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: USING UNDERWATER VIDEO TO EVALUATE THE PERFORMANCE OF THE FUKUI TRAP AS A MITIGATION TOOL FOR THE INVASIVE EUROPEAN GREEN CRAB (CARCINUS MAENAS) IN NEWFOUNDLAND, CANADA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Writing is generally clear and easy to follow, but some sentences should be more concise to improve flow (specific changes annotated in PDF). The discussion could be shortened by removing some redundant sentences. Some important references are missing (annotated in PDF).
Experimental design: This study addresses an important gap in our understanding of the efficacy of a widely-used tool.
The authors do a good job of clearly specifying their objectives, which are to 1. Evaluate performance and efficiency in terms of catchability (CPUE of Fukui traps) and 2. Understand patterns in catchability between different sites. To this end, they are only evaluating steps 3-6 of catching a crab in a Fukui trap: the approach, locating the entrance/attempting entry, and entering the trap. Importantly, they are not evaluating catch relative to abundance of crabs around the trap, nor are they considering the retention of target catch until the gear is hauled.
There is some confusion about the Methods: which videos were included in the analysis. The authors use an “elimination threshold” of a mean of 10 green crabs caught per deployment (Line 170) because “effective trapping requires that green crab be present in sufficient numbers within the area being fished” (line 359). But, in section 2.4.1 the authors say that videos were eliminated based on no or low “activity,” determined by counting the approximate number of green crab present in the FOV (Line 186). Please clarify whether videos were eliminated based on low catch or on low abundance around the trap, so that the text matches with SI Table 2.
Validity of the findings: The dataset is small in terms of number of videos (8 out of 37 deployments used in analysis) but the study is focused only on the approach, attempted entry, and entrance into the trap. To that end, there were 2,373 approaches, which is a sufficiently large dataset to make conclusions about the performance of the Fukui trap.
Conclusions are well-stated, and speculation regarding the causes of the results are clearly stated as such. However, the potential importance of additional factors should be mentioned (e.g. sex and year, annotated in PDF) as well as the day-night effect, which is interesting and not given enough attention in the discussion. Be careful to specify where you are referring to the effect of the camera on the trap, versus environmental factors or the trap itself (annotated in PDF).
Additional comments: This is a good study that is beneficial to the literature and applicable to management of invasive green crab. The manuscript structure is easy to follow (the 6 steps are clearly described).
I have made the following suggestions to improve the validity of the findings and the readability of the manuscript: (also annotated in yellow comment boxes on PDF)
1.	Line 117:  Add more recent reference. Have any studies specifically been done on C. maenas and lights? See annotation
2.	Line 122: Citing Kahle & Wickham 2013 doesn’t make sense unless you add that you made figures with ggplot2
3.	Line 127: Should mention habitat type as this could have an effect on crab abundance, behavior, and therefore catchability (e.g. Bellchambers 2013, “Assessing the effectiveness of two methods of habitat characterisation for understanding species habitat relationships, using the western rock lobster (Panulirus cygnus George)”)
4.	Line 130: reword suggested
5.	Line 132: scientific name of herring first time you mention it
6.	Line 170: Did you test the effects of day/night?
7.	Line 189: Explain that this is the “elimination threshold.” See general comments about the confusion with the video selection criteria/elimination threshold
8.	Line 238: state potential relevance of genetic differences for catchability
9.	Line 272: Which sample subset are you referring to? Only used 8 videos in analysis?
10.	Line 306: Present in order (most common – least common, or visa versa)
11.	Line 318: Include model results (p values for study site effect)
12.	Line 326: How is saturation defined in the literature?
13.	Line 378: Inconsistent with your later speculation about trap construction.
14.	Line 386: Clarify – all bycatch present in the trap upon retrieval were released alive
15.	Line 390 – rephrase, “within seconds” is misleading
16.	Line 451 and 454: Rephrase these sentences: “often” and “not uncommon” are misleading as this was the “least common reason for failure”
17.	Line 463: suggested changing word order
18.	Line 478: The disconnect is not necessarily between abundance and final catch, it’s between attraction to the trap and final catch.
19.	Line 479: Suggested reword
20.	Line 494: Also individual traps as a factor in future studies
21.	Line 497: Should mention other studies with this same finding: Watson & Jury 2013 (“The relationship between American lobster catch, entry rate into traps and density”), Sturdivant & Clark 2011 (“An evaluation of the effects of blue crab (Callinectes sapidus) behavior on the efficacy of crab pots as a tool for estimating population abundance”)
22.	Lines 515 and 518 belong in the introduction
23.	Lines 526 – 535: most of this should be moved to the introduction
24.	Line 545: What is CHM?
25.	Line 585: Specify of C. maenas (see comment)
26.	Line 586: Should also consider the effect of year (Tremblay et al. 2006) and sex – mention other relevant studies
27.	Line 590: consider the peer-reviewed literature regarding the efficacy of sampling techniques (e.g. Stobart et al. 2015, "Performance of Baited Underwater Video: Does It Underestimate Abundance at High Population Densities?", Roberson et al. 2017, "Potential application of baited remote underwater video to survey abundance of west coast rock lobster Jasus lalandii").
28.	Line 604: This sentence is redundant, consider removing
29.	 Line 609: Should also consider testing lights to improve CPUE (See comment for line 117 – Nguyen 2017).
30.	Line 610: redundant sentence, consider removing.
31.	Line 615: Should mention future studies on tradeoffs in trap design, also potential effects on bycatch rates
32.	Figure 11: Hard to read, change red color scale


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 OLD AND THE NEW PLANKTON: ECOLOGICAL REPLACEMENT OF ASSOCIATIONS OF MOLLUSC PLANKTON AND GIANT FILTER FEEDERS AFTER THE CRETACEOUS?
Review round: 1
Reviewer: 1

Output:
Basic reporting: Literature references incomplete, important and relevant references missing (see pt. 3 and 4)
Experimental design: The manuscript is mainly speculation with relatively little new information, of which I cannot fully judge the importance (pt. 3 and 4).
Validity of the findings: The authors present several conclusions:
1.	Ammonites changed ecological role during their life time, as indicated by their extreme increase in size during ontogeny. They do not seem to bring up evidence for this statement, but it seems to be quite obvious – few organisms could eat an ammonite with diameter >1 m, many could eat ammonitella of about 1 mm.
2.	Large female ammonites produced very numerous offspring (r-selected), so juvenile ammonites likely were an important food source for planktivores.
3.	After the end Cretaceous extinction, juvenile ammonites were replaced by holoplanktonic gastropods, large pachycormid fish by filter-feeding chondrichthyans and cetaceans (sharks and whales).
The authors present newly generated information only as a part of to pt. 2, i.e., estimating fecundity of large ammonites. I know very little about ammonites, and leave the evaluation of this (important) part of the manuscript to other reviewers or the editor. I am able to evaluate pt. 3, and in my opinion the authors do not show convincing evidence that holoplanktonic gastropods diversified shortly after the end Cretaceous extinction, thus can be said to replace juvenile ammonites – there is considerable evidence that they radiated after the start of the Eocene, at least 10 million years later. The authors do not cite references showing the radiation in the Eocene. In my opinion the paper should thus be rejected, or (if the information on the ammonite fecundity is by itself sufficiently novel) be rewritten without linking extinction of ammonites at the end of the Cretaceous and expansion of Thecosomata more than 10 million years later.
Additional comments: Remarks by line number:

42-44: ‘..organisms…were erased by the consequences of an impact in Mexico and flood-basalt eruptions in India..’, followed by references. This sentence reads as if there is agreement in the community that the main cause of the extinctions were the combined effects of impact and volcanic eruption, but nothing is further from the real state of affairs: I would argue that the references show that hardly anyone would say this, but most people would argue that either the impact (Schulte et al) or the flood basalt eruptions (Keller et al) were the almost exclusive cause of the extinctions. Replacing ‘and’ by ‘or would improve the sentence..
47: only planktonic foraminifera, benthic foraminifera do not suffer significant extinction (Culver, Alegret et al.).
48: the bivalve statement is too simplistic; their pattern of extinction can in my opinion not be described as being ‘partial or total disappearance’ – see e.g. Vilhena et al 2013 Nature Sci Repts.
51-52: Did the Puzosiidae live during the late Maastrichtian, i.e. did they become extinct at the end of the Cretaceous? How common were they (and potentially other large ammonites) in the ecosystem? (something about how common they were appears in line 125, but ‘quite common’ is not very informative).
90: please define ‘derived ammonites; - are these heteromorphs? Were Puzosiidae derived?
113: how big is the lectotype of P. seppenradensis?
119: anything know about semelparous-iteroparous lifestyles of large ammonites? Is it probable that such large organisms are semelparous??
136: why discuss belemnites if they were already in decline (from about 35 million years before the K/Pg extinction)?? Do we know anything about coleoids replacing them?
153: do we know enough to make such a sweeping statement ‘these early psot-hatching developmental stages’ – all ammonites? Only derived ones?
154-155: refer to buoyancy – Shigeta 1993, Lethaia?
162: reasonable argument, but did not larger ammonites eat smaller ones as well? (I see- said in lines 169-170) – so how important were these large planktivorous fish? Common enough to have major impact?
167: I do not see that coeval extinction of two groups confirms that one ate the other- especially not if they both became extinct at the end of the Cretaceous (ammonites did)- see also below (189)
178-185: I do not really see why the discussion whether extinction of belemnites is linked to that of ichthyosaurs is relevant to the main story in this manuscript, and also do not quite see how extinction of that predator would lead to extinction of its prey only in the Pacific.
182: CTB? Cretaceous Tertiary Boundary (rather than KPg)?
189: once again, I do not see that coeval extinction of groups during a major mass extinction (when many things went extinct) has anything suggestion to make as to their trophic relations.
191-206: In my opinion it just is not true according to most evidence that the associated extinction (during the KPg) coincided with (i.e., occurred at the same time) as the rise of holoplanktonic gastropods, specifically Thecosomata. If we look at some recent papers (as well as those cited in lines 202-204), then it becomes clear that the ‘rise of the holoplanktonic gastropods’ (if equated with the increase in diversity of thecosomata) considerably post dated the KPg (and the extinction of ammonites): we see a single taxon in the Campanian and the Paleocene, with increased diversity only by the earliest Eocene, i.e., more than 10 million years after the KPg extinction. I realize that the cited Corse et al. say that there was a diversifying event ‘just after the Cretaceous/Tertiary mass extinction’, but the paper that they cite for this statement in fact only describes occurrence of pteropods in the Eocene, which in my opinion cannot possibly be called ‘just after the Cretaceous Tertiary mass extinction’ – even in geology I do not call 10 myr later ‘just after’.  I suggest that the authors look up recent articles by Janssen & Peijnenburg, 2017, An overview of the fossil record of Pteropoda (Mollusca, Gastropoda, Heterobranchia)Cenozoic Research 17(1), 3-10, and look at their nice compilation figure, Burridge et al., 2017, Time-calibrated molecular phylogeny of pteropods. PlosOne, 12(6): e0177325, who state ‘Using a fossil-calibrated phylogeny that sets the first occurrence of coiled euthecosomes at 79±66 mya, we estimate that uncoiled euthecosomes evolved 51±42 mya and that most extant uncoiled genera originated 40±15 mya.’ , and Janssen, A. W., Sessa, J. A., and Thomas E., 2016. Pteropoda (Mollusca, Gastropoda, Thecosomata) from the Paleocene-Eocene Thermal Maximum of the United States Atlantic Coastal Plain., Palaeontologia Electronica, Article 19 (3), 1-26. These all show diversification of holoplanktonic gastropods in the Eocene (as did the paper cited in Corse et al). I guess one could still compare the ecological role of holoplanktonic gastropods and compare to juvenile ammonites, but the authors argue that the latter replaced the former shortly after their extinction, and that is not supported by the literature cited above - see below.
213-214, 216-217: yes, quite a few pteropods have been reported from the Eocene, but that is NOT ‘just after the K/Pg extinction.
221-223: the baleen whales may have replaced giant Cretaceous planktivorous fish as to ther ecological role, but as shown in fig. 3, they only evolved in the earliest Oligocene (during the cooling of the Earth and establishment of Antarctic ice sheets, commonly (though not universally accepted) linked to diversification and increased abundance of diatoms; see e.g., Norris et al., 2013, Science, 341, 492; Marx & Uhen, 2010, Science 327, 993). So it seems to me not valid to link the origin/diversification of whales to extinction of large Cretaceous planktivorous fish more than 30 million years earlier.
228: there were no early Paleogene (=Paleocene-Eocene) whales. Please document early Paleogene chondrichthyans- provide reference (also 255: which 3 lineages? Provide reference).
252-253: there was no Paleocene expansion of Thecosomata (at least, we have no evidence for that), there was an Eocene (10 million years later) expansion.


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 OLD AND THE NEW PLANKTON: ECOLOGICAL REPLACEMENT OF ASSOCIATIONS OF MOLLUSC PLANKTON AND GIANT FILTER FEEDERS AFTER THE CRETACEOUS?
Review round: 1
Reviewer: 2

Output:
Basic reporting: English is generally good; I have marked up some suggested word changes and typographical errors in the pdf of the manuscript.

References are very thorough and capture the context of the paper's topic well. They do need to be proofread more carefully, as there are inconsistencies in citation format, e.g., abbreviating vs. not abbreviating journal titles, capitalizing each word in book titles vs. not, including "Topics in Geobiology" and volume number vs. not.

The figures are beautifully constructed, but are not described or discussed in any detail in the text. They really need to be explained more both in the text and in the figure captions. For example, Fig. 2 does not provide units for the zooplankton plots. Are these numbers of species? Numbers of genera? A percentage? What is the reader supposed to notice from looking at these plots? In Fig. 3, what are the colored dots and black lines in the plot supposed to represent? What is the reader supposed to learn from this figure? How does this figure support the author's argument? It is worth the authors' time to describe the figures and their message within the text.
Experimental design: The topic of what role hatchling ammonoids and belemnoid played in Cretaceous planktonic food webs, and how they and their potential predators were replaced after the end-Cretaceous extinction, is an interesting one that has not been well-explored in the past.

The research questions are not presented very clearly in the introduction. The authors state that they consider two research questions (lines 54-59), but the first item is not phrased as a question at all. It would be helpful to rewrite this paragraph, making the questions as explicit as possible.

The methods used to estimate the fecundity of large Cretaceous ammonoids are clearly explained and make sense; these are the primary new contribution. Much of the rest of the paper involves synthesis of various observations derived from the published literature.
Validity of the findings: The authors primarily use valid existing published data and observations, plus reasonable new calculations of the likely gonad volume and egg production of the largest known Cretaceous ammonoid Parapuzosia seppenradense, to argue for the importance of ammonoid hatchlings in the zooplankton of Late Cretaceous oceans. They then discuss some likely predators on these hatchlings, as well as replacement taxa for both hatchlings and their predators after the end-Cretaceous extinction. While somewhat speculative, these discussions are supported by reference to observations in the existing literature.

One concern I have is that the belemnoids seem "tacked on" to the paper, with just brief discussion of their importance to Cretaceous planktonic food webs. It would be helpful if the authors could add a little more information and/or data about belemnoids to support their claims.
Additional comments: This paper makes an interesting and well-supported case for the importance of ammonoids and belemnoids in Cretaceous planktonic food webs. I do note a few key issues to address in a revision (in order of importance):

1) Reframe the paragraph that presents your research questions. Make the research questions actual questions, and ideally phrase them to go beyond the descriptive (e.g., "what groups might have...?") to test a hypothesis or prediction.

2) Make better use of the figures by describing them in the text, making clear what the reader should be learning from each one, and adding more information to the captions explaining figure components.

3) Amplify the discussion of belemnoids, which seems like an afterthought in this version of the manuscript.

4) Ensure references are consistent in their format.


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 OLD AND THE NEW PLANKTON: ECOLOGICAL REPLACEMENT OF ASSOCIATIONS OF MOLLUSC PLANKTON AND GIANT FILTER FEEDERS AFTER THE CRETACEOUS?
Review round: 1
Reviewer: 3

Output:
Basic reporting: Writing is generally clear but sometimes fuzzy in few sentences. Some typos also pervade the MS. This is minor but I recommend that the authors review the paper for wording/style.

L.23: fishES?

Introduction: maybe too short. Authors can add for instance some known examples of potential similar replacements in the fossil record.

l.32: mass extinction intervals: what does it means exactly? They are more short events than intervals. Maybe reword this sentence.

l.36-38: This needs a few references. Also, it may depend on if you are talking about taxonomic richness and/or functional diversity. See e.g. recent works of Foster et al. on the PT and TJ extinctions.

l.43: flood-basalt-eruptions => flood basalt eruptions

l.49: Ammonoids “evolved a great disparity”: I suggest to rephrase this sentence.

l. 50: “bizarre forms”: maybe refer directly to heteromorphs.

l.51: please rephrase the beginning of this sentence.

l. 53: “they also occurred worldwide and in great numbers”. I suggest to modify this sentence, e.g.: “they also abundantly occurred worldwide”

l.63: maybe add in the sentence if this is true for all ammonoids and periods (?).

l.66: a space is missing after “(iii)”.

l.85-89: if possible, could be nice to highlight abbreviations for measurements in italics.

l.90: “as demonstrated by”: I’m not very prone to use such terms in articles. Maybe “as shown by” (or equivalent) is more appropriate. Same apply l. 212 “undoubtedly” is likely too strong.

l.90: “derived ammonoids”: unclear, please add a definition and details.

l.113-117: Important point: I expect this is a mistake but please do not use L² to refer to a volume!! => L3.

l.118-120: iteroparity vs semelparity: what is the most realistic based on the known fossil and modern data (if any)?

l.121: “fecundity would further increase”: unclear for me, especially the link with growth of embryos after they were laid. Please add an explanation and potential references (even if these are for modern cephalopods).

l.124: => Cretaceous

l.134: “high fecundity corresponded with high mortality”: this may appear rather authoritative. You should explain why, is this always the case and add references on that topic.

l.137: are we sure that belemnites were in direct competition with other coleoids? With all coleoids?

l.136-140: In my opinion, such general sentence on belemnites should arrive earlier in the ms, e.g. in the same part authors present ammonoids and their first ontogenetic stages. It could also be nice to see a little bit more space devoted to belemnites in the introduction.

l.178-185: this sentence is really too long to be well understood.

l. 182 CTB: add definition of this acronym.

l.178-185, l.189-191 and at some other places in the ms: authors often link potential trophic relationships among organisms with associated extinctions among the same organisms. I don’t say this is not the case but this should be nuanced as this link is far to be evident and may result from environmental changes or other biotic interactions.

l.206-207: “compare the UNCOILING of the conch of Thecosomata with the COILING of ammonites”: in my opinion, this sentence sounds very strange. What are the potential “macroecological implications”?

l.212-213: may add references on that point.

l.213-215: a “few pteropods” “implies that they were abundant and widely distributed”… strange wording I think. Please clarify the sentence by making a better link with previous sentences.

l.219: “instalment”: what does it means?

l.233: late => Late?

Fig. 2: Maybe shift the gastropod data on the other side, near the ammonite and belemnite data, for clarity.

References: they are sometimes in chronological order, sometimes in alphabetical order. Maybe homogenize them if you have instructions from PeerJ.
Experimental design: No comments.
Validity of the findings: This is my first review for PeerJ and I am not sure how the following comments fit well here or should be placed in Comments for author.
This work mainly resembles a short review on some “ecological replacements” that are observed during the KT transition. The working hypothesis is interesting because results support that ammonites and belemnites eggs and embryos may have served as food resources during the Cretaceous and that their disappearance at the KT boundary led to extinction of their potential predators. Such an idea is not totally new. The hypothesis of their replacement by holoplanktonic gastropods in food webs is also interesting as well as the discussion about potential new predators feeding on these small-sized organisms. We have nevertheless only rare direct fossil evidences for such feeding; the final discussion/conclusion is therefore partly speculative, but presented as such. To slightly enlarge the discussion and maybe yield slightly more balanced scenario, authors may preliminary answer to some associated questions: for instance, can other potential candidates than holoplanktonic gastropods have also served as potential food resources for filter feeding predators. What about crustaceans at that time? Are they too small? Too rare? Also to complement the discussion: are similar potential replacements (not necessarily complete) between an ammonite subgroup and another marine clade that has been documented (or speculated) in the Paleozoic, Triassic or Jurassic? This might be a point to address. Just a (probably naive) thought: can we imagine that largest ammonites also fed on smallest ones, thus reducing the number of available preys for other groups leading to an “equilibrium” inside the ammonoid clade?
Additional comments: This short MS presents an interesting working hypothesis on ecological/functional successions during the KT transition. This is relevant for PeerJ. I suggest to slightly enlarge some discussion points and I have highlighted a few areas that may benefit from some clarifications or rewording. I recommend publication after minor revision.


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

Input:
Title: PREVENTIVE EFFECTS OF  SALVIA OFFICINALIS LEAF EXTRACT ON INSULIN RESISTANCE AND INFLAMMATION IN A MODEL OF HIGH FAT DIET-INDUCED OBESITY IN MICE THAT RESPONDS TO ROSIGLITAZONE
Review round: 1
Reviewer: 1

Output:
Basic reporting: MR. Ben Khedher and colleagues investigates whether Salvia officinalis (Sage) leaf extract prevent insulin resistance and inflammation in high fat diet-induced-obesity mice model. It should be emphasized that 598 papers (see Pub Med) were written about the sage effects. Among these references, it is described that sage exerts hypoglycaemic and anti-dyslipidemic effects in diabetic subjects (https://www.ncbi.nlm.nih.gov/pubmed/27942500; https://www.ncbi.nlm.nih.gov/pubmed/25340127; https://www.ncbi.nlm.nih.gov/pubmed/21506190).
This study may be considered original (inflammatory state related adipose tissue) and may follow a publication. In spite of that, some ambiguities need to be clarified.

Problematic question: Why the authors chose to compare the sage effects to rosiglitazone properties, whereas this oral anti-diabetic molecule (Avandia©) has been severely criticized due to cardiac complications leading many deaths, such as myocardial infarction and then withdrawn from the market since 2002. The prestigious British journal NEJM evaluated the deleterious effects of rosiglitazone (https://www.ncbi.nlm.nih.gov/pubmed/17517853).  Thanks to argue this aspect.

Relevant question: Sage can also leads to cardiovascular complications effects like rosiglitazone? The authors did not investigate this point in their study (effect on blood pressure?) and no discuss in discussion section. Indeed, in conclusion, the authors confirm that: at low dose, Sage exhibits similar effects to rosiglitazone? Thanks to argue this aspect.

In addition, it is recommended that Rosiglitazone appear in the article-title. For example: “Preventive effects of salvia officinalis leaf extract versus Rosiglitazone on insulin resistance and inflammation, in high fat diet-induced-obesity mice model”
Experimental design: Diet: 60% fat by energy value is no sufficient. What is the ratio of diet lipid composition to saturated, monounsaturated and polyunsaturated fatty acids, respectively? Also, the composition to others nutriments: proteins, carbohydrates, vitamins and minerals?

Fasting time: 5 hours is insufficient to study metabolism. 16 hours minimum. What protocol and reference?
Insulin resistance (IR): The protocol used is not clear. Why to use Oral Glucose Tolerance Test and the Insulin Tolerance Test separately? In practice (experimental animal but not in human), IR is evaluated by the hyperinsulinemic euglycemic clamp. HOMA model is no sufficient. Please clarify this point.

Obesity mice model or diabetic mice model? As the authors studied rosiglitazone (oral antidiabetic), It is important to confirm the mice C57Bl6 (transgenic model) is also a model of type 2 diabetes, and to be associated with insulin resistance. The authors have not studied. Please clarify this point.

Statistical analysis: The correlation test (Pearson test) between the comparative effects between sage and rosiglitazone is missing. Student t-test is no sufficient.
Validity of the findings: In vitro versus in vivo: The results are obtained from both the pre-adipocytes cells (3T3-L1) and mice (in vivo study). What relationship between these two studies, since the cells were not isolated from the obesity model mice (C57Bl6)?

Anthropometric parameters: This study concerns obesity related to glucose tolerance. Although in Table 1 the authors present the weight variations, Results not show whether sage extract effect on Body mass index variation. In addition, the imaging data (Lean and fat mass were measured by Nuclear Magnetic Resonance) for the assessment of fat qualitative mass composition (subcutaneous or visceral) have not been shown.

Lipogenesis versus lipolysis: There is confusion in the data to explain the lipids metabolism effects of sage. The authors confirm that sage exerts both lipogenic and anti-lipolytic effects at the same time (Line 267:... however sage-treated animals had a decrease in plasma NEFA and triglycerides levels, suggesting an inhibition of lipolysis…. Line 271:... the plant extract reduced lipogenesis…). Please clarify this point.

Sage inefficacity or sage toxicity: Line 317:...   This might explain the beneficial effect on food intake of sage low dose when compared to high dose…
It’s not clear the dose effect of sage. If sage has no beneficial effect at high doses, can to become toxic? In this case, how will sage be correlated with rosiglitazone? Please clarify this point.
Additional comments: Thank you to see critical above.

In Figure 5, authors should correct that panel A: is anti-inflammatory cytokines and panel B: is pro-inflammatory cytokines.


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: PREVENTIVE EFFECTS OF  SALVIA OFFICINALIS LEAF EXTRACT ON INSULIN RESISTANCE AND INFLAMMATION IN A MODEL OF HIGH FAT DIET-INDUCED OBESITY IN MICE THAT RESPONDS TO ROSIGLITAZONE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors report positive effects of methanol extracts of Sage (salvia officinalis) on inflammation, obesity and diabetes related parameters both in vitro in 3T3L1 adipocyte differentiation model and in vivo in a high fat nutritional obesity mouse model. The authors appropriately conducted tests related to obesity and diabetic related studies that include glucose and insulin tolerance test and further evaluate the effects of Sage extract on adipokine leptin and inflammatory proteins. Although the in vitro data from differentiated 3T3L1 does not completely correlate with the in vivo data regarding the lipolytic effects of Sage, the authors successfully demonstrate positive effects in both models. In general, the manuscript is sound in logic and writing. The conclusions support the results. Appropriate statistical tests have been performed. Please refer to general comments for the reviewer’s critique.
Experimental design: No comments
Validity of the findings: No comments
Additional comments: 1)	Since the Sage extract contain several active compounds including toxic compound like alpha and beta-thujones, have the authors conducted a toxicity profile of the methanol extract of Sage. I would recommend a annexin-PI staining of the 3T3L1 cells and a TUNEL staining of frozen section of liver tissue after treatment with SAGE.
2)	The authors claim that the presence of several ppar gamma and alpha agonists in the SAGE extracts may be responsible for the observed effects. I would recommend the authors to do a selective knockdown of PPAR gamma or alpha in 3T3L1 adipocytes and/or use the adipose specific knockout mouse model for the PPAR receptor gamma or alpha to prove the validity of results. Alternatively, in addition to the above suggested experiments, can the authors selectively treat cells with ppar gamma or alpha agonists observed in the Sage extract with mass spectrometry data alone or in combinations in vitro to demonstrate the validity of their results.
3)	The reviewer would recommend the authors to represent all the in vivo bar graph data for ELISA as scattered or aligned dot plots.


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: PREVENTIVE EFFECTS OF  SALVIA OFFICINALIS LEAF EXTRACT ON INSULIN RESISTANCE AND INFLAMMATION IN A MODEL OF HIGH FAT DIET-INDUCED OBESITY IN MICE THAT RESPONDS TO ROSIGLITAZONE
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a well written manuscript that addresses the effect of sage extract on insulin sensitivity. Sufficient literature references and background context has been provided.
Experimental design: How was the differentiation of adipocytes confirmed? Were adipocytes markers evaluated in the differentiated cells to validate the differentiation? Also, the markers should be tested when differentiation was carried in presence or absence of the extract.

The authors have used two dosing concentrations of sage extract? How were these doses finalized? Also are these doses the weight of the total extract?

What kind of validation was performed on the extract to check for the reproducibility of the contents and concentrations of the component of the extract?

More details about the change in body weight from baseline before treatment to end of the treatment should be presented as a validation of the HFD.

The authors have performed a post-hoc dunnett’s multiple comparison tests that compares the means of the treatment group to the control group. Maybe the authors should consider doing something like Tukey’s to compare all the groups so that they can also judge the difference in effects of the two treatment concentrations.
Validity of the findings: The authors need to touch upon various aspects of HFD model in their discussion to tackle the drawbacks. Male mice are more susceptible to hyperglycemia and inflammation compared to female mice. Further more the authors purport that their study has an advantage over the previous studies since they have used a HFD model vs drug induced diabetes. However they also need to address issues like T2D is a more age associated disease and is more common in the older population. Studies hence caution the use of younger mice.
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: PREVENTIVE EFFECTS OF  SALVIA OFFICINALIS LEAF EXTRACT ON INSULIN RESISTANCE AND INFLAMMATION IN A MODEL OF HIGH FAT DIET-INDUCED OBESITY IN MICE THAT RESPONDS TO ROSIGLITAZONE
Review round: 2
Reviewer: 1

Output:
Basic reporting: 1. BASIC REPORTING

MR. Ben Khedher and colleagues investigates whether Salvia officinalis (Sage) leaf extract prevent insulin resistance and inflammation in high fat diet-induced-obesity mice model. It should be emphasized that 598 papers (see Pub Med) were written about the sage effects. Among these references, it is described that sage exerts hypoglycaemic and anti-dyslipidemic effects in diabetic subjects (https://www.ncbi.nlm.nih.gov/pubmed/27942500; https://www.ncbi.nlm.nih.gov/pubmed/25340127; https://www.ncbi.nlm.nih.gov/pubmed/21506190).
This study may be considered original (inflammatory state related adipose tissue) and may follow a publication. In spite of that, some ambiguities need to be clarified.

Problematic question: Why the authors chose to compare the sage effects to rosiglitazone properties, whereas this oral anti-diabetic molecule (Avandia©) has been severely criticized due to cardiac complications leading many deaths, such as myocardial infarction and then withdrawn from the market since 2002. The prestigious British journal NEJM evaluated the deleterious effects of rosiglitazone (https://www.ncbi.nlm.nih.gov/pubmed/17517853).  Thanks to argue this aspect.

Relevant question: Sage can also leads to cardiovascular complications effects like rosiglitazone? The authors did not investigate this point in their study (effect on blood pressure?) and no discuss in discussion section. Indeed, in conclusion, the authors confirm that: at low dose, Sage exhibits similar effects to rosiglitazone? Thanks to argue this aspect.

In addition, it is recommended that Rosiglitazone appear in the article-title. For example: “Preventive effects of salvia officinalis leaf extract versus Rosiglitazone on insulin resistance and inflammation, in high fat diet-induced-obesity mice model”
Experimental design: Diet: 60% fat by energy value is no sufficient. What is the ratio of diet lipid composition to saturated, monounsaturated and polyunsaturated fatty acids, respectively? Also, the composition to others nutriments: proteins, carbohydrates, vitamins and minerals?

Fasting time: 5 hours is insufficient to study metabolism. 16 hours minimum. What protocol and reference?
Insulin resistance (IR): The protocol used is not clear. Why to use Oral Glucose Tolerance Test and the Insulin Tolerance Test separately? In practice (experimental animal but not in human), IR is evaluated by the hyperinsulinemic euglycemic clamp. HOMA model is no sufficient. Please clarify this point.

Obesity mice model or diabetic mice model? As the authors studied rosiglitazone (oral antidiabetic), It is important to confirm the mice C57Bl6 (transgenic model) is also a model of type 2 diabetes, and to be associated with insulin resistance. The authors have not studied. Please clarify this point.

Statistical analysis: The correlation test (Pearson test) between the comparative effects between sage and rosiglitazone is missing. Student t-test is no sufficient.
Validity of the findings: In vitro versus in vivo: The results are obtained from both the pre-adipocytes cells (3T3-L1) and mice (in vivo study). What relationship between these two studies, since the cells were not isolated from the obesity model mice (C57Bl6)?

Anthropometric parameters: This study concerns obesity related to glucose tolerance. Although in Table 1 the authors present the weight variations, Results not show whether sage extract effect on Body mass index variation. In addition, the imaging data (Lean and fat mass were measured by Nuclear Magnetic Resonance) for the assessment of fat qualitative mass composition (subcutaneous or visceral) have not been shown.

Lipogenesis versus lipolysis: There is confusion in the data to explain the lipids metabolism effects of sage. The authors confirm that sage exerts both lipogenic and anti-lipolytic effects at the same time (Line 267:... however sage-treated animals had a decrease in plasma NEFA and triglycerides levels, suggesting an inhibition of lipolysis…. Line 271:... the plant extract reduced lipogenesis…). Please clarify this point.

Sage inefficacity or sage toxicity: Line 317:...   This might explain the beneficial effect on food intake of sage low dose when compared to high dose…
It’s not clear the dose effect of sage. If sage has no beneficial effect at high doses, can to become toxic? In this case, how will sage be correlated with rosiglitazone? Please clarify this point.
Additional comments: Thank you to see critical above


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

Input:
Title: PREVENTIVE EFFECTS OF  SALVIA OFFICINALIS LEAF EXTRACT ON INSULIN RESISTANCE AND INFLAMMATION IN A MODEL OF HIGH FAT DIET-INDUCED OBESITY IN MICE THAT RESPONDS TO ROSIGLITAZONE
Review round: 2
Reviewer: 2

Output:
Basic reporting: This reviewers comments have been adequately addressed. However the reviewer would appreciate that the authors show a toxicity profile of SAGE extract with a more robust assay like annexin v-PI staning.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: Acceptable revision. No further 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: PREVENTIVE EFFECTS OF  SALVIA OFFICINALIS LEAF EXTRACT ON INSULIN RESISTANCE AND INFLAMMATION IN A MODEL OF HIGH FAT DIET-INDUCED OBESITY IN MICE THAT RESPONDS TO ROSIGLITAZONE
Review round: 2
Reviewer: 3

Output:
Basic reporting: None
Experimental design: None
Validity of the findings: None
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: BEYOND HARM’S REACH? SUBMERSION OF RIVER TURTLE NESTING AREAS AND IMPLICATIONS FOR RESTORATION ACTIONS AFTER AMAZON HYDROPOWER DEVELOPMENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, the writing and style of the manuscript is high quality, concise, and easy to follow. The paper utilizes pre- and post-dam data to analyze the impact of a dam’s reservoir on one species, which is an important, but many times neglected, element of understanding the realized impact of hydropower projects. A minimal amount of text (specific suggestions given) added to the methods and results will aid in reader understanding.

Given the high predation of turtle nests by humans, the authors should acknowledge the complex impact of dams on local humans, specifically that human-ecosystem relationships change in ecosystems altered by dams. Human predation on the turtles is discussed in one paragraph of the discussion, and there is just one sentence stating that humans in the submergence zone are compensated but that these turtles have not been considered. No acknowledgment is made by the authors that this compensation to humans is rarely, if ever, equivalent to the economic loss suffered by the displaced peoples (McCully 2001). It would be appropriate to briefly discuss the situation of these displaced peoples, if known from personal communication (potentially 244 families according to the EDP annual report 2013), and how this could potentially relate to the increased pressure on turtle nests, especially given the higher density of (and ease of finding) nests. Given the impact of dams on turtle nest-areas, it seems like decreasing human predation on turtle nests would be a critical component of turtle conservation in this area and a necessary component of mitigation efforts (in addition to those mitigation efforts suggested by the authors: BACI studies, restoring bank and island habitat, and protective legislation).
Experimental design: The experimental design is well suited to answer the proposed research question, how far upstream the reservoir impacted one species of turtle and whether this result was accurately reflected in the environmental impact assessment.

Line 123: Remove “potential and effective” before turtle nest-areas, as the description comes in the following paragraph.

Line 130: Please add one sentence clarifying how you determined potential nest-areas. Was this done by walking the banks and mapping all areas in the 66 km stretches of riverbank not covered by rock/boulders/root/clay substrates? Please move the other sentence describing potential nest-areas (Lines 146-147) to this earlier description. Please also state in this description that potential does not include effective (this was made clear by Table 1).

What about the nest-area designations being potential and actual (instead of effective) nest-areas? Effective may suggest to some readers that the nest was successful in producing young.
Validity of the findings: I found the majority of the results presented in a clear manner. Readers would be interested in the authors’ speculation in the discussion on how changing water levels in the reservoir would affect turtle nesting habitat and how the dam and altered flows could affect migration patterns.

Line 171: Why do you state the percentage of area that is reduced along 60.1 km and not the full study area of 66 km?

Figure 3: Panels A and B are redundant. Please remove. “C” should be capitalized. Please report an equation and R^2 values on the plots for the lines of fit.
Additional comments: Text to add to the “Study area” section: What type of dam is Cachoeira Caldeirão? Who paid for the dam and completed and paid for the EIA?

Be consistent in using pre and post vs pre- and post-

Include the product information for Rapideye

Clayey should be clay

Consistent spacing between numbers and units (Line 152)

Line 189: Remove the statement of novelty

Line 233: Mention that the Congdon paper is referring to the Blanding’s turtle and the location of the study area.

Line 289: Add “are” to reservoirs are built


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: BEYOND HARM’S REACH? SUBMERSION OF RIVER TURTLE NESTING AREAS AND IMPLICATIONS FOR RESTORATION ACTIONS AFTER AMAZON HYDROPOWER DEVELOPMENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: Summary Norris et al. investigated the effect of the construction of a dam on the reproductive success of an aquatic turtle in the Amazon region. The results indicated that the construction of dams had negative effects on the reproductive success of this species. Additionally, the authors proposed some strategies to mitigate these effects.

Overview The article is well written and easy to follow. The analyses are adjusted to theobjectives of the study and the results are adequately discussed. The study has a strong point, which is that it compares the success of nesting before and after the river regulation; however some sections of the manuscript would benefit from further literature support. The study has also important implications for the management of turtle populations in basins impacted by dams.
Experimental design: Overview The article is well written and easy to follow. The analyses are adjusted to the objectives of the study and the results are adequately discussed. The study has a strong point, which is that it compares the success of nesting before and after the river regulation; however some sections of the manuscript would benefit from further literature support. The study has also important implications for the management of turtle populations in basins impacted by dams.
Validity of the findings: The analyses are adjusted to the objectives of the study and the results are adequately discussed.
Additional comments: Specific points
Abstract The introduction of the abstract is excessively long (5/13 lines). I suggest to the authors to reduce it. The authors could use this space to explain (in the last sentence) some of the mitigation proposals.
Introduction In general, it is well structured, although the authors could consider a more general approach at the beginning of the introduction (e.g. effect of dams on riverine biodiversity).
Ln 63-Ln 67. These effects have no interest in the current study, although they could be cited in an introduction to the ecological impact of dams/river regulation. Perhaps a general revision about these impacts could be placed at the beginning of the introduction (including population isolation, reservoirs for invasive species, …).
Ln 64-67. These lines could be moved to the end of the introduction and used to formulate and support a hypothesis.
Methods
The authors could briefly describe the climate of the study area. This would help the reader to understand the nest-area survey timings. They could also (briefly) discuss some aspects of the target species (eg distributional range, natural history -focusing in breeding aspects-, IUCN status) that authors believe could provide more background and strength to their discussion. Non-Brazilian readers may find the article interesting but largely ignore the geographical and ecological frame of this study system.
Ln 118. Are there no references in the literature describing the nesting season of P. unifilis?
Ln 121. I suppose that the difference in the length transects (2011 vs 2015/2016) is explained by the inclusion of a control transect. It should be detailed.
Ln 122. Authors have to specify which are these conditions and include appropriate references.
Ln 134. Authors could consider include references to this method of survey. What are the ‘systematic substrate searches’?.
Ln 158. The software used to implement the GLM should be specified. Also the distribution family assumed for the dependent variable (nesting beaches / km2).
Discussion
Ln 248. Authors should consider include these references.
Ln 268-279. I find this part of the discussion interesting and ‘ethically’ justified, but completely out of context. In my opinion, the discussion should focus on the subject of study. Here the authors could provide some examples (references) explaining that restoring nesting habitats in aquatic turtles is a successful strategy. This would support the mitigation measures proposed below.
Ln 281-294. Apart from the negative impact on nesting, the dam and river regulation may involve some other pernicious effects (some indirect, mediated by predators or competitors) on turtle populations??.
Authors should comment this here or just in the previous paragraph.


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: BOUNDARIES IN GROUND BEETLE (COLEOPTERA: CARABIDAE) AND ENVIRONMENTAL VARIABLES AT THE EDGES OF FOREST PATCHES WITH RESIDENTIAL DEVELOPMENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: This interesting manuscript is dealing with the identification of boundaries in environmental variation and ground beetle community structure using triangulation wombling. Moreover, the authors tried to determine whether these boundaries are related. The topic of the manuscript is very interesting and relevant, since ecological responses to the presence of habitat edges are one of the most extensively researched topics in ecology. The main strength of this manuscript is the use of a novel and powerful spatial partitioning technique, the triangulation wombling, to identify boundaries. Objectively identifying boundaries is a key topic in edge studies, as different groups of organisms may operate at different spatial scales, and what appears as a homogenous patch to one species may comprise a very heterogeneous patchy environment to another. Earlier this manuscript was submitted to the Ecosphere and the Ecology and Evolution and was thoroughly reviewed. Based on the reviewers’ comments, the authors completely re-wrote and substantially improved the manuscript. The present form of the manuscript is generally well written. The analyses are well explained and straightforward, and the discussion is sound. The most recent edge studies on ground beetles (e.g. Urban Ecosystems, 20: 971-981, 2017; Forest Ecology and Management, 384: 371-377, 2017; Journal of Insect Conservation, 20: 49-57, 2016; Ecological Research, 31: 799-810, 2016), however, are not referred in the manuscript. Please cite and discuss these papers. Based on the above, this manuscript is valuable and should 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: BOUNDARIES IN GROUND BEETLE (COLEOPTERA: CARABIDAE) AND ENVIRONMENTAL VARIABLES AT THE EDGES OF FOREST PATCHES WITH RESIDENTIAL DEVELOPMENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: I am not an expert on beetles, pit traps, nor triangulation-based methods, so I can only comment from a general science and statistics perspective.

I don't know the "triangulation wombling" was explained well for a journal of general readership. E.g.:
"Second, we calculated a rate of change and its orientation for each triangle using the values of a variable of interest at the triangle’s vertices."
Rate of change of what with respect to what? How do you define the "orientation" of a triangle?
I had to look up the referenced book to determine that "traingulation wombling" involves a finite-difference method for approximating spatial derivatives in multiple dimensions and orientation is that of the approximated gradient.
This method naturally would involve some assumptions about continuity that I doubt are checked in practice, but for detecting "boundaries" that run perpendicular to large gradients perhaps that doesn't matter.

From a statistical perspective, the layers of estimation atop the data were a bit uncomfortable.
First, finite-difference derivatives are calculated.
From that boundaries are detected at p=10% significance and with various thresholds.
Then the boundary overlaps were calculated, also at p=10% significance.
This looks like a typical use of this method, but I do not find it ideal.

Otherwise, the paper looks fine to me.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: RESOUNDING FAILURE TO REPLICATE LINKS BETWEEN DEVELOPMENTAL LANGUAGE DISORDER AND CEREBRAL LATERALISATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is generally clear and well written, and the coverage of literature is appropriate. The tables and figures are clear. If anything, the data are over-analyzed, but this is understandable given that the results are largely negative with respect to the hypotheses under test—and with respect to previous claims. Some of the statistical techniques will be unfamiliar to many readers, but as far as I can tell they are appropriate.

I think the formula for computing LI should be given, along with more detail as to how their significance was tested for the assignment into laterality groups (binomial? T-test?).

The data have been made publically available.
Experimental design: One concern with the design is that the study was based on twins, and there might be some question as to whether the results can be generalized to nontwins. This is perhaps a relatively minor issue, although there is some evidence, again inconsistent, that twins may be slightly more likely to be left-handed than nontwins (as claimed, for example, by Annett). It might be worth citing the very large-scale study by Medland et al.. (2009,  Neuropsychologia, 47, 330-337) showing effectively no difference in handedness between twins and nontwins, or between MZ and DZ twins. The idea that MZ twins of opposite handedness derive from mirror-splitting of the ovum can probably be dismissed, as the authors suggest, and it might be worth noting that the left-handed member of mirror pairs is typically left-dominant for language—just as left-handers in  general are  (e.g., Badzakova-Trajkov, et al.,  2010. Neuropsychologia, 48, 3086-3093).

The authors cite McManus (1981) as evidence that handedness is unaffected by birth stress, although there are (or were) claims to the contrary, and there may be more than just birth stress that differentiates twins from nontwins.

It seems that the groups were not completely matched on IQ, and given the standard deviations I suspect the difference may be significant. Of course this partly reflects the language impairment in the DLD group, but I wondered whether they might be matched on nonverbal IQ.

It would also have been useful to know whether there were differences between the MZ and DZ twins. I realize that this will be the topic of another report, but I did wonder whether it might qualify the results reported here. The sex difference might also be a (minor) issue, and I think it is generally better to include possible confounding effects in the model rather than dismiss them if their effects are not significant.

These are actually fairly minor points, and the results are compellingly negative even if they are considered. Any minor deficiencies in design can be weighed against the fact that the samples were impressively large, and the analysis comprehensive. I might add though that previous reports of significant effects should not be attributed to lack of power, which has to do with Type II error, not Type I error.
Validity of the findings: In spite of some minor issues of design, the results are impressively negative with respect to the hypotheses being assessed. Acceptance of a null hypothesis (or rejection of the experimental hypothesis) is always an issue, given the logic of hypothesis testing, but here the p-values are impressively large.

I wondered if the finding of a slight right-hemisphere bias for the TD group might reflect different strategies during the fTCD sessions. Perhaps some of the participants were more likely than others to incorporate mental imagery while describing the cartoon action. I wonder if the results would have been different had a task without a visual component, such as word generation, been used. The authors do acknowledge that use of different measures of cerebral asymmetry might yield different results.
Additional comments: This is a bold and commendable report, especially given that it seems to contradict some of your own previous findings.


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: RESOUNDING FAILURE TO REPLICATE LINKS BETWEEN DEVELOPMENTAL LANGUAGE DISORDER AND CEREBRAL LATERALISATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article meets the necessary standards - it is clear, with professional English used throughout.
The article does cite sufficient and relevant references although I note that one review that seems very relevant and complementary to this paper has not been cited - Mayes et al Dev Med Child Neurol. I think this was a 2014 or 2015 publication and am sure it focused on MRI evidence for or against the lateralisation hypothesis. It concluded that the field is a mess due to small numbers of participants, inconsistent MRI methodologies in terms of data acquisition and analysis methods etc. Whilst an MRI method was not applied in this paper, I would imagine that the findings of this review would serve to further strengthen the rationale for yet another study in this area (ie you address a number of the limitations of the field reviewed in their paper)?
The paper has a professional article structure and is self-contained with relevant results to the hypothesis posed.
Experimental design: Question is well defined. Strong participant numbers for this field. Rigorous investigation performed to a high standard.
Validity of the findings: No comment
Additional comments: This is a careful body of work that builds on past related work by this leader of the field and team. I wonder if there is any room for inclusion of genetics discussion in this paper? Is Clyde Franks and team at Max Planck Institute in Nijmegen working in this space re genetics. Would be worth adding in a few lines on what has been found around hereditary links for language, lateralisation and handedness. Could this be an important missing variable in the debate in this field - ie we keep focusing on brain and behaviour but are genes missing here to make this a more sophisticated argument and get us into more specific genotyping of cases ...presumably this is a highly complex genetic relationship that will not be unravelled for many decades - but perhaps worth a mention as regards future direction...


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: IS THERE A LINK BETWEEN AGING AND MICROBIOME DIVERSITY IN EXCEPTIONAL MAMMALIAN LONGEVITY?
Review round: 1
Reviewer: 1

Output:
Basic reporting: citations are missing
Experimental design: The issues with experimental design are closely linked to the validity of findings, so these are commented on below.
Validity of the findings: This study investigates the anal microbiome of Myotis myotis collected at different localities in France.  The authors frame the analysis of microbiome composition in terms of aging, as these bats can be long lived.

The authors find no significant differences between sexes or ages, and conclude that this species has a static anal microbiome and that this is relevant to aging.  They also comment on the abundance of Proteobacteria and certain functional categories that were inferred and how they think these observations are relevant to aging.

There were multiple aspects of the interpretation and data presentation of this article that are problematic. One of the most obvious flaws is that the microbiomes are said to be 'stable' over time.  In the discussion it is stated that microbiomes are "unchanging" between ages.  Although not explicitly presented, it appears, for example from consideration of the range in number of OTUs observed from sample to sample, that there is considerable variation in this dataset (interindividual).  How does one reconcile the wide latitude in differences among individuals with the notion that there is an aspect of stability that helps protect bats from aging?

How does the fact that the dataset appears to only include bats that are not at the upper end of the life span influence the ability to design a robust study to look at microbiomes in bat aging? It seems that it would preclude the ability to address the question, and that the comparison of results in humans and mice is not valid.  Given that these bats appear to roost in groups, how could microbiome dispersal effects arising from social interactions (Elife. 2015 Mar 16;4. doi: 10.7554/eLife.05224.) erase any age-related patterns?  Bats were collected at different localities, but the effect of locality, was not assessed.

If only some bats are considered to be long lived (if this is the case), how is the observation that Proteobacteria is apparently a bat-wide association relevant to aging?

The discussion of functions inferred from the metagenomes appears to only include a list of general functions that are the most abundant in bacterial genomes in many datasets.  I don't see any function frequencies that stand out from the norm for a digestive microbiome, although the authors conclude that the presence of metabolic pathways, among others, is somehow signal for the specific bat-bacteria energetic relationship. It doesn't seem likely that tabulating the frequency of KEGG terms summarized at some ontological level, and summarized across all bacteria in a microbiome, then doing a test for frequency differences between groups would be empowered to understand any age-related functional differences.  It may be worthwile for the authors to consider methods presented in this recent work (Integr Comp Biol. 2017 Jun 28. doi: 10.1093/icb/icx011. ).

The authors rarefy their dataset.  There has been a sound statistical justification for not doing so.  Please see (PLoS Comput Biol. 2014 Apr 3;10(4):e1003531. doi: 10.1371/journal.pcbi.1003531.).

The authors state that there was "apparent separation of bat to other mammals in PCoA".  Visual inspection of the plot does not support this statement (Sup. Fig. 5), but more importantly, such statements must be based on statistical testing, and this is not the case.

Although studying the occurrence of competitive exclusion in microbiomes is interesting, it doesn't seem that the putative identification of bacterial genera that belong to families that include pathogens warrents any mention of this ecological phenomenon.  There is no functional analysis presented to support that observed lineages compete for niche space with known pathogens.

The conclusion of this manuscript is very speculative, and not supported by the data.  For example, there appears to be no data connecting Proteobacteria, any of the observed functions, and biology that has effects on longevity.
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: IS THERE A LINK BETWEEN AGING AND MICROBIOME DIVERSITY IN EXCEPTIONAL MAMMALIAN LONGEVITY?
Review round: 1
Reviewer: 2

Output:
Basic reporting: Graham Hughes and colleagues present an interesting article about the gut (anal) microbiota variation across age in bats. The manuscript is well written and well supported using many references, and the structure of the article is correct. Besides, I believe this is the first paper dealing with this topic in Chiropterans, thus it is a timely and original work. They found no effect of age, which contrasts with the general trend observed in other organisms where microbiota composition varies and becomes more diverse through development. I think this finding is relevant.

However, the employed methodologies (or at least the way to present them) have major limitations, and I think they are not appropriate to in depth in the interpretation of the results. I feel that many interpretations of the data and conclusions are too courageous considering the employed approach, namely DNA metabarcoding + Picrust, and I also believe the methodological aspects of the study, or at least the way of presenting them, can be considerably improved.
Experimental design: Regarding the methodology, I think there are two major issues that need modification or further explanation. First, I miss information about negative controls. I have personally used the Illumina Nextera kit and I know how easily cross-contamination and amplification of environmental bacteria can occur. Thus, it is necessary to mention how the effect of these putative problems was controlled, because cross-contamination could make samples more similar (resulting in no differences between groups) and diverse (resulting in larger phylogenetic diversity than previously reported) that what they actually are. I don’t say the results of this study are artifactual, but this experimental design definitely requires negative controls to avoid such problems.

Second, I am also concerned about rarefaction curves and sequencing depths. I can think about two intepretations of the sentence “Samples were rarefied…“ in the methods section, but both are incorrect from my point of view.

FIRST INTERPRETATION (most likely)- First the authors say that the data was rarefied to 8000 OTUs, which I think makes no sense. I think they mean they randomly picked 8000 sequences per sample to level sequencing depth to 8000 sequences. I wouldn’t say that’s rarefying but leveling. Besides, leveling to 8000 OTUs does not make sense, since the number of OTUs of each sample will show the actual diversity. It should be 8000 reads or sequences, depending on when the leveling step was carried out. I guess it was done after quality filtering, thus I would use 8000 sequences. In addition to terminology though, it is not clear how the authors assessed the sequencing depth, and if the employed sequencing depth of each sample was enough for correctly characterizing each amplicon product. They present average values of phylogenetic diversity in Figure 1, but I believe individual information should be provided. In this kind of metabarcoding studies interested in compositional and diversity differences I believe it is necessary to generate OTUs x sequences rarefaction curves for EACH sample, to estimate whether sequencing depth was enough to cover the entire diversity. This can be easily done using the R packages vegan, iNext or DivE. Finally, there are 11 samples with less than 8000 reads according to Table 1, and it is not clear what the authors did with these samples. I think they should be discarded.

SECOND INTERPRETATION (less likely) - If what the authors did was to use a rarefaction and extrapolation method (iNEXT r package, for instance) to estimate the diversity at 8000 sequences (not OTUs) regardless the samples had more or less sequences than 8000 this approach is extremely risky, since diversity estimates will have very uncertain when the number of sequences is very low.

Either case, these methodological issues should be addressed before publishing.
Validity of the findings: The validity of the findings is related to the comments mentioned above.
Additional comments: I also have some minor edition suggestions:

Abstract

“The anal microbiome was sequenced” > make clear you did metabarcoding and not shotgun sequencing, since as it is written now, it seems you have sequenced the whole microbiome, more so when you talk about function in the next sentence.

“Functional gene categories expressed in the M. myotis microbiome” suggest you did transcriptomics, which is not true. Thus, I would use “functional gene categories inferred from metabarcoding data” instead.

Introduction

Line 64: species > organisms

Line 67: make the first sentence more explicit. I suggest: “we have used DNA metabarcoding of the bacterial 16S rRNA gene” (which implies the use of HTS)

Lines 99-112: it should be written somewhere that the weaning/nursing status of juvenile bats was not possible to determine (as it is said in the discussion). Besides, in the discussion, it would be appropriate to add a sentence about the most probable feeding state of the sampled bats based on capture date and average weaning time of Myotis myotis bats.

Lines 120-122: split the library building step and the actual sequencing. It would be more appropriate to write something like: “all 52 samples were built into Illumina sequencing libraries using the Nextera XT (…) and sequenced in a MiSeq platform using 250PE chemistry”

Line 123: mention which scripts from Fastx toolkit were used for the quality filtering

Line 132: I know Picrust requires Greengenes, but according to my personal experience the taxonomy assignment success is larger using Silva, and ideally different databases should be combined (Silva, RDP, Greengenes, NCBI…) (just a comment for the authors).

Line 137: mention the software/script used for rarefaction/leveling/extrapolation…

I hope the authors will address all the issues raised in this report and the improved manuscript will be published in PeerJ, as I think it will be a nice contribution to the literature.

All the best and good luck
Antton Alberdi
University of Copenhagen


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: IS THERE A LINK BETWEEN AGING AND MICROBIOME DIVERSITY IN EXCEPTIONAL MAMMALIAN LONGEVITY?
Review round: 2
Reviewer: 1

Output:
Basic reporting: No problems.
Experimental design: No problems.
Validity of the findings: No problems.
Additional comments: I believe that you provided a very diligent and well-rounded respond to my previous comments. Good 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: IS THERE A LINK BETWEEN AGING AND MICROBIOME DIVERSITY IN EXCEPTIONAL MAMMALIAN LONGEVITY?
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have addressed all the issues I raised in the previous review round.
Experimental design: The authors have addressed all the issues I raised in the previous review round.
Validity of the findings: The authors have addressed all the issues I raised in the previous review round.
Additional comments: The authors have addressed all the issues I raised in the previous review round.


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: ACTIVITIES CONCENTRATION OF RADIOCESIUM IN WILD MUSHROOM COLLECTED IN UKRAINE 30 YEARS AFTER THE CHERNOBYL POWER PLANT ACCIDENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: Comment to manuscript : #20396
Activities concentration of radiocesium in wild mushroom collected in Ukraine after the 30 years from the Chernobyl Power Plant Accident (#20396)

General comment:
Useful data; can be accepted after some upgrade (also with a recent literature)

Suggested improvements:

Is: This accident released huge amounts of radionuclides, including radioiodine and radiocesium, into the  environment, contaminating the lands of Ukraine, the Republic of Belarus, and the Russian Federation (Taira Y et al., 2011).
Suggested correction: This accident released huge amounts of radionuclides, including radioiodine and radiocesium, into the  environment, contaminating the lands of Ukraine, the Republic of Belarus, and the Russian Federation (Taira Y et al., 2011). A cases of a hot spot contamination with radiocaesium and high levels in mushrooms has been recorded also in the nearby countries such as Poland, Sweden or Norway while less elsewhere in Europe (Bakken and Olsen 1990; Cocchi et al. 2017; Falandysz and Borovička 2013; Falandysz et al. 2015, 2016; Strandberg, 2004; Zalewska et al. 2016)
Examplum gratia:
[ Bakken and Olsen, 1990, Accumulation of radiocaesium in fungi. Can J Microbiol 36:704-710
Cocchi et al. , 2017,  Radioactive caesium (134Cs and 137Cs) in mushrooms of the genus Boletus from the Reggio Emilia in Italy and Pomerania in Poland. Isotopes Environ Health Stud 53:doi.org/10.1080/10256016.2017.1337761
Falandysz and Borovička. 2013, Macro and trace mineral constituents and radionuclides in mushrooms – health benefits and risks. Appl. Microbiol. Biotechnol. 97, 477-501 (2013).
Falandysz et al. 2015, Evaluation of the radioactive contamination in Fungi genus Boletus in the region of Europe and Yunnan Province in China.. Appl. Microbiol. Biotechnol. 99, 8217-8224.
Falandysz et al. 2016, Determination of activity concentration of 137Cs and 40K in some Chanterelle mushrooms in Poland and China J Environ. Sci. Poll. Res. 23, 20039-20048.
Strandberg, 2004,  Long-term trends in the uptake of radiocesium in Rozites caperatus. Sci. Total Environ. 327, 315-321.
Zalewska et al. ,  2016, Radiocaesium in Cortinarius spp. mushrooms in the regions of the Reggio Emilia in Italy and Pomerania in Poland. Environ. Sci. Poll. Res. 23, 23169–23174.]

Is: Radiocesium is known to concentrate in wild mushrooms (Hoshi et al., 2000; Travnikova et al., 2001; Hoshi et al., 1994; Kakuda et al., 2006; Smith et al., 1993; Bulko et al., 2014).

Suggested: Radiocesium is known to concentrate in wild mushrooms (Hoshi et al., 2000; Travnikova et al., 2001; Hoshi et al., 1994; Kakuda et al., 2006; Smith et al., 1993) and, as mentioned, the most contaminated originated from the regions of Ukraine, Gomel in Belarus or a countries north and west of Chernobyl (Bakken and Olsen 1990; Bulko et al., 2014; Falandysz et al. 2015; Grodzinskaya et al. 2003 and 2013).

A.A. Grodzinskaya, M. Berreck, K. Haselwandter, S.P. Wasser. Radiocesium contamination of wild-growing medicinal mushrooms in Ukraine. Int. J. Med. Mush. 5, 61-86 (2003).

A.A. Grodzinskaya, S. A. Syrchin, N.D. Kuchma, S.P. Wasser. Macromycetes accumulative activity  in radionuclide contamination conditions of the Ukraine territory. Part 6. - P.217-260, 368-373. In: Mycobiota of Ukrainian Polesie: Consequences of the Chernobyl disaster. Kiev: Naukova dumka, 2013. (In Russian).

Is: ……. locally produced foods, especially edible wild plants and wild mushrooms, which are traditional parts of the regular diet (Orita et al., 2016).

Suggested: ……. locally produced foods, especially edible wild plants and wild mushrooms, which are traditional parts of the regular diet (Orita et al., 2016).

Is: …. radiocesium in each type of mushroom ..
Suggestion: … type? What do you mean? (should be “species of mushroom”)?

Is: …  (p<0.01) and L. scabrum (p<0.01) ……
Proper record is: (p < 0.01) and L. scabrum (p < 0.01) …..

Is: Our study has several limitations. First, we could not evaluate the relationship between
radiocesium concentrations in mushrooms and the concentrations in in the soil. Second, additional analytical uncertainties arose because the committed effective doses from dietary intake of mushrooms cannot measure the day-to-day variations in individuals in Ukraine.
Suggested: Our study has several limitations. First, we could not evaluate the relationship between radiocesium concentrations in mushrooms and the concentrations in in the soil. Second, additional analytical uncertainties arose because the committed effective doses from dietary intake of mushrooms cannot measure the day-to-day variations in individuals in Ukraine. A household treatment can have a high impact on content of metallic elements and radionuclides in cooked mushroom and usually a decrease of activity concentration can be expected (Drewnowska et al. 2017; Steinhauser and Steinhauser, 2016)) but this aspect was not considered in our assessment.
Drewnowska et al.,  2017. Leaching of arsenic and sixteen metallic elements from Amanita fulva mushroom. LWT - Food Sci technol 84:861–866
Steinhauser and Steinhauser, 2016, A simple and rapid method for reducing radiocesium concentrations in wild mushrooms (Cantharellus and Boletus) in the course of cooking. J Food Prot 79:1995–1999

Other remarks:
All results (data) have to be rounded and only two significant figures have to be shown!!!
Not: 583 (27–1,838)
But: 580 (27–1,800)

It also matters as relates to assessed exposure (mSv).
Experimental design: Is Ok.
Validity of the findings: Good
Additional comments: Useful data; can be accepted after some upgrade (also with a recent literature); look into a detail comment


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

Input:
Title: ACTIVITIES CONCENTRATION OF RADIOCESIUM IN WILD MUSHROOM COLLECTED IN UKRAINE 30 YEARS AFTER THE CHERNOBYL POWER PLANT ACCIDENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are many important literature references missing in the text regarding radiocaesium concentration in mushrooms in areas affected by Chernobyl accident. For example, there is no mention to the ban of mushroom collection, and how it affected the internal dose due to their consumption. Raw data are shared. A map showing sampling points is missing.
Experimental design: The analysis of the radiocaesium concentration in mushrooms in Ukraine and how it may be related to those collected after Fukushima accident is an interesting topic. However, there are only data for three species of mushrooms in Ukraine and none for Japan. The authors use raw and dried mushrooms, this is quite confusing, since a dried mushrooms is not cooked. It would be better to express this in terms of fresh and dry mass. It is not clear if the samples were measured dried or not.
Validity of the findings: No comment
Additional comments: The novelty and the importance of the manuscript is very low, as it only gives the mean value of three species of mushrooms from Ukraine. There is no comparison with data from mushrooms collected just after Chernobyl accident. There are many significant references missing. The authors only focused on previous work done mainly by Japanese scientist in that area. In my opinion, this manuscript show only that the authors collected a lot of mushrooms samples and measured them. Therefore my recommendation is rejection.


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: ACTIVITIES CONCENTRATION OF RADIOCESIUM IN WILD MUSHROOM COLLECTED IN UKRAINE 30 YEARS AFTER THE CHERNOBYL POWER PLANT ACCIDENT
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is nicely written, clear and lucid English. Sufficient literature citation. I just mention one more article in line 52, 53 of introduction part. Six references have been cited. The following reference, which is newer than some of the reference cited also strongly advocates your comment in the relevant section. Therefore may be included:

B Mukhopadhyay et al., J. Radioanal. Nucl. Chem. 273 (2007) 415-418.
Experimental design: Research question is well defined, relevant and meaningful. Methods described with sufficient detailing.

According to APS, now year is abbreviated as 'a' (annum), when half life of a radionuclide is described. Please change '30 y' to '30 a' while mentioning half-life of Cs-137.

In line 94 you described the detection limit of 137-Cs 28.5 Bq/kg (as you have calculated from median value). But it must be much less for HPGe detector for 137 Cs. I think you should calculate detection limit of 137-Cs from the background.

You have not mentioned how much dry mushroom was taken for measurement of 137Cs and in what geometry. This is important information for gamma spectrometric measurement.
Validity of the findings: Data is robust, statistically sound and controlled. I would be nice if you
(i) describe any significant physical variation of the mushrooms from contaminated regions and non-contaminate regions taken from anywhere of the world.

(ii) In figure 3 and 4, first data has very high error as calculated by you. Can you opine for this in discussion section.
Additional comments: As mentioned above.


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

Input:
Title: ON REVEALING THE GENE TARGETS OF EBOLA VIRUS MICRORNAS INVOLVED IN THE HUMAN SKIN MICROBIOME
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article has to be rewritten mainly for the language.
The approach is novel yet there are a few important lacunae, the most obvious being how does the work relate to African population where Ebola is prevalent. Are there any studies on the skin biome from African regions where Ebola is Endemic? How often is Ebola transmitted through skin contact?
Experimental design: Use of different strains of the bacteria may further help to expand the study and verify if  microRNAs are indeed important.

Are any other proteins closely associated with the pathological process that could be identified through this approach? For example any other cytokine?
Validity of the findings: The findings look interesting and  a little more detail study explaining why macrophages and not DCs maybe relevant in this case needs to be supported.The skin is home to the Langerhans cells which are mostly  associated with the immune response which the authors have not described in detail.
Additional comments: Please check for grammar and spelling


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: ON REVEALING THE GENE TARGETS OF EBOLA VIRUS MICRORNAS INVOLVED IN THE HUMAN SKIN MICROBIOME
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, the writing is clear. The structure of the paper is complete except that a conclusion or discussion is missing.
Experimental design: The scientific question is novel. More evidence and discussions need to be provided to make a valid conclusion. See below.
Validity of the findings: The experimental data is controlled. However, in Figure 3, the p-value has not enough power for it was calculated using only 3 data points.
Additional comments: This paper discovers short RNA sequences in P. acnes that might act as microRNA to regulate THSD4. It also found that the short RNA sequence PA-mir-2-3p-5 from P. acnes and micro EBV-miR-2-3p from Ebola can synergistically regulate this gene, through which they claim that these short RNA sequences may protect human from evasion of Ebola. The idea of this paper is novel and very interesting. However, I have several major concerns:

1.	Although the short RNA sequence PA-mir-2-3p-5 from P. acnes and microRNA EBV-miR-2-3p from EBOV can synergistically regulate THSD4, the roles of those short RNA sequences in protecting human from evasion of EBOV is not clear. More evidence should be provided to show how P. acnes may prevent EBOV from evasion of the human.

2.	It is not clear that increasing of the expression of the gene THSD4 play an important role in the human immune system. In Figure 3, both PA-mir-2-3p-5 and EBV-miR-2-3p can upregulate the expression of THSD4 mRNA. However, the functionality of P. acnes and EBOV are completely different. Please provide some discussion on the possible functionality of THSD4.

3.	It would be helpful to explain the reason of using P. acnes in this study. Is it possible for other bacteria, rather than P. acnes, to play an important role in preventing EBOV from evasion of human?

Minor comments:

1.	Several grammar errors:

line 83-84, the sentence is composed by two sentences. Thus there
should be a dot in the middle, not a comma

line 123, should be a dot before TargetScan

line 145, should be a comma after 48 hr

line 155, missing subject before “provide"

line 181, that are complementary

line 190, should be “is” not “has”

line 221, should be a comma after "control"

2.	Typos

line 130, nucleotides 2-7

line 109, the font of the capital T is different.

Table 1, last row, Human[40], where is [40] from?

3.  line 91-92. Thus, miRNAs constitute one of the most abundant classes of gene regulatory molecules in animals. The abundance of miRNA in human is not necessarily applied to in other animals. Please provide other evidence to support this statement.


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: ON REVEALING THE GENE TARGETS OF EBOLA VIRUS MICRORNAS INVOLVED IN THE HUMAN SKIN MICROBIOME
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: Transmission is through body fluids or broken skin indicating contact with the blood/lymphatic system.So again the question remains how biome on intact skin are related to Ebola transmission.
Additional comments: The role of Langerhans Cells seems to be vital for transmission of the virus through skin. So how do micrbiomes affect the Mobility of LCs?


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: ON REVEALING THE GENE TARGETS OF EBOLA VIRUS MICRORNAS INVOLVED IN THE HUMAN SKIN MICROBIOME
Review round: 2
Reviewer: 2

Output:
Basic reporting: The conclusion was added at the end of the result section.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: First of all, thank the authors for the revision. The paper is much easier to read now.

The conclusion is still a little confusing that "our findings demonstrated that these P. acnes sequences may act as miRNAs and protect humans from EBOV infection by regulation of the expression of their common target gene THSD4.". The first half of the conclusion is derived based on the results in Figure 2. But the second half of the conclusion is still not supported. By what kind of mechanism that P. acnes prevent EBOV from evasion of the human with the help of THSD4? Since this is the key finding in the paper, please provide rigorous investigation. Otherwise, please limit the statement to supporting results alone.


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: GEO-REFERENCING BIRD-WINDOW COLLISIONS FOR TARGETED MITIGATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: Clear, concise, an accurate professional English used throughout. Except for Nelson (2015) which I may have missed in the text, all other citations are appropriately in text and the Reference section. The figures and supplemental materials are useful, appropriate, and complement the text. Meets all your standards in my view.
Experimental design: Although a rigorous experimental design is not appropriate given the objectives of this study, the authors adequately explain this in detail and provide extensive justification for what was done, how, and the marked value for future studies; fundamentally, providing a means of gathering more efficient and comprehensive quantitative data on incidents of these important conservation events. Ample information and description is provided for replicating and enacting the proposed advancements. Meets all your standards in my view.
Validity of the findings: Introduces and encourages an enhancing data gathering technique to aid current and future work on this subject. Conclusions are generally meaningful, useful, and supported by case study results presented and interpreted. A valuable contribution is the comparison to other online sources (programs - eBird, FLAP Mapper, but why not dBird (?) from New York City Audubon) with similar intents. The authors offer detailed and convincing evidence that their recommended iNaturalist use (methods of data entry) offers the most utility. Meets all your standards in my view.
Additional comments: Compliments for recommending a useful and valuable tool to further study this important conservation issue for birds and people.


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: GEO-REFERENCING BIRD-WINDOW COLLISIONS FOR TARGETED MITIGATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: I feel the manuscript could be tightened up in places, though my criticisms are all quite minor.  They are detailed here.

Presentation of information:

Introduction -

Line 20: I would mention the leading cause of anthropogenic bird mortality and how bird-window collisions compare in terms of number of casualties.

Lines 27-34: I suggest combining the first three paragraphs into two, with the break after “(i.e. ‘greening’)”.  The current paragraph breaks interrupt the narrative.

Lines 34-50: This is useful as a case study but the paragraph overall is difficult to read due to the many internal citations.  How stable are the urls cited here?  Are they all necessary?  Consider paring down this paragraph.

Lines 61-64: This sentence (“The goal of….”) is awkward in context; needs smoothing to better align with previous and following sentences

Methods -

Lines 99-101: You should mention explicitly what led to Duke's decision to retrofit the building.

One glaring omission from the Methods is the survey methodology itself.  When were surveys done?  What time of day?  What was done with the carcasses - were they salvaged and deposited in a museum?  Was any information noted on weather conditions, wind direction, amount/height of vegetation surrounding windows, etc? How exactly was iNaturalist used on the ground during your surveys?

Results -

Lines 155-161: I think this background - specifically, why birds collide with windows, including references dating back to 1946 - should be raised earlier in the paper.  By doing this, the summary of the effectiveness of the retrofit would be more succinct.

Lines 163-165: Reference these percentages to survey years - 2014-2016.

Line 168 - this is important to highlight, that retrofitting can successfully eliminate collisions!  I would add emphasis and broader context to this point.

Minor copy edits:

Line 13 - throughout the paper, you use data as a singular noun.  While technically correct either way, I think your sentences read better when "data" is treated as plural.

Line 39 - the franchise has been, not have been

Line 44 - insert comma after "collisions"; insert "the" after "and"

Line 51 - insert comma after "limited"

Line 57 - see comment on "data" above

Line 66 - smartphone should be one word

Line 110 - "that have been"

Line 112 - cities, not areas

Line 115 - "four-conjoined" should not be hyphenated

Line 124 - delete "building"

Line 132 - delete "is"

Line 163 - insert comma after "Center"

Line 172 - insert comma after "collisions"

Line 177 - delete "a"

Line 184 - see comment on "data" above
Experimental design: No comment (see "Validity of the findings" below)
Validity of the findings: I think this is a great paper that furthers the cause of citizen science initiatives by introducing iNaturalist as a tool to provide useful and replicable data in a specific context.  Although the design of the present study is beset by problems, including small sample size and lack of controls, the authors are well aware of this and state explicitly that their conclusions should be interpreted with this in mind.  To me, the chief contribution of this paper is to highlight the rigor that iNaturalist provides over subjective descriptions of survey locations provided by study participants.  This is something that is badly needed in many citizen science endeavors, and widespread adoption of the methodology presented here will improve the quality and replicability of all studies for which georeferenced localities are an essential component of the dataset.  The study therefore has applicability far beyond documentation of bird-window collisions, and this broader benefit to the scientific community far outweighs any shortcomings in their survey design.  I would add that, based on my own experiences monitoring bird-window collisions, I am quite confident that greater sample sizes would only bolster their conclusions, and that appropriate controls would be difficult or impossible to incorporate into any study on bird-window collisions, considering the practical and legal issues involved with surveying buildings.  The authors have done a commendable job within these constraints.
Additional comments: No additional comments