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

Input:
Title: A MATHEMATICAL LANDMARK-BASED METHOD FOR MEASURING WORN MOLARS IN HOMINOID SYSTEMATICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is very well written with only a few grammatical errors (see below for the few that I noticed). Figure 1 is especially useful in helping to understand the landmarks that the authors collected data on. Overall, I would strongly support this paper being published.

 Grammatical edits:
1. On line 264, add 'and' before 'orientation'.
2. On line 383, add 'to' before '95%'.
3. On line 384, change 'cross-validated to 91%' to 'with cross-validated accuracy being 91%'.
4. On line 387, add 'and' before '60%'.
5. On line 425, change 'This' to 'The'.
6. On line 441, change 'the' to 'this'.
7. On line 530, change 'to' to 'with'.
Experimental design: Based on the results provided (especially the high classification accuracy achieved both at the species and subspecies level) the innovative and creative methods developed by the authors have great potential to be used to document the morphology of worn molars in taxonomic and phylogenetic studies of extant and fossil hominoids and, thus, could significantly increase the number of specimens available for analysis, as the authors appropriately note in their discussion and conclusion. Moreover, the methods require little in the way of technology and are easily replicated (with little subjective decision-making required in the placement of landmarks), making them more readily available to researchers with fewer resources and/or institutional support. Consequently, this submission has the potential to be extremely impactful in the field of dental anthropology and hominoid systematics given how analyses of molar morphology generally do not include well worn molars, which can substantially lower sample sizes. However, there are a number of issues that, if addressed, would improve the manuscript further (see below).

1. On line 90, I would rephrase the sentence that mentions Type I landmarks to read 'These anatomical landmarks, which are classified as Type I (Dryden & Mardia, 1998)...' Also, I believe that Bookstein, 1990 was the author that initially developed the system of classifying landmarks into types I-III.

2. While I understand the authors' reasoning for using relatively unworn molars in this study, it would have made their study even stronger to provide some proof of concept that worn molars can also be accurately classified using these methods. I understand that the landmarks they collected data on are unlikely to be affected by wear, but it is a bit odd to be arguing for the use of these methods for classifying worn molars when no worn molars were included in the analysis. I realize that this may entail a substantial amount of work and if the authors (and editor) think that this is unnecessary for this paper, I would suggest adding a line or two about conducting a follow up study in the discussion and/or conclusion.

3. I am not clear how landmarks 21-25 necessarily mark the 'mathematical center of each cusp' given that landmark 1 is in the mathematical center of the molar and, thus, will not be on the margin of each cusp (i.e., the line drawn from landmark 1 to landmarks 16-20 may include parts of other cusps or only a portion of the cusp in question depending on where landmark 1 is placed and, consequently, landmarks 21-25 will not be at the center of the cusp in most cases). I would argue for naming those landmarks using a different phrase.

4. Can the authors provide a brief explanation of why they selected the nine measurements they decided to include in this analysis and not other measurements?

5. From the discussion of the methods, it is not entirely clear whether the data collected for the anatomically-based methods were collected by the authors on the same specimens that they collected the data using mathematically-based methods on. I believe they were, but this should be made clearer in the manuscript.

6. I would argue for changing the names of measurements 2 and 3 in Table 3 to 'Buccolingual breadth at the mesial and distal cusps'. Also, should the names of measurements 5 and 6 start with 'Length of'? In the description of measurements 7 and 8, it appears that the authors are stating, for example (for measurement 7), landmarks 21 through 25 when I believe they mean to say landmarks 21 and 25 (there is a similar issue throughout the descriptions of these landmarks). Finally, the description of measurement nine is not clear to me.

7. I would suggest adding a legend to figures 5 and 6 denoting in one box what taxon each of the symbols represents. Also, the authors should orient the reader as to which direction on the wireframes is mesial, distal, etc.

(see next section for additional suggestions/comments)
Validity of the findings: 8. Have the authors examined their data to determine if any four or six cusped individuals are outliers?  One would expect that if this method accurately documents morphological differences within taxa for molars with different numbers of cusps that they would be clearly separated from others in their group. The authors even state on lines 468-474 that one of the reasons that shape variation was greater in humans than in great apes in this study was the absence of a hypoconulid in some human specimens, but did they assess whether these teeth were significantly different in shape using their landmark data?

9. With respect to the inter- and intra-observer error studies, can the authors provide more information? First, they cite the maximum differences in tilt angles along each plane, but do not discuss the extent to which this might have affected the placement of landmarks and, thus, their results. Was there a study done to examine this latter issue? Second, while they provide data on the mean deviation in the x and y axis for landmarks, they do not discuss the extent of intra-observer vs. inter-observer error. Also, these data should be contextualized. For example, the authors could note how large the error was compared to the distances between landmarks or compared to the distance differences between individuals in a single taxon. In other words, could this error have impacted the results of this study (granted, this seems unlikely given how small the error appears to be)?

10. I am confused as to how the classification accuracy of the mathematically-based methods for the comparison with Skinner et al.'s data was so much higher than it was when the larger sample was compared to Pilbrow's data (especially given that data were collected on the same variables and same taxa). Can the authors discuss this?
Additional comments: Minor points:
1. I would argue for reporting the classification accuracy with cross-validation in the abstract as that is the more statistically valid measure.
2. While I realize that it may not be technically inaccurate, I would prefer the use of 'taxonomic' rather than 'taxonomical'.
3. I would change 'populations' in line 192 to 'individuals'.
4. Shouldn't 'subjectivity' on line 524 be 'objectivity' instead?
5. In table 2, a space should be added between the information for landmarks 27 and 28.


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: BOAT ANCHORING CONTRIBUTES SUBSTANTIALLY TO CORAL REEF DEGRADATION IN THE BRITISH VIRGIN ISLANDS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: My primary concern relates to the classification of sites into high, medium, and low anchoring categories. While I was initially impressed by the use of a combination of local experts and satellite images, there were inconsistencies in the data from these two sources. For example, Long point and Monkey point are categorized as “medium” (per the recommendation of local experts), but zero boats were observed in satellite images, implying an absence of anchoring pressure at these sites. Moreover, eight boats were counted in satellite images of “low” anchoring Lee Bay, and two boats were counted in satellite images of “high” anchoring Crab Cove. These inconsistencies suggest that there is not enough justification for how sites were classified, and this needs to be improved. Furthermore, it was concerning that the values given for the number of sites in each category -among the text (Line 72-73), figures (Fig 1), and data (AnchHistGE.csv)- did not match. Please clarify how many sites were in each category, perhaps with a table listing each site, and which paired “group” and anchoring category it fell into. Finally, low and medium anchoring sites look to be statistically indistinguishable (Fig 2). What was the reasoning for distinguishing between them?

Additional Comments:

Line 86: What point was used to determine distance to shore? Each site is an embayment, which by definition is surrounded by shore. Was the reef used as the origin point? If so, how far was each reef to where boats were actually anchored?

Lines 118-120: Specify how fish were categorized into feeding guilds and juvenile/adult.

Lines 122-148: The description of statistical analyses was very confusing; please re-word for general clarity, and specify which tests were used for each variable.
Validity of the findings: The discussion contained a nice synthesis of the findings with existing literature, but there was not enough mention of the limitations of this study. Though some factors (such as depth, distance from shore), were controlled for, it is difficult to decouple the effects of anchoring from other human impacts. More boats mean more anchor damage, but also perhaps more fin-strikes by snorkelers and scuba divers, sewage/littering, and chemicals leaching from boat-bottoms. These factors have all been implicated in local-scale harm of reef-associated biota (Donohue et al. 2001; Dearden et al. 2010; Burgin and Hardiman 2011[cited in ms]; Titley-O’Neal et al. 2011; Webler and Jakubowski 2016; Renfro and Chadwick 2017). Similarly, it is too speculative to say that chronic boat anchoring “caused” the observed reductions in coral and sea fan abundance (to paraphrase lines 332-333); all declarations of causation should be replaced with language that is more representative of the tests that were conducted.

Additional Comments:

Lines 300-302: There also may be other factors controlling juvenile fish density, such as the presence of nearby seagrass, even at high anchoring sites.

Lines 302-303: There is no mention of these groups in the results.

References:
Dearden P, Theberge M, Yasue M (2010) Using underwater cameras to assess the effects of snorkeler and SCUBA diver presence on coral reef fish abundance, family richness, and species composition. Environ Monit Assess 163:531–538. doi: 10.1007/s10661-009-0855-3

Donohue MJ, Boland RC, Sramek CM, Antonelis GA (2001) Derelict fishing gear in the Northwestern Hawaiian Islands: Diving surveys and debris removal in 1999 confirm threat to coral reef ecosystems. Mar Pollut Bull 42:1301–1312. doi: 10.1016/S0025-326X(01)00139-4

Renfro B, Chadwick NE (2017) Benthic community structure on coral reefs exposed to intensive recreational snorkeling. PLoS One 12:e0184175. doi: 10.1371/journal.pone.0184175

Titley-O’Neal CP, MacDonald BA, Pelletier E, Saint-Louis R, Phillip OS (2011) The Relationship Between Imposex and Tributyltin (TBT) Concentration in Strombus Gigas from the British Virgin Islands. Bull Mar Sci 87:421–435. doi: 10.5343/bms.2010.1093

Webler T, Jakubowski K (2016) Mitigating damaging behaviors of snorkelers to coral reefs in Puerto Rico through a pre-trip media-based intervention. Biol Conserv 197:223–228. doi: 10.1016/j.biocon.2016.03.012
Additional comments: My general response to this manuscript was positive, and I especially appreciated the inclusion of less traditionally popular groups like soft branching corals, sea fans, and sponges in the surveys. With careful revision, this manuscript could be reconsidered for additional review. Below I offer some additional general comments:

Lines 149-260: The amount of parenthetical text/data made this section very difficult to read. The parenthetical information pertaining to statistical tests, which sometimes occupied up to four lines (Lines 191-194), could be moved to a table.

Lines 155-161: Consider moving these sentences to the section describing rugosity (Lines 220-224).

Lines 181-218: This gets redundant, especially because differences in surface area and density are the same, regardless of whether corals are grouped by morphology or taxonomically by genus, and they also reflect the total coral results as a whole.

Line 184: The accepted classification is Montastrea cavernosa (WoRMS 2019).

Fig 1: Please consider labelling the major islands (e.g., Tortola, Virgin Gorda). It may also be helpful to add abbreviated site labels, or markers distinguishing paired groups.

Fig 2: Please remove the caption information about multiple comparison letters, and where map data are from, since there are no letters or maps in this figure.

Fig 5: Please change “proportional bottom cover” to “rugosity” in the figure caption.

References:

WoRMS (2019). World Register of Marine Species. Available from: http://www.marinespecies.org/aphia.php?p=taxdetails&id=287962


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: BOAT ANCHORING CONTRIBUTES SUBSTANTIALLY TO CORAL REEF DEGRADATION IN THE BRITISH VIRGIN ISLANDS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a very well-written and straight forward manuscript that assesses the damage anchoring boats have caused to coral reefs of the British Virgin Islands. It reports the results of an extensive field survey of 25 reef sites, quantifying benthic community structure, physical reef structures, and associated ecosystem functions such as providing fish habitat.  They found clear and unambiguous evidence of substantial damage across all measures.
Experimental design: This Ms clearly falls within the scope of the journal and fill a well-defined knowledge gap.  Truly, when I first read this, I was doubtful that this question had not already been addressed fully.  I know that boat moorings have been placed in popular anchorages throughout Biscayne and US Virgin Islands National Parks, and I assumed that was in response to studies of anchor damage.  I also know that the US Park Service in the USVI has long-term survey data around many of their moorings on St John as I have seen these data.  However, they are all on sandy substrates covered in seagrasses, including an invasive species.  To my surprise, the documentation of damage of anchoring to hard bottom habitat appears to be sparse as the authors suggest.  This research is rigorous and the methodology complete
Validity of the findings: As stated above, the data are strong and well analyzed.  The single criticism I have is that the presentation of the statistical results as parenthetical statements make this Ms really hard to read and follow. I am an ecologist, so I am used to this type of reporting, but even for me, it was too much. For a more genera audience, I fear this is prohibitively distracting.  I think these statistics need to be moved to a table, where those that are really interested can study all of the details.  I understand that there are a lot of different transformations and analyses due to the nature of the data, so a creating an appropriate table is not trivial.  However, I think it is key to make the Ms more digestible to a general audience
Additional comments: I think this Ms is of broad enough scope that it merit publication 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: BOAT ANCHORING CONTRIBUTES SUBSTANTIALLY TO CORAL REEF DEGRADATION IN THE BRITISH VIRGIN ISLANDS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is well composed and readable. The introduction provides a nicely constructed background for the study, includes relevant literature, and the objectives and hypotheses are clear. The study fills an important knowledge gap about how boat anchoring translates to coral reef benthic cover and structure.

The structure of the article meets the journal’s standards, and the figures are relevant. I have a few suggestions to improve readability:

Results – this section was difficult to read as it is composed more like a list of tests than a narrative of results. Perhaps you can add some of these results as tables and refer to them that way, and use this section to highlight the most important results.

Table 1 – spaces in between the mean and ± would make it easier to read
Figure 1 – need to indicate in some way the location of the map (e.g., include latitude/longitudes).
Figure 3 caption – remove ‘Plotted are’
Figure 4 – fix superscript in y-axis labels
Figure 6 – right hand side of the figure is cut off in the pdf

Also, the data used in the analyses are attached, but could benefit from some data descriptors/metadata. Please describe what each file consists of, what data are in each column, what are the units, etc.
Experimental design: The data were collected in a sound manner, and statistical analyses were appropriate to the data and questions being invested. A potentially minor issue is that I found the classification of low-medium-high boat traffic to be a bit circular. These classifications were made by ‘expert opinion’ and then later backed up by counting boats in satellite images. Why not use the counts to classify the sites? Low/medium sites didn’t have a significant difference in #boats (Fig 1), so perhaps the analyses should lump the low/medium sites? Would that change the conclusions?

Line 306 – reference to Jackson et al here not the best reference as we didn’t explicitly test this. I suggest referencing Adam et al 2015 MEPS:520 for a review of the topic.
Validity of the findings: The authors did a nice job of tempering their conclusions given that they could not assess the effects of boat anchoring in the context of other anthropogenic stressors, and the conclusions were well justified by the results.

Overall the study was well thought out, the manuscript was nicely composed, and I have relatively few and minor comments such that I recommend the publication of this study.
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: BOAT ANCHORING CONTRIBUTES SUBSTANTIALLY TO CORAL REEF DEGRADATION IN THE BRITISH VIRGIN ISLANDS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: The authors greatly improved the methods section, and the new table is a good addition. I also appreciate the further justification of sites into their respective anchoring categories, and description of the rationale for choosing a "medium" anchoring category. However, I did notice some incorrectly defined/labeled terms while going through this revised ms. First, the standard error is incorrectly defined in lines 170-171, and this is the definition of the standard deviation. The standard error = standard deviation divided by the square root of the sample size. Similarly, the error bars in the bar graphs show the 95% CI, not the standard error. I recommend correcting the bar graphs so that error bars represent SE, as this is more relevant for comparing groups.
Validity of the findings: The authors have done a nice job of addressing the limitations of their study, and rephrasing some of their previously speculative language.
Additional comments: This revised manuscript is much improved, and I agree with the other reviewers that this work addresses an important knowledge gap, and aligns with the scope of the journal. After the minor revisions mentioned above, I consider this manuscript ready for publication.


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

Input:
Title: THE BRAINCASE OF MESOSUCHUS BROWNI (REPTILIA, ARCHOSAUROMORPHA) WITH INFORMATION ON THE INNER EAR AND DESCRIPTION OF A PNEUMATIC SINUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The MS provides new anatomical information on the braincase of the early diverging rhynchosaur Mesosuchus browni based on the mCT data from the superb skull SAM-PK-6536. The most interesting result is the identification of pneumatic sinuses reported for the first time in this group. Such findings have important implications for the evolution of the pneumatic systems in Archosauromorpha. I detected which I consider problems that should be addressed before final publication.
I am not a native speaker, and I did not conduct a revision of the language. However, as far as I can tell, the MS employ proper scientific writing. The MS presents adequate background and a sufficient introduction to contextualize the new finding in the broader field of knowledge. In general, the relevant literature is appropriately referenced.
Experimental design: Apart from the lack of adequate comparison to other rhycnhosaurs and the pneumatic sinuses and ear of crocodylians, the investigation was conducted rigorously (see below).
Validity of the findings: One central aspect that needs improvements is the comparison to other taxa in the discussion section. The comparison among rhynchosaur is basically restricted to information provided by Benton (1983). There is no adequate comparison to Rhynchosaurus articeps, Stenaulorhycnhus, Hyperodapedon and Teyumbaita. The comparison to the taxon Eohyosaurus is limited yet the MS provide the reconstruction of its braincase.
The same lack of comparison is detected regarding the pneumatic sinuses and ear. The MS includes comparison to theropods but not to crocodylians. We have a fairly amount of information available on the pneumatic sinuses and ear of crocodylians (e.g. Tahara & Larsson 2011, Dufeau & Witmer 2015). Such comparison would greatly strengths the importance of the findings.
Given the position of Rhynchosauria outside crown-Archosauria, the comparison to lizards would also be informative.
In addition, the authors compare the new findings to Scaphonyx. However, Scaphonyx is considered a nomen dubium. The authors should provide the rationale behind the comparison to Scaphonyx.
Additional comments: One reservation I have about the paper is the quality of the line drawings. In the present form, the line drawings do not help on the evaluation of the anatomical information provided in the description. I recommend improving the line drawings. I also suggest some features to be highlighted in the figures (foramina for the cerebral branch of the internal carotid arteries, “crests 1-3”, recessus stapedialis, “two small fossae on the opisthotic”, perilymphatic notch, obliterated external foramina), and the addition of a figure of the ventral view of braincase.
All figures lack scale. Please, include scale to the figures.
Line 43. Previous papers also had referred rhynchosaurs as “pig-like cretatures” but it does not deliver the true picture about the group diversity. The group also includes tiny taxa such as Rhynchosaurus articeps with the approximated size of an agouti, and Brasinorhynchus which probably exceeded the size of a tapir. Although, it does not have a real impact on the scientific merit of this MS, it is an oversimplified view of rhynchosaur diversity.
Line 44. Mesosuchus does not present tooth plate nor beak-like premaxillae.
Line 48. Actually, rhynchosaurs became important faunistic components worldwide during Mid-Late Triassic (Schultz et al. 2016, Ezcurra et al. 2016).
Line 49. At least Teyumbaita crossed the Carnian-Norian boundary (Butler et al. 2015, Schultz et al. 2016, Montefeltro et al. 2010, Ezcurra et al. 2016).
Line 87. Please provide the full spelling of the institutional abbreviation.
Line 94-97. I am not sure if I understood the possible divergence between the Author’s opinion and Ezcurra’s opinion on the height of the braincase. In my opinion it all depends on the real articulation of the braincase to the skull. I suggest the author to elaborate more this possible divergence of interpretation.
Line 266. I failed to recognize the remarkable differences proposed between the braincase of Stenaulorhynchus and Mesosuchus. Please, elaborate it.
Line 287. I suggest to elaborate more on the reasons of the proposition of Mesosuchus hearing adapted to low-frequencies sounds.
Line 291. I am interested on the evidences to suggest that rhynchosaurs did not have tympanic membrane.
Line 321. I would like to see more evidences for the statement: “It is safe to postulate that Mesosuchus had an even more erect posture and was more active than both rhynchosaurs”. I failed to see the connection to the skeletal reconstruction from Dilkes (1998).
Line 366. Montefeltro et al. 2010 described a distinct depression of the exoccipital in Teyumbaita, which have topographical correspondence to the small fossae on the opisthotic.
Caption of figure 1. Specimen number is wrong.
Caption of figure 8. It is missing the PNS.


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

Input:
Title: THE BRAINCASE OF MESOSUCHUS BROWNI (REPTILIA, ARCHOSAUROMORPHA) WITH INFORMATION ON THE INNER EAR AND DESCRIPTION OF A PNEUMATIC SINUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: General Comments: This paper presents a significant advance in our knowledge of an important Middle Triassic archosauromorph represented by specimens that are wonderfully amenable to recent advances in non-invasive imaging such as micro CT scanning. The unexpected presence of pneumatic sinuses in the braincase and details of the inner ear hold great promise to inform phylogenetic hypotheses and enhance our understanding of the biology of Triassic reptiles.

Specific Comments:
Abstract. It’s common to describe rhynchosaurs as pig-like, but this really only applies to the later genera. Mesosuchus has more of a lizard-like body shape than that of a pig.

Introduction.
Line 45. Herbivory was likely true for later rhynchosaurs (perhaps including Howesia), but there is little to suggest such a diet for Mesosuchus. Mesosuchus seems more like an insectivore.
Line 46. The earliest record for rhynchosaurs is the Early Triassic, but the presence of the archosauriform Archosaurus in the Late Permian pulls the lineage back to an origin in the Late Permian.

Description.
Lines 95-97. Yes, the braincase is certainly not transverse. The dorsoventral orientation is also evident in Figure 2C & D of Dilkes (1998).
Lines 129-131. The description of the dorsum sellae in Dilkes (1998) was based on SAM-PK-6536. Although the middle region is not completely present, it was evidently a tall structure.
Lines 132-133. The median ridge described in this line is labeled in Figure 3B, not 3A.
Lines137-142. There is confusion here due to my poor writing regarding the crista ventrolateralis. As I understand it, the term should have been used to describe the ridge between the basal tuber and basipterygoid process with a posterior extension that contacts the basal tuber portion of the basioccipital. The crista ventrolateralis is a part of the amniote braincase. Do the authors identity it in Mesosuchus?
Lines 15-151. Can the two crests “crest 1” and “crest 2” be labeled in a figure?
Lines 152-154. Would it be better to describe it as being initially anterodorsal to the foramen for CNVII and reaches the anteroventral side of this foramen as it extends ventrally?
Line 193. “…external foramina of the of the vena capitis dorsalis…” should be changed to remove one of “of the”.
Line 196. “Ventral do it…” should be “Ventral to it…”
Lines 204-206. Dilkes (1998) did describe a pair of foramina for CNXII in a deep fossa on the lateral side of the exoccipital.
Lines 210-212. Choice of words to describe the shape of the stapes has clear implications for impressions of function. Calling it stout automatically implies in the mind of the reader poor ability to conduct high frequency sounds (a function presumably restricted to a slender stapes). Why is this stapes stout rather than slender? The width of the shaft does not appear to be markedly different from the width of the head described by the authors as small. What anatomical criteria are the authors using to distinguish between stout and slender?
Line 290. “…although no mention to it…” should be changed to “…although no mention of it…”.

Figures.
Figure 2. The figure has bo.rd that is clearly a combination of labels bo and rd. Should have bo.rd as an abbreviation in the figure caption. Similarly, st.bo.ps should be one of the abbreviations.
Figure 3. Label on figure is cr3, but figure caption has c3.

References.
The following papers listed in the References could not be located in the body of the paper or figure captions:
Brusatte et al. (2016)
Cordorniú et al. (2016)
Dzik (2003)
Gow (1975)
Hungerbühler et al. (2012
Kubo and Benton (2007
Marugaán-Lobón et al. (2013)
Nesbitt (2007)
Sereno et al. (2007
Thewissen and Nummela (2008)
Witmer et al (2003)

Thank you for the opportunity to review this manuscript. It's nice to see another example of how new technology can be used to correct errors in past papers and provide significant new anatomical information.


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

Input:
Title: THE BRAINCASE OF MESOSUCHUS BROWNI (REPTILIA, ARCHOSAUROMORPHA) WITH INFORMATION ON THE INNER EAR AND DESCRIPTION OF A PNEUMATIC SINUS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a generally very well done manuscript that does a good job of describing and interpreting the morphology of the braincase of the basal rhynchosaur Mesosuchus. The structure of the manuscript is fine. The English is also generally very good, but could benefit from a close read by an editorial eye.

As for the figures:
1. The Introduction needs a cladogram with all of the taxa mentioned in the manuscript, as well as the nodes, if only so the reader can get a sense of the phylogenetic framework. Many taxa are mentioned, which is good, but we need to know how they all fit together, even if just plotted on someone else’s tree. This is required in my view.
2. The inner ear isn't reconstructed in isolation and compared with other relevant species, and such a figure would seem to be not only possible but absolutely necessary. It’s almost promised by the manuscript’s title.
3. The photos in Figures 2 and 3 are very hard to interpret because the lighting is nonstandard and many important features are in dark shadow. The interpretive line drawings also aren't very helpful and they're not extensively labeled.
4. The 3D volume renders of the skull are quite muddy and dark. It's hard to see detail. Moreover, considerable detail is lost in the dark, raking shadows, which is a persistent problem with rendering in VG Studio Max.
5. In general the figures aren't labeled enough.
6. Figures with slices (e.g., Figures 6 & 8) should have an inset of the braincase showing where the slice comes from. Otherwise, they're very hard to orient, made worse by the fact that they're not labeled very much, and again are very dark and muddy, especially in Figure 8.
7. It’d be very nice to have comparative drawings of relevant taxa showing key features compared to Mesosuchus. It would make the manuscript much more useful.
Experimental design: A CT-based analysis of the braincase of Mesosuchus is highly appropriate and welcomed given the basal position of Mesosuchus within the rhynchosaur clade as well as the basal position of rhynchosaurs within Archosauromorpha. The authors are experts—especially the senior author—in basal archosauromorph braincase structure, and thus this project is on a sound footing. This kind of work hasn’t been before for this clade so it’s absolutely needed.

A major concern, however, is that the authors do not seem to have taken any steps to make the CT scan data available (e.g., on Dryad or MorphoSource). In fact, it was hard for me to do an adequate review of the manuscript without being able to see the scan data. Making the data available on an open-data portal is now expected in that it addresses the need for repeatability and replication. The absence of providing the data actually seems to be a violation of PeerJ policy, although I’m no expert on PeerJ policy.
Validity of the findings: The morphological findings are generally fine although I’ll point out some concerns under General Comments. Again, the figures need some attention. The Conclusions section is generally fine in terms of summarizing some of the major outcomes of the work, although a lot of it pertains to the pneumaticity interpretations about which I’m less confident (see my General Comments).

Also, there’s one statement in the Conclusions—lines 404-406: "The inclination of the lateral semicircular canal indicates Mesosuchus held its head horizontally in relation to the rest of body, also in agreement with previous suggestions."—which is the first time that this point is made. It shouldn’t appear for the first time in "Conclusions," but rather should be presented in more detail in the body of the manuscript. Moreover the statements requires references: "...in agreement with previous suggestions"…whose previous suggestions?
Additional comments: I really liked this manuscript, as it presents very important information about an important species. I think the figures really need to be improved. The manuscript relies extensively on CT-based imagery, which in itself can be okay, but the images here need to be—and I think could be—much better.

Some more specific points are made here:
1. Lines 149-163, 272-280: The sections (there are two) on the braincase crests need some work. First, they’re not well illustrated. Only crest 3 is labeled (Fig. 3) and Figures 4 and 5 would also be possible places to label the crests. Why call “crest 1” anything other than crista prootica (or my preferred term [see below] otosphenoidal crest). This synonymy is not revealed until line 272 and not in the section on the prootic. To be honest, I’m not sure what’s going on with these crests—I wasn’t sure in recent Euparkeria article and I’m not sure here either. Better figures might help, but also seeking really clarity in the text. Function might help, too, since soft tissues are making these crests.
[Aside: It might be useful to note that the “crista prootica” has also been referred to as the “crista otosphenoidalis”—and not just by me. I didn’t invent the term, either, but I prefer it because in many species (including Mesosuchus, apparently), it’s not restricted to the prootic bone but actually runs from the paroccipital process (opisthotic), across the prootic bone, and down to the basipterygoid process of the basisphenoid bone…that is, it’s literally a crest that runs from the otic region to the sphenoid region. It’s an extremely consistent feature that functionally separates the tympanic domain from the adductor and orbital domains.]

2. Line 214: What does "it" refer to? Footplate or fenestra ovalis? Also, how can you not confirm whether the footplate fills the FO. It obviously doesn't in Figure 6

3. Line 218: "The fenestra ovalis is very small..." It looks huge in Fig. 6B.

4. The identification of pneumaticity is a pretty big deal here because it’s so unexpected. The authors themselves seem very tentative at times, and I think that’s fair. I’m not fully convinced either. I’ve devoted a lot of thought (and a lot of ink) to pneumaticity over the years. An important point I’d like to make at the outset is that I have no a priori bias against pneumaticity in Mesosuchus. It’s totally possible, doesn’t conflict with any pet ideas of mine, and would be really interesting. So let’s dig in… Lines 241-242: "...the braincase of Mesosuchus is trabeculate, which makes it difficult to assess the real extension of the system." Yes, it can be very difficult. Lots of extant squamates have a quite open trabecular structure of the skull bones...but they're not pneumatic. The key attribute for pneumaticity is a pneumatic aperture (foramen) that opens to (communicates with) a known air-filled space, like the middle ear or pharynx. Can you identify the aperture in all cases? If not, the case for pneumaticity is weaker. Lines 251-252: "Its external foramina were could not be identified..." Delete "were." Also, it seems very unlikely that the foramina on the occiput lateral to the foramen magnum are the pneumatic foramina. What would be the air-filled space providing the source of the diverticulum? The tympanic cavity isn't there. More on this point below. Lines 343-350: The identification of foramina leading into open spaces is critical for the inference of pneumaticity. The authors report finding foramina in lines 343-344, but then in the next paragraph they say that they don't have foramina. Lines 351-360. The authors identify a putative caudal tympanic recess but lack foramina connecting to the middle ear, which would be the source of the air. I agree that the "obliterated foramina" (are they really obliterated?) are for the external occipital vein, which is highly conserved, but it seems odd to then call it a pneumatic foramen. First, if it's "obliterated" then why would there be a pneumatic space, since in extant amniotes patency of the pneumatic foramen is required for maintenance of the pneumatic space. Second, what would be the source of air passing through the "obliterated foramen"? The choices would be middle ear and lung but both of these seem very unlikely given their distance. Lines 366-368: Fossae on the occiput seem like very weak criteria for pneumaticity. Again, how would a diverticulum of the tympanic cavity get there? Also, what about the cervical musculature? Certainly neck muscles attach to the occiput in this area and could make these fossae. Such depressions for muscular attachment are common. Also, using the "obliterated foramina" of Mesouchus as a basis to infer pneumaticity in other taxa seems unwarranted.

5. Lines 288-289: How does the absence of a quadrate conch and having a robust hyoid relate to low-frequency hearing? References?

6. Line 291: How do we know that "rhynchosaurids lack a tympanic membrane.”

7. Inner ear. The inner ear isn't reconstructed in isolation and compared with other relevant species, and such a figure would seem to be possible. Lines 308-309: "also suggestive of an active animal with a more upright posture." What is the basis of this statement? No reference is provided. Such a statement about activity patterns and posture is quite bold given that the link between inner ear structure and activity and posture have been controversial at best. At a fundamental mechanistic level, the SCC and cerebellar flocculus are associated with sensing head and body movements and coordinating eye movements. Any connection to activity and posture must flow from the neurology, which is indirect at best in this case. Lines 313-321: Comparison to Protoceratops—and certainly the inner ear of Protoceratops—are of doubtful utility given the vast difference in phylogenetic history.


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

Input:
Title: THE BRAINCASE OF MESOSUCHUS BROWNI (REPTILIA, ARCHOSAUROMORPHA) WITH INFORMATION ON THE INNER EAR AND DESCRIPTION OF A PNEUMATIC SINUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors present an improved version of the MS. In the new version, the comparisons are better conducted and most of my concerns had been addressed. However, the MS still contains what I consider minor problems that should be addressed before final publication.
Experimental design: No comment
Validity of the findings: I still think that comparison to lizards would greatly improve the reliability of the generalizations made about the evolution of the pneumatization. However, it is fair if they prefer to restrict the scope to Archosauromorpha.

I failed to see in which manner the basipterygoid process of Mesosuchus is different from Stenaulorhynchus and Rhynchosaurus (lns 262-263). The more developed basipterygoid process is recognized as a plesiomorphy of Rhynchosauria. Only Hyperodapedon and Teyumbaita present a shorter process (see Schultz et al. 2016, Langer et al. 2017 character 52). Please clarify.

Other osteological correlated are proposed for inferring the presence and extension of the Tympanic Membrane in crocodylian lineage (see Montefeltro et al. 2016).
Additional comments: Garjainia prima not in italic, please change (ln 283).

The pictures of the braincase in figures 3 and 4 are too bright in the pdf version of the revised MS. If this is intended for the final version, it should be re-worked.


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

Input:
Title: THE BRAINCASE OF MESOSUCHUS BROWNI (REPTILIA, ARCHOSAUROMORPHA) WITH INFORMATION ON THE INNER EAR AND DESCRIPTION OF A PNEUMATIC SINUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: This new version of the manuscript is much improved. I’m grateful to the authors for providing access to the CT scan data because it was indispensable and made possible an adequate assessment of the morphology. As before, the manuscript is well written, and the basic structure of the manuscript is very sound.

Thank you for adding the new Figure 1 in that the cladogram will be very helpful for those less familiar with the group…like I was with the first review…I’ve since dug into the rhynchosaur literature a lot more than I did the first time. I also appreciate the authors’ adding more labels to the line drawings.

However, the authors chose not to change the figures very much and some of the changes are now for the worse. I was hoping for better versions of the photographs in Figs 3 and 4 but it looks like they just decreased the contrast in a very coarse way such that they now just look washed out. It didn’t help and they now look worse. If the first versions are the best that can be done then so be it, although if photos can’t be reshot then maybe some skillful application of Photoshop might be able to make the photos more useful. If not, then the first versions are preferable.

I appreciate that the authors generated new versions of the 3D volumetric renders of the braincase in Figs 3–6, but these also seem blown out and with no shadows or contrast; they look like flash photographs of white plaster casts. Once again, I think the first versions are preferable. Having worked with the dataset now myself, I understand that it’s a little tricky, but maybe they could try again. Likewise, the slices in Fig 7 are a little blown out whereas they’re pretty nice in Fig 9. I was disappointed that the authors decided not to take my recommendation to have a separate inner ear figure. Figure 8 is nice, but it’d be helpful to see the isolated labyrinth in lateral and dorsal view.

I don’t mean to be overly picky on the figures but this work is really nicely done and important, and it would be great if the figures matched the manuscript in quality.
Experimental design: Experimental design is fine
Validity of the findings: Validity of findings is fine although I make some points in General Comments.
Additional comments: p. 10, line 107: "opening foramen of the pneumatic sinus" Or is this the Eustachian (pharyngotympanic) tube opening?

p. 11, line 131: "median pharyngeal recess" This doesn't seem like much of a recess. It's just the normal concavity. It true that it’s rather arbitrary to decide whether a normal fossa is deep enough to be called a “recess.”

p. 12, lines 153-155: "This third crest runs from a point anterior to the ventral bending of the crista prootica sharply anterodorsally to the anterior margin of the prootic. It terminates dorsal to the foramen of CN V. The lateral surface of the prootic dorsal to this third crest is smoothly depressed." This crest and the fossa behind it are widely distributed (Desmatosuchus, Allosaurus, others), where it's likely the attachment for musculature.

p. 12, lines 161-165: "The foramen of CN VII is damaged on the left side. On the right, it is positioned posterior to the crista prootica, so that it is visible in lateral view of the braincase. A shallow sulcus runs postero-dorsally from the foramen of CN VII along the ventral surface of the crista prootica and represents the hyomandibular branch of the facial nerve." I don't think that the facial nerve foramen is correctly identified. I think it's more dorsal, tucked under the crista prootica rather than being the large opening labeled in the figures. The more dorsal opening is visible in the CT data on both sides. Moreover this is precisely where the facial nerve foramen is located in a diversity of archosaurs. The hyomandibular and palatine branches of the palatine nerves travel just under (ventral to) the crista prootica. I'm not sure that the feature identified as the facial nerve foramen is truly an aperture, but may just be very thin bone. It also would be a giant aperture for such a small nerve.

p. 12, lines 170-172: "Posterior to the ventral part of this projection, and dorsal to the foramen of CN VII, another small projection bearing a foramen can be seen. The foramen is identified here as the entrance of the posterior branch of the auditory nerve (CN VIII; Fig. 5D, E)." I'm not sure that there's really a "foramen" there as much as a large unossified space. I looked pretty hard at the CT data and I’m not convinced of a discrete foramen, which is consistent with poor ossification of the medial wall of the inner ear which is common in this part of the phylogenetic tree.

p. 13, line 183: "two small fossae on the opisthotic…" I only see the one on the left. There's nothing on the right that I'd call a fossa. On neither side is there anything that I'd regard as an opening for either vasculature or pneumaticity. They're labeled "pf" in Figure 3, but that seems without adequate basis. I also see no basis for regarding any apertures as "obliterated" because I see no evidence that there ever was an opening.

p. 15: Pneumatic sinuses: the ventral opening may indeed be the pharyngotympanic (Eustachian tube) opening. The space it leads into is completely confluent with the inner ear, which makes no sense for pneumaticity (which is middle ear). The challenge here is that the area may have been really poorly unossified. There's also the unossified gap between the basioccipital and (para)basisphenoid contributions to the basal tubera. That gap within the basal tubera (often a very roughened area) is extremely common among basal archosaurs (even some dinosaurs). The authors refer to this gap as a pneumatic sinus in Figure 9A, but I think it's just the gap between the bones. The fact that this gap is continuous with the sinus raises the possibility that some of the "sinus" could be simply unossified areas.

p. 16-17: "Two other systems of open braincase spaces". I agree that there are some rather compelling open spaces with smooth walls that look like pneumatic spaces. However, they indeed lack foramina opening into an air-filled space, and are continuous with clearly cancellous or trabeculated regions. They may simply be marrow spaces. Lots of extant lizards have similar large, smooth-walled diploic cavities. The case for pneumaticity is not strong but I understand the authors' willingness to consider the case. Their treatment of it is now sufficiently measured. Well done.

p. 19, lines 314-315: "The quadrate of Mesosuchus also lacks a notch, indicating a tympanic membrane was absent in this taxon." I'm not sure that I fully agree. There seems to be a pretty reasonable tympanic crest running the length of the quadrate laterally and even a gentle "conch" caudally. Even if more derived rhynchosaurs lack the tympanum, Mesosuchus is so basal that it may have retained a tympanum.

p. 20, lines 337-338: "the unossified gap represents the ventralmost portion of the lagenar recess (Sobral et al., 2016:28; figure 3D), but this is clearly not the case in Mesosuchus" I'm not so sure. The "pneumatic" space (which I previously mentioned is continuous with the inner ear) is precisely where the lagena or cochlear duct would have been located. In fact the ventral tip of that space is at the BO/BSPH junction, which is typically where the lagena is directed. Perhaps in Mesosuchus the structure is there but is walled off laterally. It is indeed different and a little weird.

p. 21, lines 359-362: "Although a direct link between fossa volume and ecology has not been found for either extant birds or mammals (Ferreira-Cardoso et al., 2017; Walsh et al., 2013), in the absence of better proxies, it continues to be used to infer agility and modes of locomotion in extinct taxa (Bronzatti et al., 2017). Therefore, it will also be used herein." I'll quote from my previous review: "At a fundamental mechanistic level, the SCC and cerebellar flocculus are associated with sensing head and body movements and coordinating eye movements. Any connection to activity and posture must flow from the neurology, which is indirect at best in this case." I can also add now that any connection to ecology is also indirect at best. The authors cite Witmer et al. (2003 and 2008) as stating that scientists have related these systems to ecology and locomotion, but our emphasis as always been on their specific role in gaze stabilization mechanisms, which may relate to agility, locomotion, and ecology...but again only indirectly.

p. 21, lines 370-376: "The inner ear of Protoceratops shows an elongate common crus with relatively slender semicircular canals (Brown & Shclaikjer, 1940). The anterior and posterior canals are roughly the same length, while the lateral one is markedly shorter. The semicircular canals of Mesosuchus are as slender as those of Protoceratops, but the anterior canal is comparatively longer. The floccular lobe of Protoceratops is not developed, being absent from the endocast. Thus, if these structures reflect the mode of locomotion, Mesosuchus would have had a more erect posture and was probably more agile than Protoceratops." I'll again reiterate my criticism from my first review: "Comparison to Protoceratops—and certainly the inner ear of Protoceratops—are of doubtful utility given the vast difference in phylogenetic history." The authors' justification for maintaining this passage is not compelling. Moreover, the assumption that "these structures reflect the mode of locomotion," has not been substantiated. Again, they relate neurologically to coordinating eye movements.


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: FUNPRED 3.0: IMPROVED PROTEIN FUNCTION PREDICTION USING PROTEIN INTERACTION NETWORK
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript introduces a new version, 3.0, of an existing program, FunPred (by the same authors) for protein function prediction.
Experimental design: The methods are very poorly described. I'll give some examples:

L92-93: "While in another, FunPred 2 (Saha et al. 2017a), fifty percent of
93 proteins are selected as test proteins from each formed cluster."
What cluster is this referring to? No cluster has been mentioned before.

L97: "strongly connected essential proteins"
"Strongly connected" usually refers to graphs. What is a strongly connected protein?

L105-106: "Application of three levels of threshold for the formation of clusters and selecting all proteins from the clusters as test set to overcome the limitations of its predecessors."
This is the first difference between FunPred 3.0 and FunPred 2.0. The choice of the test set is an evaluation difference, not a design difference.

Fig.1: "M clusters are formed, the proteins of which are selected as test proteins"
This seems to imply that ALL proteins in the clusters are chose as test proteins, which does not make sense.

Fig.3: the diagram is highly redundant, without clarifying what the program does.

I cannot say I understand what the new algorithm does.
Validity of the findings: The results are not impressive at all.
First, Table 2 shows almost no difference between the precision and recall obtained for the three different thresholds.
Second, and most important, Table 3 shows negligible F-score improvement w.r.t. two existing programs.
Additional comments: The new algorithm has to be clearly described. Also, since there is negligible improvement of the state of the art, the introduction of a new algorithm has to be justified.


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: FUNPRED 3.0: IMPROVED PROTEIN FUNCTION PREDICTION USING PROTEIN INTERACTION NETWORK
Review round: 1
Reviewer: 2

Output:
Basic reporting: The introduction has a good discussion of the context of the problem and similar work that this manuscript builds on.  The language needs minor editing for grammar at a few places.

The methods, however, are not described in insufficient detail for certain points of the analysis. For example:
1.	The definitions of the node and edge weights are described in the cited paper and the supplementary methods but the main text doesn’t say what these weights are or where to find these.
2.	Line 125 says “… creating M mutually exclusive protein clusters…”, but the value of M (number of clusters) is never mentioned. In addition, in the algorithm in Figure 1, it is not clear whether the algorithm proceeds until all the proteins have been clustered, and the number of clusters simply depend on the chosen thresholds, or whether M can be controlled.
3.	The selection of the test set proteins is also not clear. Line 105 says “ … and selecting all  proteins from the clusters as test set …”, which either implies that all the proteins are part of clusters and are part of the test set, or only those proteins that are part of the clusters can be part of the test set. Figure 6 implies a conventional selection of a small set of the proteins as the test set. All of these statements and the Figure are not consistent which each other.
4.	It is not clear what is meant by “ … prediction of unknown/missing protein pair functions in MIPS dataset …”. Does it mean prediction of missing protein pair interactions? If it is prediction of protein function, why are these pairs of proteins supposed to have the same function. Conventionally, the functions of single proteins are predicted. What if a protein is part of multiple pairs and each has a different function?
5.	Table 4 doesn’t clear the confusion. Pairs of proteins are predicted, but some of the predictions are functions or biological processes the proteins might be involved in, such as cell polarity, vesicular transport, DNA repair etc., while others such as two hybrid and synthetic lethality are interactions. Prediction of protein function and the prediction of protein interactions are very different problems and should be conceptually separated, even if the underlying algorithm is similar for this method. Table 5 again mixes these two modalities.
6.	The protein functions of the annotated proteins, and consequently, the predicted functions should be clearly defined prominently where the interaction dataset is defined. Is this the Gene Ontology BP or MF set? Are these functions for which the best features are found, as described in lines 148-159?
Experimental design: The basic idea of clustering the proteins into clusters, and then predicting protein functions using the cluster that is “closest” to a protein in terms of some network distance and/or physiochemical properties is valid. However, it is hard to evaluate the method in detail when the method Is inadequately described (as mentioned in the Basic Reporting review section). At the very least, the following points should be cleared:
1.	The selection of the number of protein clusters.
2.	The separation of protein function prediction and protein interaction prediction.
3.	If protein function is done for pairs of proteins, this is unconventional, and it needs an explanation for its logic and a discussion of why this is a good idea.

At this stage, the only way to get answers is to dig deep into the provided code. But the manuscript should provide at least the conceptual framework.
Validity of the findings: It is hard to evaluate the validity of the findings while questions remain about the experimental design. As mentioned earlier Tables 4 and 5 mix two different modalities of prediction.
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: FUNPRED 3.0: IMPROVED PROTEIN FUNCTION PREDICTION USING PROTEIN INTERACTION NETWORK
Review round: 2
Reviewer: 1

Output:
Basic reporting: N/A (revised version)
Experimental design: N/A (revised version)
Validity of the findings: N/A (revised version)
Additional comments: I appreciate the authors' efforts to improve the quality of the presentation. However, the authors agree with me on the most important aspect: the new program presents negligible improvement over the previous version:

"Since FunPred 2 is modified to FunPred 3.0 and the basic working mechanism of the both remains same, negligible improvement in the F-Score has been observed in Table 3 though major improvement has been observed when compared to the basic version FunPred 1."

Since FunPred2 has been already published in all details, FunPred3 is in fact an incremental improvement, more appropriate to be implemented only in the github webpage of the software.


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: FUNPRED 3.0: IMPROVED PROTEIN FUNCTION PREDICTION USING PROTEIN INTERACTION NETWORK
Review round: 2
Reviewer: 2

Output:
Basic reporting: The updated manuscript has added important information to attempt to answer some of the questions raised in the previous review. However, there are still many questions regarding the methods, and describing the methods in sufficient detail is essential for a potential reader to gain useful knowledge from the article.
In the following, I will touch on some of these points.
Major points:
1.	Line 76 states that a certain number of interactions are either unknown or missing. What does this mean? If a PPI interaction is not listed in MIPS, how does one conclude whether a) this pair of proteins do not interact, or b) this is a missing interaction? What are unknown interactions? Bioinformatics databases list the experimental modality and source for each interaction. So what are these unknown interactions? Does this have something to do with unknown functions of proteins? What is the criteria for calling a pair of proteins to have unknown function? When one of the proteins has unknown function or both of them?
2.	It is not explicitly mentioned how the True Positives, False Positives etc. are calculated in line 267. Are these for the presence/absence of a protein-protein interaction or for the functional classification of proteins? If it is for the protein function (as can be assumed the title and text), what/how many are these functional categories considered? The article mentions both Gene Ontology and MIPS Functional Catalogue. Which of these is used? Both GO and the MIPS functional catalogue are hierarchical. How is the function prediction of a wider/narrower category handled? For example, a protein if a protein has been annotated to MIPS function 11.06.03.01 (mRNA editing)is it counted as a true positive if the algorithm predicts its annotation to be 11 (transcription)? Or are these categories taken at a particular level, such as the GO slim categories?
3.	The language/sentence structure should also be improved, but this can be done by a proof-reader or language editor.

Minor points:
1.	Please consider using the more familiar terminology of a test set/test instance, cross-validation  set or a hold out set rather than a target protein.
Experimental design: Broadly, the methodology seems within reason, but the experimental design can only be evaluated completely after the methods have been unambiguously described.
Validity of the findings: Dependent on questions raised earlier.
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: FUNPRED 3.0: IMPROVED PROTEIN FUNCTION PREDICTION USING PROTEIN INTERACTION NETWORK
Review round: 3
Reviewer: 1

Output:
Basic reporting: I thank the authors for their detailed answers to the questions raised in the previous review. Since the mixing of the experimental modality and function, and prediction of protein functions of pairs of proteins rather than individual proteins is unusual, it will be helpful if the explanation written for the review is made available to the readers, perhaps as a supplementary methods file. At this point, I feel that the method has been adequately described that a discerning reader will be able to understand the results.

I just have a few minor suggestions for the authors.

Line 330 should read “Last but not least”, rather than “Last but not the least”. While discussing the other methods in lines 334 to 351, it’s better to include the citation for each method, even though they’ve been included earlier in lines 313 to 319.

Are the performance measures of the other methods listed in Table 4 taken from the different papers, or are they computed by the authors on the same test set chosen for this work? Please describe this somewhere. If they were computed on the same dataset, it would be nice to include the code for this in the repository. The captions for Tables 5 and 6 can be edited to clearly mention where the interacting pairs are being predicted, and where the function is being predicted while the pair is already listed in MIPS.
Experimental design: no comment
Validity of the findings: I am not sure whether this algorithm as reported will be used for practical function/pair prediction, but the authors have reported a valid method and described it for other researchers. Some of the ideas presented here may be used by other researchers in future work.
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: FUNPRED 3.0: IMPROVED PROTEIN FUNCTION PREDICTION USING PROTEIN INTERACTION NETWORK
Review round: 4
Reviewer: 1

Output:
Basic reporting: I think the language/readability of the text is barely satisfactory, but detailed language editing is outside the scope of this peer review.
Experimental design: no comment
Validity of the findings: The results in Table 4 are copied from the different publications, and this should also be indicated in the table caption. As such, the different studies probably use different test and training set splits than the authors. Therefore, a direct comparison will not necessarily support the superiority of this method. The corresponding statement in the first sentence of the discussion section should be removed/modified.

The columns 5 and 6 in Table 2 should probably not be called Prediction Accuracy. Accuracy is usually understood as a fraction or percentage of the correct predictions.

Tables 5 and 6 caption should also mention whether these are all the unknown/missing interactions, a random sampling, or selected based on some scoring.
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: CHEMODIVERSITY OF CALOPHYLLUM INOPHYLLUM L. OIL BIOACTIVE COMPONENTS RELATED TO THEIR SPECIFIC GEOGRAPHICAL DISTRIBUTION IN THE SOUTH PACIFIC REGION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article should include sufficient introduction and background of accD and PsaA-Ycf3 to know the work better. Your introduction needs more detail I suggest that you improve the description at lines 40- 51 to provide more justification for your study.
Experimental design: Methods should be described with sufficient information to be reproducible by another investigator.
-	Line 69-70: Why do you use EtOAc (not Hexane) in microscale extraction process?
-	Line 84-96: Standard’s purification was not clear.
This fraction ……………. Yielding 12 fractions. Why were only fraction 7,9 and 11 submitted to repeated preparative HPLC?
Validity of the findings: Overall, this main idea of this study is not a high novelty, because previous study has investigated the genetic variations, likes the authors said in the introduction. The novelty of this study was the use of different marker.
Additional comments: This study aims to utilize barcoding universal gene markers in accD and PsaA-Ycf3 as tools to study the genetic variations occurring intra-geographically and inter-geographically from three South Pacific countries (French Polynesia, New-Caledonia and Fiji). Authors used tamanu oil for identifying new compounds and tamanu leaves for DNA analysis. This study can be published with revision and clarification of the issues.


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: CHEMODIVERSITY OF CALOPHYLLUM INOPHYLLUM L. OIL BIOACTIVE COMPONENTS RELATED TO THEIR SPECIFIC GEOGRAPHICAL DISTRIBUTION IN THE SOUTH PACIFIC REGION
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript is scientifically sound and it is written in clear sequences. It is supplied with appropriate and sufficient data.
The author is advised to justify/rectify a minor comments.

The author should emphasise that from which ground/data they can elucidate the isomer of Tamanolide E1 and E2.
Line 117, what type of gel? (SDS page/agarose?)
Line 283, it should be Fig 4.
Line 199, use ring instead of  cycle.
To differentiate the structure of Tamanolide E1 and E2 in Fig 3.
Caption in Table 3, please use symbol instead of parenthesis.


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: CHEMODIVERSITY OF CALOPHYLLUM INOPHYLLUM L. OIL BIOACTIVE COMPONENTS RELATED TO THEIR SPECIFIC GEOGRAPHICAL DISTRIBUTION IN THE SOUTH PACIFIC REGION
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment
(Detail report is in the attached file)
Experimental design: No comment
(Detail report is in the attached file)
Validity of the findings: No comment
(Detail report is in the attached file)
Additional comments: Overall, the manuscript is generally well-written. The backgroud of the study was clear and the experiments were well-design with satisfied parameters.
There are corrections that can be seen in attached file.
Since authors proposed new compounds, authors should provide the NMR, IR and MS data of those new compounds in 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: CHEMODIVERSITY OF CALOPHYLLUM INOPHYLLUM L. OIL BIOACTIVE COMPONENTS RELATED TO THEIR SPECIFIC GEOGRAPHICAL DISTRIBUTION IN THE SOUTH PACIFIC REGION
Review round: 2
Reviewer: 1

Output:
Basic reporting: It is Clear and sufficient field background.
Experimental design: Please put material information, such the solvent, the reagent, etc.
Validity of the findings: Conclusions are well stated.
Additional comments: This study can be published with minor revisions


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: CHEMODIVERSITY OF CALOPHYLLUM INOPHYLLUM L. OIL BIOACTIVE COMPONENTS RELATED TO THEIR SPECIFIC GEOGRAPHICAL DISTRIBUTION IN THE SOUTH PACIFIC REGION
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: Line 154: Samples were immersed in EtOAc and sonicated for 5 mins before this was
155 partitioned with EtOH at a 1:1 ratio v/v....

The sentence is not clear. Which one is the first?
Partitioning between which solvent?....EtOAc and EtOH are miscible. The authors need to clarify this method.
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: CHEMODIVERSITY OF CALOPHYLLUM INOPHYLLUM L. OIL BIOACTIVE COMPONENTS RELATED TO THEIR SPECIFIC GEOGRAPHICAL DISTRIBUTION IN THE SOUTH PACIFIC REGION
Review round: 2
Reviewer: 3

Output:
Basic reporting: This the second review. The improvement made by the authors are adequate and satisfactory. I have no further comment on this manuscript.
Experimental design: This the second review. The improvement made by the authors are adequate and satisfactory. I have no further comment on this section.
Validity of the findings: This the second review. The improvement made by the authors are adequate and satisfactory. I have no further comment.
Additional comments: No additional comments


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

Input:
Title: AROMATISATION OF STEROIDS IN THE BIVALVE MYTILUS TROSSULUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper by Hallmann et al. is well written and they reported a potential steroidogenesis, particularly aromatization of androgens for estrogen synthesis, in Mytilus trossulus based on the precise experiment using radio-labelled steroids. The authors suggested the occurrence of aromatase activity influenced with temperature, pH, gender, maturity in this species, and the specific conversion of androgen to estrogen.
Experimental design: The experiments were well designed and the results from these experiments provided an accurate and convincing data.
Validity of the findings: The findings are significantly valuable to discuss about endogenous estrogen synthesis in bivalve mollusks because invertebrate steroidogenesis is still highly controversial.
Additional comments: L553-555: The authors argued that bivalves are able to synthesize vertebrate estrogens. This argument is uncertain and supposed to mislead readers to synthesis of estrogens, which is completely identical to vertebrate estrogens, in bivalves. The inhibitory effects of inhibitors to aromatase on aromatization reaction in microsomes of gonad were not observed as the authors expected and vertebrate type estradiol-17ß have been reported to bind to invertebrate estrogen receptors with low affinity, which is discussed in binding sites of ER to E2 in detail by Thornton group. These facts disagree with endogenous synthesis of vertebrate type estrogens in bivalves although the possibility of synthesis of estrogen-like compounds cannot be ruled out in bivalves. Recently Thitiphuree et al. (J Steroid Biochem Mol Biol, 186, 22-33, 2019) proposed potential steroidogenic pathway including aromatization.


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: AROMATISATION OF STEROIDS IN THE BIVALVE MYTILUS TROSSULUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript reports results from in vitro measurements of mussel activity using radiolabelled steroids. It aims at demonstrating the activity of aromatisation in the mussel Mytilus trossulus by measuring the release of radiolabelled 3H2O from 1β-3H androstenedione and by the identification of estradiol or estrone in mussel tissues resulting from the metabolisation of aromatisable substrates.
This is a very interesting subject worth investigating.
The manuscript is well presented and written and conforms to essential requirements.
However, there are some methodological weaknesses and the existence of interpretations that are not fully supported by the facts. The manuscript must therefore be corrected before publication.
Experimental design: The M&M part need more precise description. Please provide explanations to the following questions.
l. 199-200: How many mitochondria and microsomes fractions were prepared per sampling time (i.e. how many 25mL of tissues were extracted) ?
l.207 and l. 222: It is mentioned that these fractions were fractionated into 1mg portions. 1 mg of what? How was it measured?
l. 180. According to M&M “In vitro analyses were performed on organisms collected in the period from 2012 to 2018.” However, Fig 3 show that there were large variations of activities between sampling times (seasonal effects). How did you ensure that the microsomal and mitochondrial fractions used (each 1mg extracts) were comparable between assays?
Were the results from n=5 shown in fig 3 and 4 from different extractions (different fractions)?
Enzymatic activity: Please show the results of the controls (1) with denatured (heated) microsomal fraction and (2) no NADPH. This is very important as no inhibitors are identified.
Please show results with consistency using a single unit (pmol/h/mg protein) in all figures.
Fig 6: What were the sex of the sample used?
Fig 6: How many mussels from the two experiments (15 unsexed or 10 sexed mussels) were used in the showed results? How come that n=10? Are those results from only the second experiment? Please specify.
The symbols are misplaced in the figure 6. Please use the same form as the figures you published in 2018.
There is no indication of any difficulties to determine the sex of the sample mussels. However, some were sampled in November where usually no sex can be easily determined especially with the method used in this work. Please explain.
l.267: Steroids-13C3 identification: please provide detection/quantification limits.
Please explain the sentence (l.526-527): “Unfortunately, due to the methodological restrictions simultaneous detection of androgens and estrogens after exposure to labelled substrates was not possible.”
Validity of the findings: A number of questions and remarks may arise considering the discussion and conclusion.
As noted by the authors (l.105-108), “non-specific cross-reactivity cannot be excluded since the reaction can be catalysed by aromatase as well as by any random enzyme belonging to the group of the cytochrome P450 family that contributes to oxygenations and loss of the methyl group at C-19 position.” This means that it is unsure that any aromatisation of steroids occurred. It would have been necessary to identified the products. Thus what the authors called aromatase activity should be designated with more caution.
Validity of the findings are subjected to methodological weakness as specified above. Full description of the methods is required in order to better judge the strength of the results.
l.413-430. Temperature effect: According to your previous published paper (2018, table 1), the temperature of your samples was close to optimal in February 2013 at your sampling location (7,8°C) and too high during the other months (14,5-17,5°C). Please discuss the implication of these findings considering that you reported low levels of steroids (and especially E2) in February 2013 (winter time) and high in May 2012 (fig 3 and previous paper). Your discussion is not in accordance with this optimum in winter.
l.455-478: Deduction from lack of inhibition: This (very) long paragraph discuss the fact that there were no inhibitory actions of several of known vertebrate aromatase inhibitors on the measurements of the potential mussel aromatase activity (release of radioactive water) in the present study. From the absence of the vertebrate aromatase in the mussel extract, the authors conclude that (what may or not be) the mussel aromatase is different. It is very surprising to conclude in the existence of a particular protein by demonstrating the absence of another! (It is also a bit strange to write in a scientific journal that “we believe” as a concluding remark. The evidence is missing).
l.518-552: Are the mussel able to aromatise steroids in vivo? This paragraphs discuss the results from the exposure to A-13C3 and T-13C3. Please explain why the chromatograms could not allow the identification of the radiolabelled compounds simultaneously.
As noted (l.562-564), mussel can very rapidly metabolise steroids into esters. How come that none was observed here? Why did not you include any saponification step in your method?
Additional comments: The present description of the method in this study and the results does not allow to conclude on the existence of any aromatase in the mussel. Further information and description are needed.
The authors might provide satisfactory answers. If not, conclusions should be changed 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: AROMATISATION OF STEROIDS IN THE BIVALVE MYTILUS TROSSULUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors considerably addressed the issues on synthesis of vertebrate type estrogen in bivalve species in Discussion.
Experimental design: Basic information on the specimen and sample preparation was added.
Validity of the findings: The authors revised their argument on endogenous vertebrate type-estrogen synthesis according to the review comments, which can be understood.
Additional comments: The author's response to the review comments and revision satisfied me. I would recommend the manuscript to be published.


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

Input:
Title: AROMATISATION OF STEROIDS IN THE BIVALVE MYTILUS TROSSULUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The answers provided are generally satisfactory (although some seem to leave some uncertainties). The article seems to me to be publishable as it stands.
Experimental design: the complementary data provided after the corrections are satisfactory.
Validity of the findings: The authors' interpretation is valid.
Additional comments: Thank you for your efforts to answer all the questions. And congratulations on your work.


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

Input:
Title: THE USE OF BAT HOUSES AS DAY ROOSTS IN MACADAMIA ORCHARDS, SOUTH AFRICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an important study testing the factors that influence bat houses occupancy in macadamia orchards. No comments regarding the English level used. Some of the literature used was quite repetitive and some times (Rügger et al. 2016), the reference list was longer than the sentence that was referring to (line 58-59).
Some of the figures and tables need to be appropriately described such as which are the dimensions (mm or cm) of the artificial roost.
Regarding to the raw data shared, I wasn’t able to opened, it was illegible.
Experimental design: Even thought that they have not used a large number bat boxes, they obtained good results in terms of what type of bat boxes do they prefer most.
Seems quite confusing for me when and how the bat boxes were erected, I will suggest a chronological explanation that may also be accompanied with a figure showing the location of each type in each orchard.
Another methodological concern is the small sample size monitored with the Ibuttons not knowing the temperature of the rest of the bat boxes. Addressing this potential criticism in the discussion would be advisable.
Validity of the findings: Statistical analysis should be improved explaining the packages they used in R and specifying the summary statistics used.
Also adding the ANOVA obtained to the supplementary material will be helpful.
Seems quite confusing the way to show the results regarding the statistical models used, better to show them all in supplementary materials and just comment the selected one
However, the conclusions are well stated and linked to the hypothesis.
Additional comments: No additional comments


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

Input:
Title: THE USE OF BAT HOUSES AS DAY ROOSTS IN MACADAMIA ORCHARDS, SOUTH AFRICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comments; see general comments.
Experimental design: No comments; see general comments.
Validity of the findings: No comments; see general comments.
Additional comments: The study entitle “The use of bathouses as day roosts in macadamia orchards, South Africa” investigates factors associated with the structure and environment of bat houses influence bat occupancy in a region where little is known about important roost characteristics. I believe this study is an excellent contribution to the field of using artificial structures for conservation in agricultural areas, especially for species that provide vital ecosystem services through crop pest control. Overall, I found the manuscript to be well written and the study methods and analyses to be robust. I only have minor comments on the content in the manuscript as outlined below:
1.	Figure 1: Could you add a zoomed in aerial image of the study location showing: 1) where the orchards were located within regard to one another, and 2) where the bat houses where located within those orchard sites? This would allow the reader to better understand the distribution of the bat houses in each of the orchards (since different numbers of the types of bat houses are placed in each orchard site) and get a better sense of proximity to water and other landscape features.
2.	Lines 135-137: I’m a little confused which three bat houses in each of the orchard sites received an IButton unit. Is it the three multiple chamber houses but not the black/white ones, the rocket ones or the colony one? Please clarify. (Note: once I read the results it did become clear that it was the 3-set of bat houses, but perhaps you could clarify in the methods still)
3.	I agree with the idea that type of bat house may be confounded with temperature and insulation of the central bat house, since that was the warmest bat house (most likely due to its location in the set up and had more chambers). What this made me realize though was I didn’t see (or may have missed) what the type of bat house was for the black/white pairing. Can you add this information somewhere or make it more apparent, if I missed it? If the black/white bat houses were the six chamber house, then perhaps temperature is the most important, but of course factors affecting temperature are also the number of chambers which help insulate it.
4.	Why do you report 166 individuals in the results and 220 individuals in the discussion? Please address this discrepancy.
5.	Minor: should it be bathouse or bat house? It’s called the North American Bat House Program, so perhaps separating the words is most appropriate?


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

Input:
Title: THE USE OF BAT HOUSES AS DAY ROOSTS IN MACADAMIA ORCHARDS, SOUTH AFRICA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript was generally well written but it could be more concise and checked for the occasional incorrect use of tense. While a minor matter of personal preference, and not necessary to change, my preference is to reference literature without the extra words (e.g., “According to…”, “The review of…”) as this is implied. Instead I acknowledge the published literature with appropriate citations but very rarely noting the authors in anything other than parentheses. For instance Lines 66-68 could be reduced to “Peer-reviewed studies focusing on artificial roost site use by African bat species are literally non-existent (Rugger et al. 2016).” In fact, the three sentences that speak to the review of Rugger et al. could be combined into 1-2 sentences.

Lines 60-65 - the link in the first paragraph of global bat decline to bats being useful for pest control to the lack of knowledge of bat roost preferences and artificial roosts is not clear. While implicitly understood, perhaps this could be made more explicit?

While it is understandable that there is limited published literature on bat house use by bats, I think the authors rely too much on dated grey literature when there might be published alternatives, even if dated.  For example, there is reference to Kiser & Kiser (2004) to substantiate comments on roost fidelity and parasite loading when instead “Lewis, S.E., 1995. Roost Fidelity of Bats: A Review. J. Mammal. 76, 481–496.” could be used. If this study was indeed meant to be an extension, build upon, or be a confirmation of the Bat Conservation International newsletter findings, perhaps it could have been framed that way?
Experimental design: While the overall concept of the research is important and could help inform bat conservation - determining the key features of artificial roosts used by bats - I am not convinced that this study/analysis was sufficient to disentangle key features from potentially confounding factors.

While not incorrect to use the term “occupancy”, this term is fairly unambiguously used to describe occupancy modeling (e.g., MacKenzie et al. 2005). Perhaps “bat use” instead?
The authors acknowledge that bats have occupied the boxes on days when no bats were physically present. Was the fact that bats had been present between monthly visits noted and included in the analysis? If bat use was recorded monthly, wouldn’t the present of faeces be an indication of presence during the month and be worthy of inclusion into the analysis? Perhaps as an overall measure of “bat” use - i.e., aggregate all sightings and indications of use as “use” for the month and re-run the analysis, particularly as there aren’t any fine-scale temporal covariates?

I think the statistical methods could be written more clearly. Could the full model be written out for clarification? I’m assuming the full model was something like: Bat presence ~ Bat House Type + Altitude + Distance to Water + Height of Bat House + (1|Farm) + (1|Month). Is this correct? I wonder if “Time Since Installed” should be a fixed factor as literature supports (and this manuscript acknowledges) that bat use of artificial roosts generally increases over time. The fact that 21 bat houses (in sets of 3) were installed years earlier than the other bat houses and the remaining houses were all installed in May or March 2016 makes me wonder if the reason that the colony house had no bats was a confound of only having 1 replicate of that type and it being installed in March 2016.

I’m not quite sure why the data for Bat House Type “Colony” was removed - if the model is set up as I wrote it then there is no reason for data to be removed. I’m also not clear on why Farm and Month are used as random factors. The authors acknowledge that there might be some sort of temporal trend but then use Month as a random factor. Why not convert month into a continuous variable (such as a sine/cosine function) and keep it in the model as a fixed factor to test if there is a temporal trend? I’m also a little concerned with the use of the “dredge” MuMIn function and the low sample sizes. Considering all of the tests that are run using dredge, might the few statistically significant results be spurious (i.e., if you run 100 tests you should expect 5 of them to show significance from random chance)?

Table 1 is not very useful. It’s not clear from the methods/results how the models were run (see comments above) and thus it’s not clear if this is the best top model (as suggested by the AICc score, which is the same for all variables and thus redundant in this table) or if these were competing models, which is normally what would be presented with AICc scores. Could a table of all possible models be presented with AICc scores or delta AIC to give the reader an idea of how many models were run and how “good” the top model is in relation to all other models?
Did the authors run a null model and full model to compare against their top model? It would be useful to see the results, especially if the top model is significantly better than the null/full (i.e., comparing log-likelihoods using something like the anova() function in R). In addition, have the authors thought about calculating the evidence ratio to determine the strength of evidence for each variable? It might be valuable for the authors to review Burnham et al 2011 prior to a revision of the analyses. (http://www.ericlwalters.org/Burnham_etal_2011.pdf).

I’m not clear on the purpose of the iButtons recording temperature in only 3 (adjacent?) bat houses. What was the ambient temperature? Is mean temperature something that is truly important to bats? I would imagine it might be the maximum/minimum/difference from ambient that might be the most useful as houses that are too hot/cold might be detrimental to bat health. Can the authors provide a rationale for why they chose mean temperature and justification how this small replicate test can provide insight into bat house preferences? Also, I would revise line 190 as p=0.55 is not a “marginal significant difference”.

Is it possible to include a figure of the study area/sampling design? Perhaps the current study area figure (Fig 1) could be included as a small inset to orient the reader to the region with the main figure showing the placement of box types in relation to one another and to the other farms. This would help the reader understand how nested/confounded the experiment is. It would also be quite useful to have some sort of symbol for each of the different type of box and have the size of the symbol proportional to the number of bats detected in the box. I found it very confusing to try and remember the experimental set-up and number of occurrences in each bat box type from reading the manuscript in its current form.

What is the landscape surrounding the farms like? From Figure 2 it seems that it might be treed, although this could just be my ignorance of what macadamia orchards look like. If it is treed do you think this might influence bat use of artificial roosts? I.e., will you be less likely to have bats roosting in the bat houses if surrounded by natural roosts and, if yes, is the surrounding habitat consistent around all farms? This relates back to my comment above suggesting a figure to help the reader understand the layout of the sampling design and if there might be confounding factors.

While a nice picture, Fig 4 seems irrelevant to the study as there was no research relating bat house use to insect availability or insect observations/data of any kind.
Validity of the findings: Unfortunately, I did not find that the data was robust, statistically sound or adequately controlled. Nor did I think that the conclusions were limited to supporting results.

Much of the “suggested” in the discussion might be better framed as author speculation. While interesting thoughts, I might argue that the research does not actually suggest these findings but the authors are speculating based on the findings and/or observations as much of the discussion relates to the observed data rather than results from any statistical tests. For example, is the conclusion related to bat preferences of warmer houses accurate (lines 207-208)? From my reading of the methods I thought that temperature was only recorded in one set of 3 boxes, but not in the set of white/black boxes (lines 134-137). Please clarify the methods. Assuming there was only temperature recorded in the set of three bat boxes, how can there be the conclusion that bats preferred warmer temperatures? This is not substantiated by the findings of bats occurring more frequently in the central bat house and in the black bat houses as temperature was not measured in all the boxes nor related to bat house use in any statistical test.
Additional comments: Other comments: Is bathouse a word? I would write it out as two words or bat box, as is typically written.

Line 164 notes that there were 166 individual bats observed while line 203 notes 220 individual bats. Were 166 or 220 bats observed?


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

Input:
Title: THE USE OF BAT HOUSES AS DAY ROOSTS IN MACADAMIA ORCHARDS, SOUTH AFRICA
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In general, the revision to the manuscript helped address many of my previous comments on the manuscript. The new figure 1 greatly helped me understand the set-up of the study. Overall, I think this study provides insights into management/conservation methods using artificial roost structures, and is an important contribution to that field. My only issues with the current version of the manuscript is with the writing style and some-what sloppy formatting. Below I’ve listed examples and places for improvement.
1)	Abstract: Lines 51-53 read a bit awkwardly to me. Its important that this sentence is edited as this is a main take-home result. Do you mean “of the different bats houses tested in the study, the houses that had characteristics that made them the warmest and best insulated—which were erected in sets—attracted the most bats”? Do you need to mention that they are freestanding on poles? Because they were all freestanding.
2)	In a number of areas, there are one-sentenced paragraphs (Lines 75-77, 99-100, 189-192, 238-241). In most of these cases, I do not see justification to keep them as a single sentence. I recommend incorporating those single-sentence paragraphs into another paragraph to make your points clear. Also, I wasn’t sure if the authors meant to have these sentences be a stand-alone paragraph as the formatting was not consistent throughout the article, with a space inconsistently occurring between paragraphs.
3)	Lines 84-85: I suggest changing “Generally, the microclimate of bat houses, respectively insulation, sun exposure and color seems to be an important factor influencing bat house occupancy” to “Generally, the microclimate of bat houses (e.g., insulation, sun exposure and color) seems to be an important factor influencing bat house occupancy.” Because respectively is miss-used in this sentence and the original sentence is complex and difficult to read.
4)	Figure 1 is very helpful in understanding the study set up. But, I would like to see the quality of that figure improved in terms of how its formatted, especially with regard to the aerial image used in part (a) and the map used in part (c). In the map in part (c), it is difficult to notice the tiny circle (almost looks like a lake on the map) and seems odd that its not inset within the part (a) image.
5)	In a number of places, “respectively” should be changed to “respective to” (e.g., line 122, 250, 313).
6)	There are still a couple of places with “bathouse”, not “bat house”. I always read it as “bath house” (e.g., Line 155, 188).
7)	The first paragraph in general repeats what is stated in the results and then what is later stated in the discussion. I would remove it since it doesn’t get to the interpretation of the results until paragraphs 2 and 3.
8)	Line 276: affect, not effect