	The sampling methodology does raise issues for me with corals only being removed from the surrounding seawater and not actively washed to remove loosely attached microbes. Especially since these samples were collected by divers not specifically trained in sample collection and the samples spent up to 4 hours in the seawater before processing. All these factors can change the microbial community diversity patterns.
4.	Finally I still think the manuscript is very long for a diversity analysis of 14 samples and suggest a few areas that can be further cut or reduced to focus the manuscript.
It would be advantageous if the Authors could provide some short qualification in a revised manuscript addressing the points 1 -3 above and also still address point 4 which does result in a lack of focus of the manuscript.  These are only minor corrections that I believe would help the manuscript and provide a useful contribution to the coral microbiology field.

Other points:
•	Lines 281- 303 is essentially discussion and not results. This section should be integrated into the discussion. It is still quite speculative assigning location to the coral tissues specifically based on retrieval of only sequences, especially considering the samples were not washed to remove loosely attached and mucus associated communities.    It is also not clear why OTU5 sequences are specifically highlighted as presumably many of the recovered sequences are tissue associated, and or mucus, skeleton.  This is an issue for many coral studies as the localized habitats of coral associated microbial communities are vague, hence based on these samples and only recovering sequences it is impossible to infer if they are surrounding, mucus, tissue, skeleton or gastric cavity associated microbes.  I would recommend being very cautious in speculating on location without additional evidence.
•	Lines 320-333 Can be removed as these two paragraphs are very short and essentially saying what is also discussed in the following paragraphs (i.e. line 334 onwards).   This again contributes to the length and lack of focus in the manuscript.
•	Lines 382-394;  This section again is highly speculative based on recovery of a short region of the 16S rRNA gene sequence. Hence starting the bacterial discussion on such a speculative topic is problematic in my view. The discussion should initially focus on the results that can be supported – i.e. diversity patterns between sample depths and no significant changes (unlike the Symbiodinium).  Then discuss some of the co-occurrence patterns and then bring in the speculation (in a very limited and focused way on this OTU1 combining the results (lines 281-303) with this paragraph.  However keep it short and focused and do not go into too much unsubstantiated speculation.
•	Note the Mothur script I can not see in the uploaded Supplementary files.


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: INTER-DOMAIN MICROBIAL DIVERSITY WITHIN THE CORAL HOLOBIONT SIDERASTREA SIDEREA FROM TWO DEPTH HABITATS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript is greatly improved in comparison to the first version of the manuscript.
Experimental design: I have no further comments on the experimental design.
Validity of the findings: I have no further comments on the validity of the findings.
Additional comments: There are a few grammatical issues in this manuscript that should be corrected in the copy editing process.


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: FORECASTING BIODIVERSITY IN BREEDING BIRDS USING BEST PRACTICES
Review round: 1
Reviewer: 1

Output:
Basic reporting: I found the paper very clear and easy to follow, with a good intro/discussion that tied the current work into previous studies. All data shared - in addition to code. More minor comments in General Comments section.
Experimental design: This question and forecasting competition was well designed. I had minor comments to improve clarity with models. The analysis is all documented/replicable on the Github repo. More minor comments in General Comments section.
Validity of the findings: All data is robust, and analyses are sound. Conclusions and recommendations are well stated.  The authors have really done a great job with transparency - this is a model of what all papers should strive for. See additional comments in General Comments section
Additional comments: Review of Harris et al. Forecasting biodiversity in breeding birds using best practices

In general, I thought this paper was interesting and well written. These results add to the increasing literature supporting the idea that ecological forecasting in time/space is difficult. I think the recommendations/best practice bullet points described by the authors are essential for anyone interested in forecasting this kind of data. All of my points below can be considered minor issues, which I think will improve the paper’s clarity.

Introduction:
Line 41: I think this is generally more common in terrestrial ecology – in fisheries these SDM models with more of a theoretical background don’t seem to be used as much

Line 62: I really like the recommendations / clarity in Box 1, and think these will be accessible to most ecologists

Line 71-73: I’m re-reading this after commenting on data, and am now a little confused. The bird responses are annual snapshots during the breeding season? And I thought the environmental data you used was annual or quarterly, not monthly?
https://www.mbr-pwrc.usgs.gov/bbs/grass/genintro.htm

Methods:
Line 92: For those not familiar with the BBS protocol, maybe describe in a sentence. I could be mis-remembering, but isn’t each site made up of 50 stops, and presumably you aggregated richness across these stops?

Line 105: I assume all these species have been similarly ID’d over the course of the dataset – e.g. birds split into sub-species haven’t been included.

Line 107: For the environmental variables, do you have any that match up with the temporal resolution of the response data (monthly?). It seems like all the variables are annual / quarterly / etc.

Line 124: I’m not as familiar with terrestrial projections, but are the  CMIP5 projections relatively unbiased / precise when compared to recent data?

Line 138: Maybe also cite any of the interfaces you used, like RStan:
http://mc-stan.org/users/citations/

Line 140: I’m curious why you didn’t consider spatial structure in the random effects here, using GMRF models or similar? One hand these models might be overkill if the habitat/environmental variables (which are spatially correlated) explain variability in richness, but the spatial correlation may pick up other sources of variability not accounted for by those variables.

Line 141-143: I think the paper thus far is pretty clear. I was hoping to see a few equations here – it helps me especially when components start to become hierarchical!

Line 163-164: again, I think equations could really help here to describe the baseline models. I think it’s also important to use these to clarify key details – for example, by training models on a site-by-site basis, you’re estimating separate parameters by site. For example with the uncorrelated noise model, you’re estimating unique variances by site right? Maybe say something like this, in addition to including equations.

Line 180 – Maybe also mention this is in the forecast package – as you do with gbm below?

Line 183: Because these defaults may change over time, it’d be good to specify things like the ranges of AR / MA order that you searched over, which criteria was used to compare models, etc. And whether or not you included a drift parameter?

Table 1 caption: without getting to more methods (below), I don’t understand the sentence ‘Environmental models were trained using all sites together, without information regarding which transects occurred at which site or during which year’.

Table 1: Just my personal preference, but I’d include the check marks and replace the ‘Xs’ with blank cells

Line 194-221: It seems for each approach you only considered the full models with all environmental covariates? I’m curious whether any of the covariates appeared to not improve explanatory power, and whether you considered models that dropped these uninformative predictors?

Line 216: Cite randomForest / caret/ party R package – or whatever else you used?

Line 242: Again, I think including the equation here would be useful

Line 245: In our 2014 forecasting paper, we used MASE over RMSE because of rationale in Hyndmand and Koehler (2006). Using RMSE here is probably ok because you probably don’t have zeros/huge values/etc

Line 249: Can you elaborate on what you did with the deviance? By itself mean deviance is just a measure of average fit (I think most of the models are giving you this). Var(deviance) should incorporate precision – but I’ve only seen this extracted from Bayesian models

Line 266: I think you guys have done a great job putting together this public repository + made the analysis totally transparent. My one hang up with the repo was that it’d be awesome to include a short vignette with example data from this project that is more easily accessible to readers without having to install Jupyter/R packages/etc. For example – I was travelling when I started this review and couldn’t install one of the R packages on my government computer without making an appointment with our IT staff (so it took ~ a day).  This isn’t your fault of course, but much harder for me to dig through the repo.

Line 269: See my above comments about spatially correlated random effects / GMRF models. One way to confirm these other approaches are overkill would be to make some maps of the estimated random effects, and fit some simple models to estimate variogram parameters – e.g. even gls() in R can do this

Line 276: Is one of the potential reasons that richness is stationary that presence/absence on the BBS varies less than other measures – maybe abundance, or other measures of diversity are more variable?

Line 294: Is the narrow predictive distribution for the stacked SDM also why this exhibits the strongest trend in decreasing coverge as a function of forecast length (Fig 5)?

Line 329 – maybe reword, you use forecast 3x in this sentence

Line 414: Agreed – doing this same kind of forecasting competition with compositional data, or other species diversity measures (Simpson’s) would be interesting

Line 461: Another thread with conservation implications is that back in the 1990s, it was pretty common for single species PVA models to be forecasted 100-200 years. This seems less common, in part because some predictions may have not performed well, and others are on a time horizon that can’t be evaluated. In Steve Beissinger’s PVA book he cites Goldwasser (2000) “Variability and measurement error in extinction risk analysis...” for this point (p 133).


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: FORECASTING BIODIVERSITY IN BREEDING BIRDS USING BEST PRACTICES
Review round: 1
Reviewer: 2

Output:
Basic reporting: see general comments
Experimental design: see general comments
Validity of the findings: see general comments
Additional comments: In this paper, the authors use the incredibly rich data from the Breeding Bird Survey to examine how well various models perform at predicting bird richness at sites throughout North America. They train models on data from 1982-2003 and attempt to predict data from 2004-2013. They examine the performance of six different model types, two of which are null or baseline models.

I find it a bit surprising that the authors think that any of these richness models could predict a high level of accuracy for theses ten years. I think of richness estimations as a very coarse technique for looking at broad shifts in richness over relatively long time periods rather than these 5-species (~5-7%) shifts in richness on annual bases indicated in Figure 2. The authors don’t provide a lot of their raw data on sites other than as examples, but my impression is that they are pursuing an unrealistic level of accuracy and detail. That being said, given what the paper does, it’s okay. The models seem to be performed well. The authors give all of the keywords to indicate that they know what they are doing.

Here are some comments:
-	Birds are not the best system for doing any sort of distribution analyses. They are incredibly vagile, hard to detect, and the distributions of breeding birds are affected by many components besides environmental variables (particularly interspecific interactions). No assessment of detectability is included here other than accounting for observer identity. However, I do realize that BBS data are detailed and compelling data to use given what a large amount of detailed time-series it provides.
-	Abstract: The authors forecast the data and then test it using known data. Hindcast only refers to back-in-time predictions.
-	25-29: rather than relay the type of information that the paper will provide, the authors should summarize their results and findings
-	57-58: this is not the definition of hindcasting. This is the definition of testing. Also, the authors exclude the many deeper-time hindcasting studies that have been performed on these types of models.
-	Methods: the authors perform their analyses on data that are collected from an incredibly dynamic time period. I wouldn’t expect species to have settled into a richness pattern given the incredibly disrupted nature of the last 32 years. Some strategies to try to handle these issues might be to train and predict at different temporal scales and to both forecast and hindcast the predictions. (e.g. train on 2004-2013 and try to predict 1982-1992 data + 1993-2003 data). If the authors were to make splits based on expected periods of dynamism, they could better tell whether the drivers that are included in the models are accurate predictors.
-	124-130: I didn’t see where future projections were performed/used in this paper. Why is this here?
-	Fig. 2: Panels not labeled. No key for colors. Somewhat confusing.
-	Fig. 6 caption: “compoonents”
-	466: only other mention of future forecasts… not sure why this is included in this 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: BIOREACTOR VIROME METAGENOMICS SEQUENCING USING DNA SPIKE-INS
Review round: 1
Reviewer: 1

Output:
Basic reporting: -	Minor points:
o	A clearer picture of the potential samples that would be processed with this protocol should be presented. The assumption is that these would be environmental samples, but even that is too broad. Water, soil, plant material, clinical samples?
o	Lines 42 and 62: “low quantity” and “low yield” of DNA. This is too vague. The reader should also be presented with DNA concentration ranges from environmental samples so that they can fully understand the problem. Obviously some would contain enough DNA.
o	Line 61: “relative large amount of DNA needed”: Again, this is too vague. Please present the input requirements for several popular library prep kits so that the readers can clearly see how the expected DNA extraction yield compares to the kit requirements.
o	Relating to the last point, with several commercial kits, DNA can be prepared for sequencing using < 1ng of DNA. For example, even though Nextera XT is optimized for at least 1 ng of DNA, as little as 5-10 pg can be used to generate libraries. However, sequencing from pg of DNA opposed to ng could also skew the viral populations. It would be nice to discuss this approach as an alternative.
Experimental design: -	The authors present a potential solution to a problem that many sequencing labs face, low input concentrations. However, the experiments and data presented here are not thoroughly convincing. Major points:
o	There are no controls. A high input (i.e. 1 or more ng DNA) control would provide the expected results. At this point, I cannot tell if there should only be 6 viruses present in the population or more. Also, a water or negative control would help to convince me that some of these reads were not contamination. A comparison between spiked and MDA is not enough.
o	N=1 for all test groups. This should be expanded to at least n=3 for all groups for your results to be sufficiently convincing.
o	Only 16S reads were removed the DNA-spiked reads (via mapping to SILVA). All groups should be treated to the same analysis. This may have also removed real 16S reads that were present in the bacteriophage population, but the 16S were left in the MDA samples. This may have accounted for some of your % reads aligning to the viral sequences.
o	A dilution series of input DNA would be required to justify how much input DNA is required for this protocol. Likewise, why was 43.2 ng chosen as a spike-in concentration? Adding a test range of spike-in amounts, in addition to the dilution series of input concentrations, would help potential users of this protocol know what combinations to use.

-	Minor points:
o	Include a table that shows the data per library. My suggestions:
♣	total number of reads pre-trimming
♣	total number of reads post quality trimming
♣	total number of reads post 16S removal
♣	Percent processed reads aligning to bacteria and viruses #1-6
o	Line 218: show the data shift towards bacteria genes. This could be included in the table.
o	An overview figure of the method would help readers better understand the process.
Validity of the findings: o	Line 236: Conclusion that you could examine the viral metagenome using an extremely low input (0.1 ng DNA needed) is not fully supported here. See experimental design. Controls and additional comparisons are required.
Additional comments: This very well could be a really neat, easy solution to low input amounts of DNA heading into the library prep process. The data shown supports the authors method, but I am hesitant to be convinced until I see additional replicates and controls. Also, the input and spike-in ranges need to be defined.


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: BIOREACTOR VIROME METAGENOMICS SEQUENCING USING DNA SPIKE-INS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper meets the general requirements for this area.
Experimental design: One major issue for the study is that the comparison is made with N=1.  The reproducibility of the spike-in library data is unknown.  Since this paper is arguing for the virtue of the method, at a minimum, the authors must repeat the library construction and sequencing of the spike-in sample, and define the reproducibility of the results.

Ideally, I would prefer to have seen a defined viral metagenome (mixture of purified, known viral genomes) assessed by the spike-in vs MDA methods. This would avoid issues arising from uncertainties as to the composition of the unknown viral metagenome used in this experiment (e.g. the presence of small bacteria that pass through the viral purification step that the authors mention, etc). Nonetheless, useful data can certainly be extracted from the authors approach.

The mass ratio of the spike in—0.1 ng with 42 ng of spike would suggest an ~ 400:1 ratio of corresponding reads.    What are the relative numbers of reads that are derived from the spike to non-spike sequences?  If they do not approximate 400:1, the authors should discuss possible explanations for the actual ratio.   The authors should present statistics regarding the actual number of reads at each step (total, mapped to 16S, etc) and not just the relative abundances and %.   By my ballpark calculations from Figure 3 (197k genome * 300x coverage)=60 MB of viral sequence. This constitutes ~40% of the total viral metagneome, so at least 120Mb out of the total run is from the viral metagenome.  Seems like the actual ratio has to be much lower than 400:1.  Why would this be?

The authors claim that 6 putative viral contigs were obtained.  However, no information is presented regarding their identity—what viruses are they most similar to?  What criteria were used to call them (and not any of the many other contigs obtained) viral?  More detail needs to be provided about this.
Also, it is not clear  what is meant in line 182 “The
DNA-spiking method resulted in five viral genomes while the MDA set only resulted in one.”   The authors demonstrate that reads map to all 6 of these viruses from both methods—so is it the assemblies of the two that differ and the criteria for obtaining a viral candidate?  This needs clarification.

What is unique about the 42k contig that is it is favored in the MDA dataset?

Figure 3 is a bit complicated.  Most importantly, the authors depict circles of different sizes in the graph, but provide no explanation in the legend or the text as to what the diameter of a given data point reflects.  Is this the size of the contig?
Validity of the findings: GC content shift is a simple indicator that there has been a change, and the authors’ data clearly demonstrate a change in the GC content of the reads with MDA.  However, the paper would be strengthened if the authors were to analyze the taxonomic distribution of the reads generated by spike vs MDA to explicitly define which taxa are increased/decreased in representation by the MDA process.
Given that one known bias is that MDA will preferentially amplify small circular genomes, is it possible that there is some low GC-content small circular DNA template contaminant (e.g. plasmids or dark matter circular viruses) that is being amplified and driving this observed increase in low GC content?   Because the authors conclude from this single example that MDA biases against high GC and favors low GC, it is important to determine as best as possible the source(s) that contribute to their observations.   Again, this is a single sample—would other samples show this same pattern?  The authors should temper their conclusions in the absence of additional data.
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: BIOREACTOR VIROME METAGENOMICS SEQUENCING USING DNA SPIKE-INS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors report here a simple but efficient method to sequence samples with low amount of DNA such as is often obtained in viral metagenomic studies. The introduction and material & methods are overall clear and well structured and below are some minor comments. However, the authors should globally improve the quality of the report in the results and the discussion for both english and meaning/clarity (also find some additional more specific comments in further review sections below).

Introduction:
L35-38: Please cite some relevant research and reviews for the definition of the viral "black matter" and its development with the advent of NGS.
M &M:
There are several repetitions in lines L138-144 and L145-150. Please clarify the difference between those lines.
Results:
L182 The M&M states "one more putative viral genome", which implies that the other genomes were also retrieved, which is contradicted here. Please revise the sentences.
L202-203 What is "a perpendicular distribution"? Please better describe the results obtained.
Discussion:
L215: Replace "is emphasizing" by emphasizes
L238: Replace sequence facilities by sequencing facilities
Experimental design: The authors discuss the annotation of contigs in the discussion section but no information is provided in the materials and methods. They should describe the method used for annotation and to distinguish bacteria vs virus genes.
Validity of the findings: Given the bimodal distribution of GC content in reads (Fig 1), it would be interesting to fit the values with two Gaussian distribution for each method. This would enable the authors to obtain reliable estimate in terms of mean and variance that would better show the shift due to MDA amplification (instead of approximate values).

L219-222 Please extend the discussion on the WS6-like bacteria. Are reads mapping to these bacteria also observed in the spiked DNA sample?

L223: Please discuss more largely this bias in the light of other studies reporting biases in MDA

L227-231: Rewrite this paragraph to clearly describe the differences observed, the implications, and better convey the message on the potential of DNA spiking instead of MDA with regard to the estimation of organisms' abundance.

The conclusion could be made stronger by avoiding vague terms such as "a more valid alternative" or "the obvious bias" (which may not be that obvious - are we talking about GC content bias?) and clearly stating the advantages of DNA spiking over MDA
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: BIOREACTOR VIROME METAGENOMICS SEQUENCING USING DNA SPIKE-INS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Table 1 is confusing. P1, SP, and GP need to be defined.
Experimental design: See general comments
Validity of the findings: See general comments
Additional comments: The authors state several times within the rebuttal that critiques were not within the scope of the current article. Without knowing the limits of input DNA detection and the optimal ratios of spike-in concentrations, this manuscript is essentially just about how the authors rescued viral DNA from their one “precious” bioreactor sample. Thus, if they cannot fulfill these requirements, the title of the manuscript “DNA-spiking in viral metagonome sequencing: A new method with low bias” is misleading. Interested readers would see this expecting a validated method to work for their own samples coming from a range of environments, but instead would find a case study about sequencing DNA from a bioreactor. It is not clear how beneficial this method would be outside of the current design, which drastically limits the impact. If the authors are unwilling to make this change, then perhaps it should be refocused – i.e. change title and remove suggestions that this is a general use protocol.


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: BIOREACTOR VIROME METAGENOMICS SEQUENCING USING DNA SPIKE-INS
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: There are still no replicates provided in this study.  The paper purports to describe a useful method, but there is insufficient evidence of the reproducibility of this method.

The major point of the manuscript is the description of a method (per the title). I fully appreciate that the materials used by the authors are very dilute—however, to demonstrate a method for the first time, those do not seem to be the appropriate materials to use.   Rather, it should be straightforward to reconstruct a virome (by mixing defined quantities of known viral genomes) to demonstrate the performance, reproducibility and utility of this method.   Subsequently extending this validated approach to one or more true unknown sample (such as the samples used by the authors) would then be convincing.

I do not understand why the authors argue “a defined viral metagenome is not really feasible." "The aim is to describe a method usable for low amounts of DNA obtained from precious samples”.

If the authors’ true interest is to analyze the viromes in their dilute samples, then they should retitle and rewrite the paper to focus on the viruses they were able to detect rather than present the results as a new method.

I do know on what basis the authors assert “It is very unlikely that MDA preferentially amplifies small circular genomes.”  The literature is extensive about rolling circle amplification by phi29 polymerase, and that compared to larger, linear fragments, preferential amplification of small circular genomes will occur.  See for example:
 A sequence-independent strategy for detection and cloning of circular DNA virus genomes by using multiply primed rolling-circle amplification. Rector, A. et al. J. Virol. 2004; 78: 4993–4998
Rolling-circle amplification of viral DNA genomes using phi29 polymerase
Reimar Johne, Hermann Müller, Annabel Rector, Marc van Ranst, Hans Stevens 2009 Trends in Microbiology.
Validity of the findings: see above
Additional comments: No additional comments


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

Input:
Title: BIOREACTOR VIROME METAGENOMICS SEQUENCING USING DNA SPIKE-INS
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors have added useful citations of previous work, and corrected some sentences. However, they have also significantly expanded the previous version of the article, and the quality of the reporting is not satisfactory. Different samples have been prepared with different methods, and the results do not always clearly specifiy the sample/protocol used, as for example in Figure 3 legend ("on one sample"). Unnecessary repetitions are often found, for example "Several different causes have been given in literature regarding the bias of MDA. Reasons such as fragment length, GC-content, quality of DNA and even different MDA kits 416 (Abulencia et al., 2006; Kim & Bae, 2011; Yan et al., 2004; Yilmaz et al., 2010) have been implicated in MDA bias.". The authors should improve the overall quality of the report and the quality of English writing, trying to facilitate the reader's understanding as the complexity of the various samples sequenced and methods used has increased.
Experimental design: The software used for the mapping of the reads to P1 phage (L183) as well as to the SILVA database should be mentioned.
Validity of the findings: Results reported in Table 2 have been obtained using different cutoffs to map reads to the SILVA database. As such, the results in column DNA-spiked-SP and 1x-2xMDA are not comparable. Why did the authors change their cutoffs ? The 16S used to spike the sample has been removed prior to the mapping, and therefore should not interfere with this second mapping. The presence of chimeric reads should be checked for before using appropriate tools.

Figure 1 showing the methods used is a good addition to facilitates the reader's understanding. Given its current 2/3 of a page width size, it could be expanded to include as well a representation of the different sample preparation, sequencing (P1, GP, SP, spiking, MDA) & naming convention.
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: AN INDO-PACIFIC DAMSELFISH (NEOPOMACENTRUS CYANOMOS) IN THE GULF OF MEXICO: ORIGIN AND MODE OF INTRODUCTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: - The English should be improved, mainly in the introduction and methodology sections. More attention should be given to the sentence construction.
- The introduction and background is appropriated but can be improved in relation to the information about the species. A restructuring of the introduction is encouraged to make it clearer. The references used are in agreement with the subject addressed in the article, but more references should be added to reinforce your expected results.
- The structure are in conforms to PeerJ standards.
- The figures are relevant and the quality seems good. The labels should by improve and more detailed, mainly the Fig. 2 label.
- The sequences were deposited in GenBank and the accession numbers are provided.
Experimental design: - The research is in agreement with the PeerJ scope.
- The article question is relevant, meaningful and well-defined.
- The investigation was performed with an appropriate methodology.
- The methods description should be improved to be more understandable.
Validity of the findings: - The data is robust and statistically sound.
- The conclusions are well supported by the results obtained and linked to the original research question.
Additional comments: - Provide the species name in title “An Indo-Pacific damselfish (Neopomacentrus cyanomos) in the Gulf of Mexico: origin and mode of introduction.”
- In the M&M section I don’t understanding why you have two COI fragments, one of 594 bp and other of 652 bp. The “DNA sequence” part is confusing, which makes the understanding hard. Please consider reorganize the DNA sequence part.
- You not specify the program used to calculate the genetic diversity parameters.
- Provide the parameters used in the maximum likelihood analysis.
- The neutrality tests and mismatch distribution are nice to give an idea about the historical changes. However, a more sophisticate and less speculative analysis should be included. Thus, I suggest include a Bayesian Skyline Plot. You can do this using the program BEAST/BEAuTi.
- In the Result section, I recommend include a table with the genetic diversity parameters and the values of neutrality tests and mismatch distribution analysis. In addition, a separate figure with the ML tree should be nice (just a minor suggestion).
- Other minor comments are made in the attached document.


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: AN INDO-PACIFIC DAMSELFISH (NEOPOMACENTRUS CYANOMOS) IN THE GULF OF MEXICO: ORIGIN AND MODE OF INTRODUCTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: Writing is clear overall and results in figures and tables well presented.

However I consider that the introduction could be structured better, I think authors jump too quickly to present their research questions and the last paragraph of introduction reads a bit like a discussion, it would be useful to tidy it up a bit to make it more concrete and short.

The last paragraph in discussion section/subsection “Where in the GoMx was N. cyanomos initially introduced?”, lines 446-457, is very important as future directions, however it does not fit with the overall theme of this subsection, I would suggest change the name of subsection, distribute its contents along the discussion of each of the three hypothesis, or add a new subsection.

Conclusions section, lines 468-469, authors refer to the Neopomacentrus species, perhaps should be the Neopomacentrus genus?

Figures overall, it would help in the interpretation if the same color palette between Figure 1 and 2 is used as currently different blues are used for groups 1 and 4.

Figure 1. Please add a clear description of what each slice of pie represents.
Experimental design: Research questions are well defined and analysis is implemented thoroughly, overall I do not see any flaws on this area. However I do think that in the Methods section (particularly lines 121-124), it is not very clear which data was collected for this study and which data comes either from other studies or collected for other purposes.
Validity of the findings: I consider the overall interpretation of data solid, however I am missing a bit more discussion to strengthen the discussion presented on the competing hypothesis, in particular:

I understand that the molecular markers used do not support the first hypothesis, however I think authors are dismissing it very rapidly without digging it out completely, a couple important points: 1) stating that marine aquarium trade is negligible in Mexico based on “personal communication” (line 257) is very weak to say the least, perhaps cite: Lango-Reynoso et al 2012 (Lat. Am. J. Aquat. Res., 40(1): 12-21, 2012. DOI: 10.3856/vol40-issue1-fulltext-2) or other paper that actually proves or show this is the case; 2) additionally, I think the idea in line 455-457 is kind of lost and out of place here as this is an important point to make in light of data currently analyzed and remaining research avenues to explore.

I find that authors did a solid job at discussing why hypothesis 2 is not plausible in terms of the most used shipping routes for cargo ships, however I have some concerns and fail to see the same thorough link between the ecological plausibility of a fish species such as N. cyanomos surviving a journey from the Indo-Pacific to the SwGoMx in petro platforms, that is when discussing hypothesis 3. In particular, while authors do present examples from other introductions, all these have been comparatively less traveled distances from origin to final destination. Additionally, supplemental Figure 2 indicates the origin of platforms as a set of arrows from the origin to the final destination, however it is not clear to me whether this is a depiction of their actual traveling paths? If so, tropical sessile fouling organisms and associated fish would need to endure a travel through temperate water areas in South Africa as cold as those present in California (annual mean temperature range for both location is ~14-22 C), which is one point authors present against hypothesis 1 (lines 297-299). Authors should address these concern or specify the likely travel path of the petro-platforms.

Furthermore, and while I understand this may not be the goal of the manuscript, I think authors should present or state as future research directions why – if these petro platforms/drilling ships carry such large communities – have we failed to see more invasive species establishing in the SwGoMx, has it been a lack of detectability, or perhaps some specific characteristics inherent to the studied species N. cyanomos?
Additional comments: This paper is very relevant for the field of invasive species in coral reef ecosystems as there is a need to understand the vectors of invasive species to implement control and management strategies as to minimize such introductions. This paper is also relevant in light of recent invasive species that have produced large and potentially everlasting ecological damage to invaded areas such as that of the invasive Indo-Pacific lionfish to the North Western Atlantic. Authors did a great job at presenting solid research questions and addressed them accordingly.


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: DETECTION OF STABLE COMMUNITY STRUCTURES WITHIN GUT MICROBIOTA CO-OCCURRENCE NETWORKS FROM DIFFERENT HUMAN POPULATIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The language is ok, but some mistakes should be fixed (see General comments).

Literature references & relevance: reference format should be fixed in a couple of places in the manuscript.

Raw data: «LLDEEP 16S rRNA gene sequencing data is available from the EGA (Accession: EGAD00001001991).» - However, at the specific location, the reads are in restricted access.
Experimental design: Identification of co-occurence groups in microbiota is a topic of high interest. Advance in this area will make metagenomic data analysis and interpretation more robust and insightful. The manuscript contributes to the field via large-scale meta-analysis performed using a novel verified ensemble-based methodology.

The methods are described in details.
Validity of the findings: The findings are well supported.
Additional comments: Intro & background: As far a reviewer is concerned, in order to make the introduction more rounded, reference to co-occurence modeling in relation to metabolic interactions should be added (http://www.pnas.org/content/110/31/12804.full ) - as well as to the algorithms for inference of microbial co-occurrence from temporal points analysis (not just single metagenomes).

Could you comment on how would the main outcomes of the study change if the OTU are generate not at 97% but at higher or lower percent of identity?

There is another method for co-occurrence network analysis - SPIECEASI - that is related to SparCC but reported to be superior to it [http://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1004226]. Addition of it to the set of analyzed algorithms would add value to the manuscript, as far as the reviewer is concerned.

Other specific comments - line-wise

Line #23: "The interactions defining these communities can be inferred from the co-occurrence of taxa across multiple samples" - not always: the microbes might just share 1 niche and not interact at all (e.g. see the conclusions of http://www.pnas.org/content/110/31/12804.full)

38 - "in either an actively targeted or passive manner" - it can be neutral, too

50 — specialist approaches - specialized approaches might sound better.

57 - subsets OF taxa

86 - It is worth noting that that the sequencing platform was the same in all studies.

109 - "de novo" - should be in italic here and elsewhere. Same applies to "in vitro".

131 - Is there any rationale behind the number 25%?

(many times in the text) Perhaps, "chosen" should be replaced with "selected".

155 - misprint: compossitionality

161 - unfinished title

166 - Why do authors use different adjustment method (Bonferroni - while applying FDR in other analyses)?

176 - From biological point of view, it was not completely clear to the reviewer why was the fitting of network structure to scale-free network used to identify the optimal p-value. Perhaps, this could be clarified.

177 - "whose" - please replace here and elsewhere:
We use "who" when referring to people or when we want to know the person.
We use "which" to refer to a thing or an idea, and to ask about choices.
We use "that" for both a person and a thing/idea.

182 - R2 - 2 should be superscript

186 - used -> was used

210 - sub set - ?

Fig 2B - Could you comment on the impulses observed for Israeli data in top 2 plots? Looks like potential inconsistency in the data - in comparison with the overall smooth plots.

340 - please explain the meaning of the "mixture of assignments" - here or in Methods. Also, in Suppl. Table 1 it is not clear which of the assignments are "mixture".

353 - "heritable taxa" - the term appears to be unclear. Strictly, the heritability of gut microbes has not been demonstrated - we can only talk about its inferred extent. Consider - "highly heritable taxa".

357 - associated -> were associated

423 - With BMI, the direction of causality is not that certain.

436 - Consider citing some of the recent high-impact articles from 2017 about this topic (for instance, https://www.nature.com/articles/nbt.3981 or https://www.ncbi.nlm.nih.gov/pubmed/28967887).

476, 497 - reference format.

488 - butryate

489-492 - The logic is not clear. Moreover, the 2006 study is about mice and the results have not been confirmed in humans in a large-scale meta—analysis (http://mbio.asm.org/content/7/4/e01018-16.full).

492 - Bifidobacterium - should be in italic.

493 - As far as reviewer is concerned, Yatsunenko et al have reported the descrease of Bifidobacterium for other age cohorts - prevailed by infants. Might be better to rephrase.

494 - negatively -> were negatively


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: DETECTION OF STABLE COMMUNITY STRUCTURES WITHIN GUT MICROBIOTA CO-OCCURRENCE NETWORKS FROM DIFFERENT HUMAN POPULATIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is generally very well written. The abstract and introduction suffer from typographic errors - for example line 30 is missing an adverb (‘significantly more similar’), line 57 a preposition (‘subsets of taxa’). A simple proofread will correct this.

Weiss et al. 2016 is a joint first author paper. Perhaps it should read Weiss and Van Treuren et al. 2016 here and in other locations where it is cited.
Experimental design: From a methodological perspective, the paper is well thought out. The explicit description of the algorithmic steps taken to generate final modular network make it clear the authors evaluated each choice in this pipeline.  The description and exploration of the important parameters (e.g. gamma) is admirable and more papers would do well to emulate this.  Certain choices seem somewhat arbitrary, but that is inevitable in a pipeline that transforms the data through multiple steps.
Validity of the findings: The findings are valid and the data accessible.
Additional comments: Jackson et al. present a method for detecting/building taxa co-occurrence graphs and then analyze a co-occurrence network built from three large human 16S sequencing datasets.  Primary network building is accomplished by selecting the intersecting edges of graphs generated with four independent detection techniques following recommendations of Weiss and Van Treuren et al. The stringency of edge detection (p-value) is set by choosing the p-value that best produces a scale-free network. Finally, communities are detected in the network by aggregating the edges (pairwise co-occurrences) into modules based on local connection and modularity.
To validate this method of community detection the authors recapitulate findings from Goodrich et al. 2014 in the same dataset used in that paper. They also find associations between host subject parameters (e.g. BMI) and community abundance that are supported by recent literature.  To conclude, the authors suggest their method creates analytical tractability and dimensionality reduction while capturing the important ecological units that are operating across population in the human gut.
	From a methodological perspective, the paper is well thought out. The explicit description of the algorithmic steps taken to generate final modular network make it clear the authors evaluated each choice in this pipeline.  The description and exploration of the important parameters (e.g. gamma) is admirable and more papers would do well to emulate this.  Certain choices seem somewhat arbitrary, but that is inevitable in a pipeline that transforms the data through multiple steps. While the methodology is clearly described, the benefit of the final network in data analysis, hypothesis generation, experimental motivation, etc. is unclear. The authors could strengthen the manuscript by indicating what their network approach enables that was unattainable with previous methods.


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: DETECTION OF STABLE COMMUNITY STRUCTURES WITHIN GUT MICROBIOTA CO-OCCURRENCE NETWORKS FROM DIFFERENT HUMAN POPULATIONS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is clearly written, and provides a good background and literature references. I felt like a lot of the technical details regarding the analysis (e.g. choice of gamma parameter) disrupted the flow of the manuscript. I would significantly shorten these parts of the "Results" section and defer the more detailed description to the "Materials and Methods"and supplement.

Additionally, the use of the word "community" may be confusing to some readers. It is used in this work as a technical term from network science, representing groups that are more likely to be linked (correlated) within a group than between groups. However, for microbiome researchers and ecologists the term is used more generally to describe the full set of taxa that reside in the gut. This is a subtle difference that may be worth clarifying explicitly.
Experimental design: This is an original primary research with well defined questions addressing a current gap in our knowledge. Specifically, the authors ask whether similar groups of correlated microbial taxa are found in the intestinal tracks of distinct groups of people, and whether such groups show similar correlations with host properties.

Sufficient detail are given for these results to be replicated. I would just add references to the QIIME and VSEARCH publications.
Validity of the findings: Overall, this is a well executed study, and the authors do a good job highlighting potential caveats. Nonetheless, I have two main concerns regarding the validity of the conclusions.

First, the authors have made several somewhat arbitrary choices in the analysis. These include the choice of the ensemble methods for inferring correlations, fit to a scale-free networks for determining p-values threshold, procedure for picking gamma, use of unweighted networks that don't account for the magnitude of correlations, and the use of different multiple-hypothesis corrections for different datasets. While these are mostly reasonable choices, the results may be sensitive to some of these choices. It would substantially strengthen the validity of the conclusions if they can be shown to be robust to variations in these arbitrary choices. I realize that changing these details would affect the specifics of the networks and detected communities, but the robustness of the qualitative conclusions should be assessed.

Second, I am concerned that many of the detected communities do not represent biologically meaningful groups of correlated taxa, but rather artifacts associated with sequencing errors and chimeras. The authors could try and control for such effects by grouping OTUs with a lower identity threshold, using closed-reference OTU calling, and focusing on communities composed of phylogenetically-diverse taxa.
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: DETECTION OF STABLE COMMUNITY STRUCTURES WITHIN GUT MICROBIOTA CO-OCCURRENCE NETWORKS FROM DIFFERENT HUMAN POPULATIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Please remove extra "the" at the beginning of the abstract.

Line 560 - Bifidobacterium - should be in italic.
Experimental design: No comments
Validity of the findings: No comments
Additional comments: All remarks have been addressed thoroughly.


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: DETECTION OF STABLE COMMUNITY STRUCTURES WITHIN GUT MICROBIOTA CO-OCCURRENCE NETWORKS FROM DIFFERENT HUMAN POPULATIONS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: I thank the authors for their detailed response, adding details, clarifications, and novel analysis that has mostly addressed my main concerns. Nonetheless, I still feel there are a few places where showing that the results are more robust to some of the thresholds would strengthen the findings. In addition, providing more details about the choice of thresholds (as detailed below) would help others implement this analysis on additional datasets.

Specifically, I appreciate the authors' points regarding the utility of picking a p-value threshold based on the fit to a scale-free network. However, it still seems warranted to check the sensitivity of results to the selected p-value, as should be done for any other method for picking thresholds. For example, I would be concerned if analysis based on a different p-value threshold, say 0.005, that fits a bit worse to a scale-free network results in very different communities that are not conserved across datasets.

In addition, in these datasets, it was fortunate that a single p-value threshold offered good fit for all datasets, and resulted in approximately the right slope (This seems very fortunate indeed, given the erratic behavior of the fit for the Israeli-PN dataset). But what should be done if such a threshold does not exist? Should a different threshold be chosen for each dataset? What if several thresholds fit? What should be done if one threshold offers a better R2, while another a slope closer to the desired one?

Similarly, there is no unique, obvious choice of gamma threshold. The authors very reasonably pick a threshold that results in reproducible communities and statistically significant modularity. However, looking at Figure 3, other values may serve as well, say 0.2. I would be more confident in the results if the authors checked how sensitive are results to this choice, and elaborate on how exactly it is made in this case and in general (as above, when no single threshold fits all datasets, and there are trade-offs between reproducibility and significance within datasets).
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: MOVING TO 3D: RELATIONSHIPS BETWEEN CORAL PLANAR AREA, SURFACE AREA AND VOLUME
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall this paper provides valuable research into the growing field of photogrammetry from SfM in marine environments. The methodology is sound, and the use of planar conversions could be a helpful tool for management purposes. However, this paper suffers from a lack of cited literature that relates to the field of photogrammetry from SfM in coral reefs. Please see below for comments:

The submission adheres to all PeerJ policies.

The article must be written in English using clear and unambiguous text and must conform to professional standards of courtesy and expression: In general this is true, though there are some minor errors in the way the introduction is structured.

Lines 7-8: making this statement at the end of the first paragraph is confused, it would fit better towards the end of your intro.

The article should include sufficient introduction and background to demonstrate how the work fits into the broader field of knowledge. Relevant prior literature should be appropriately referenced.

This is primarily where the article falls short. Numerous times throughout the introduction (primarily lines 61-81) false statements are made regarding the efficacy or use of photogrammetry/SFM. For example, lines 63-66 ignores recent published studies, e.g. Raoult et al., 2016, Ferrari et al., 2016, Figueira et al., 2015, Storlazzi et al., 2016, Lavy et al. 2015 that all use photogrammetry/sfm to measure 3D aspects of coral reefs. All these studies use low-cost imagery techniques (action camera or digital camera in dive housing) to produce metrics from corals/coral reefs. The paragraphs lines 61-81 need to be heavily revised to take into account the recent developments of the use of SfM for managing coral reefs.

The definition of photogrammetry lines 68-69 is inaccurate: photogrammetry does not include building models. This is what structure from motion does (hence why the authors use VisualSFM first and a model measuring tool second).

The statement lines 78-81 is false: there are numerous published studies that use open-access software or freeware to study coral colonies (i.e. Lavy et al. 2015, Gutierrez-Heredia et al. 2016, Figueira et al. 2015, Agudo-Adriani et al. 2016).

Lines 78-81: I would add a caveat to this sentence. While open-access software is available, it is generally less user friendly, less streamlined in processing (i.e. requires three separate types of software) and the computational requirements are often greater than off-the-shelf SfM specific payware (an issue that the authors appear to run into). Numerous studies have turned to Agisoft Photoscan for SfM processing (i.e. Raoult et al. 2016, Burns et al. 2016, Burns et al. 2015) as the most efficient all-in-one software (SFM to measurement), and some studies have turned to creating their own algorithms (i.e. Ferrari et al. 2016).
Experimental design: Lines 117-118: It is not made explicit whether corals were taken out of their natural environment (i.e. pictures taken in the air or underwater). This is important because immersed cameras in dive housing generally have higher indices of reflection, which can distort images. If a dive housing was used, provide the model. You also provide a lens (18-55mm) but do not state at what focal length the images were taken. This can have an impact on the accuracy of SfM models if it is not corrected appropriately.

Lines 125-127: What is the rationale for zooming in (I assume 'cropping' is the intended meaning)? Is it just to reduce processing time by having fewer points to align?

Figure 2: The bottom image with SfM models needs to be re-aligned, it looks messy (partial overlap). Include a) b) c) on the image itself rather than only in the caption.

Lines 159-163: It does not appear that any corrections for lens distortion were made. This can have an impact on the accuracy of SfM, and should at least be stated.

Citations are inconsistent and/or have errors throughout the manuscript. Please ensure you use a consistent referencing style and check for errors.

Line 159: Error in citation (should be Wu et al., 2011).

Line 171: Error in citation (should be Jorstad et al., 2014)

Line 171-173: This sentence is confusing and needs to be reworded. It would also fit better after the sentence lines 173-174.

Line 220: Should be "The model" rather than "model"

Linees 249-250: Put spaces between = signs. Include all the statistical information (df, statistical value)
Validity of the findings: The conclusions (lines 275-275) need to be worded more precisely. You found a planar relationship with 3D structure, however, it appears many of your corals were small in size, and as a result your planar area would be closely related to volume or TSA/LSA. If, however, you measured a very vertical colony (i.e. a highly branching species), a planar image would greatly underestimate TSA and volume. Perhaps underline that these models are valid for small colony sizes? Line 80 you talk about measuring corals on a large scale, yet you have not done so in this study. Be careful making broad statements like this.

Do not interchange photogrammetry and SfM throughout your text. Photogrammetry is the measurement of points within models, SFM is how those models are constructed. You should generally refer to 'SFM models' and 'measurements using photogrammetry'

Lines 286-289: You can reliably increase the resolution of SfM models by increasing the resolution of the camera, taking more pictures at various distances, or within the program itself (this is where VisualSFM falls short, because you have little control over resolution settings).

Paragraph line 295: You state there are issues with processing time. It would be very beneficial to provide the specifications of the computer used to construct the point clouds in the methods and to provide a range of processing time (if available). Again, VisualSFM does not use graphics processors in PCs that can more than halve the processing time. Again, do not use photogrammetry so liberally: you generally mean SfM in this paragraph.

Line 303-305: This statement needs greater consideration of the benefits of streamlined software designed for this task (you can get the same measurements in Agisoft Photoscan with 4 steps and a dozen or so human inputs).

Lines 304-307: It's hard to foresee a situation where the costs (financial? labour? time?) for SfM would be so great as to suggest planar extrapolation given the benefits of 3D measurements over planar ones. I think the benefit of this technique would primarily be for historical data that has already been retrieved.

line 308: again, photogrammetry is not a 3D technique, you mean SfM here

Lines 309-310: This is a crucial statement. The issues with SfM are generally from the camera end rather than the processing end

Line 313: Laser scanners are definitely becoming more financially viable, but they don't obtain information on living or dead coral. I'm also not sure what the benefit of stereo cameras would be in this application, since they generally are processed with SfM anyway.

Paragraph line 316: Yes, this entire paragraph is what you should focus on. I think it would be better placed just after the first paragraph in your discussion. It also has a bit of a nonsensical statement: if you are taking planar images of coral, presumably it is not necessary to record morphotype.

Paragraph line 327: it may be relevant to discuss classification of corals here, as recent projects focus on coralite structure for classification (i.e.  Coral Finder) as opposed to traditional morphotypes.

Conclusions: Need to reword line 356, as the shift is already occurring (see citations provided)
Additional comments: Citations that are relevant and should be included in this paper:

Raoult, V., David, P.A., Dupont, S.F., Mathewson, C.P., O’Neill, S.J., Powell, N.N. and Williamson, J.E., 2016. GoPros™ as an underwater photogrammetry tool for citizen science. PeerJ, 4, p.e1960.

AGUDO-ADRIANI, E. A., CAPPELLETTO, J., CAVADA-BLANCO, F. & CROQUER, A. 2016. Colony geometry and structural complexity of the endangered species Acropora cervicornis partly explains the structure of their associated fish assemblage. PeerJ, 4, e1861.

BURNS, J., DELPARTE, D., GATES, R. & TAKABAYASHI, M. 2015a. Integrating structure-from-motion photogrammetry with geospatial software as a novel technique for quantifying 3D ecological characteristics of coral reefs. PeerJ, 3, e1077.

BURNS, J., DELPARTE, D., GATES, R. & TAKABAYASHI, M. 2015b. Utilizing underwater three-dimensional modeling to enhance ecological and biological studies of coral reefs. The International Archives of Photogrammetry, Remote Sensing and Spatial Information Sciences, 40, 61.

BURNS, J., DELPARTE, D., KAPONO, L., BELT, M., GATES, R. & TAKABAYASHI, M. 2016. Assessing the impact of acute disturbances on the structure and composition of a coral community using innovative 3D reconstruction techniques. Methods in Oceanography.

FERRARI, R., BRYSON, M., BRIDGE, T., HUSTACHE, J., WILLIAMS, S. B., BYRNE, M. & FIGUEIRA, W. 2016. Quantifying the response of structural complexity and community composition to environmental change in marine communities. Global change biology.

FIGUEIRA, W., FERRARI, R., WEATHERBY, E., PORTER, A., HAWES, S. & BYRNE, M. 2015. Accuracy and Precision of Habitat Structural Complexity Metrics Derived from Underwater Photogrammetry. Remote Sensing, 7, 16883-16900.

GUTIERREZ-HEREDIA, L., BENZONI, F., MURPHY, E. & REYNAUD, E. G. 2016. End to End Digitisation and Analysis of Three-Dimensional Coral Models, from Communities to Corallites. PLoS ONE, 11, e0149641.

LAVY, A., EYAL, G., NEAL, B., KEREN, R., LOYA, Y. & ILAN, M. 2015. A quick, easy and non‐intrusive method for underwater volume and surface area evaluation of benthic organisms by 3D computer modelling. Methods in Ecology and Evolution, 6, 521-531.

STORLAZZI, C. D., DARTNELL, P., HATCHER, G. A. & GIBBS, A. E. 2016. End of the chain? Rugosity and fine-scale bathymetry from existing underwater digital imagery using structure-from-motion (SfM) technology. Coral Reefs, 1-6.