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: DIVERSITY, SPATIAL DISTRIBUTION AND ACTIVITY OF FUNGI IN FRESHWATER ECOSYSTEMS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Many grammatical errors.
Figures 5 and 6 can be combined.
Experimental design: "Rigorous investigation performed to a high technical & ethical standard" is not met.

"Methods described with sufficient detail & information to replicate." is not met.

See my general comments for details.
Validity of the findings: "Data is robust, statistically sound, & controlled." is not supported.
Additional comments: Lepere et al. provided a neat summary of our knowledge about freshwater fungi by inventorying the 18S rRNA gene in public databases. In addition, they included a small rRNA dataset they generated themselves to evaluate the activity of freshwater fungi. While I think the topic is interesting to a broad audience, there are a few major issues with the manuscript that need to be addressed before it is adequate for publication.

First, the authors should focus their effort on freshwater fungi if they do not intend to make an effort to inventory public database for marine fungal 18S rRNA genes. Currently the authors include a few marine datasets to “compare environments and define spurious OTUs”. While the second purpose is fine, it is not appropriate to compare the complete freshwater dataset with a small fraction of the marine dataset and no meaningful conclusion can be drawn from such a comparison (e.g. lines 382-383). If the authors could provide a comprehensive analysis of the marine 18S rRNA genes in public databases, the profile and the contribution to the field of this article can be significantly enhanced. The manuscript in its current form is taking advantage of a mostly analyzed dataset from an already published study that examined all freshwater microbial eukrayotes (Debroas et al. 2017), and only serves as a “zoom-in” in part of that study.

Second, the authors included a small 18rRNA dataset they generated themselves to evaluate freshwater fungal activity, but very little detail was given on how that was done which precludes readers from interpreting the results properly.

Below are detailed comments.

Line 42: “Fungi” should be lower case.
Line 42: The authors probably want to say “little” as opposed to “a little”.
Line 48: “extend” should be “extent”.
Line 80: In what form were these public data collected? If it’s in the form of raw reads, it’s important to include in Table 1 how many reads are collected from each study.
Line 112: Specify which version of USEARCH was used for analysis.
Line 118: Justify the choice of 95% similarity threshold and discuss its implication for results.
Line 139: Citations should be provided for these two methods.
Lines 163-164: The “probably due to…” part doesn’t belong to the Results section.
Line 164: What is the definition of “reads” here? It seems unlikely that 19,008 OTUs were generated from only 1.6 million raw reads.
Lines 173-176: The implication of these statistics (Figure 2) is inconsistent with the diversity indices (Table 2). According to the diversity indices, Cryptomycota have the highest species richness. However, the OTU-to-reads ratio was actually the lowest for Cryptomycota (17.6% divided by 15%). Please explain this inconsistency.
Line 187: It should be “accounting” instead of “counting”.
Line 204: It should be “most” instead of “more”.
Lines 218-233: It is important to provide context to the sampled 18S rRNA. When were they sampled? What was the sampling procedure? None of such detail was outlined in the method section but they are necessary for interpreting the results properly. Additionally, in the discussion the authors should address whether and how the difference in sequencing platform between their own sequencing effort and previous ones may have an impact on the comparison.
Line 246: “is” should be “are”.
Lines 277-278: Why is this the case? Is this a result of the different life cycles between the chytrids and the dikarya fungi? This observation is interesting and should be looked into in greater details.
Line 288: The sentence needs to be broken down into two.
Lines 334-339: The authors seems to believe that Dikarya fungi previously identified as terrestrial should not contribute to organic matter recycling in freshwater lakes, even though their data suggest otherwise. I think the authors should either provide stronger arguments for their stand, or not jump to the conclusion since there is much conflicting literature on this topic.
Line 362: Why is this FISH image buried in the supplemental material? Is it published somewhere else? I think the authors should move it to the main text, and describe the associated methods.
Line 364: “term” should be “terms”.
Lines 382-383: This statement is unwarranted because the authors did not inventory the marine fungi 18S rRNA gene database.
Figure 5: Why are Basidiomycota and Ascomycota lumped as Dikarya here while they are not in the other figures? Basidiomycota and Ascomycota should be shown as separated groups.
Figure 5 and Figure 6 can easily be integrated into one figure and be more informative.


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: DIVERSITY, SPATIAL DISTRIBUTION AND ACTIVITY OF FUNGI IN FRESHWATER ECOSYSTEMS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have done a good job responding to my comments and I now recommend this manuscript for publication.  Please note however, that some of the newly added citations are missing from the reference list.


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: LOWER ROTATIONAL INERTIA AND LARGER LEG MUSCLES INDICATE MORE RAPID TURNS IN TYRANNOSAURIDS THAN IN OTHER LARGE THEROPODS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In an attempt to stick to the PeerJ reviewer format, I will put my general thoughts and comments on the paper in the final section, but I encourage the authors to read them first, before my more critical comments, which follow below.

My largest comment in terms of basic reporting is that many in-text citations are missing from the bibliography. Here is a list I jotted down, but is likely not comprehensive:

Lu et al 2014
Snively and Russel 2003
Holtz 1995
Peterson et al 2006
Thomas et al 2009
Weiss et al 2010
Snively et al 2013
Mallison et al 2015
Snively 2012
Trinkhaus et al 1991
Allen et al 2010

Of these, three citations are missing from the bibliography that I find a crucial omission, on which the premise of the current study is based. On lines 80-82, it is stated that maneuverability is directly correlated with maximal muscle force in humans. Three studies are cited, none of which are in the bibliography, and briefly searching for them myself I was unable to find them. This is a crucial issue, as this entire study assumes that attachment area is equal to muscle cross sectional area, muscle cross sectional area is proportional to muscle force generation, and muscle force generation is proportional to some metric of agility or maneuverability. I will point out in the experimental design why this is so important. Similarly, the next sentence states that maximal muscle force is straightforward to estimate from fossils as opposed to muscle moment arms, which are difficult. Young et al. 2002 is cited here as evidence of this, but it is missing from the bibliography. Furthermore, I don’t necessarily agree with the statement. I admit that I am not a dinosaur expert, but there are many taxa and/or specific bones for which attachment site morphology is not a good proxy for muscle area or mass (e.g. Williams-Hatala et al., 2016, Scientific Reports; Rabey et al., 2014 Journal of Human Evolution), and similarly muscle moment arms (depending on the muscle) can be estimated from bones alone, and indeed has already been done in some of the taxa investigated here.

One of thing I’d like to point out in terms of basic reporting. The methods and approach used in this paper will likely be of interest to functional morphologists outside of the dinosaur realm, and because of this, I would very strongly encourage the authors to add a figure of the phylogenetic tree of the taxa utilized in this study. Even more helpful would be a phylogenetic tree that also has skeletal outlines that more or less approximate how much material is preserved from each specimen. There is some degree of presumed knowledge of taxa when discussing the methods, and it would be a fairly easy inclusion that would make this paper much easier to read and interpret.

I found that Figure 3 was not a crucially needed figure. In fact, it is only relevant for interpreting the appendix, and I think should not be included as a main figure. At the very least it should not occur before the result figures.

I also found that the methods section was entirely too long (1/2 the total manuscript), and in the experimental design section and general comments section, I have some suggestions for where superfluous information can be reduced.

I have some confusions about the tables and results sections as well. In the results, ranges of body masses are listed that don’t match those in the tables. For instance Arcocanthosaurus was listed as having a range of body mass or 4416-4485 kg, but in table 2, it is listed as 5474.1 and in Table 4 it is listed as 5603. I understand that the authors went through lots of permutations of models, but it needs to be made more explicit which are reported in the tables, and which are reported in the text. The values in the text seem to be lower than those in the table. Furthermore in the table it is unnecessary to report values (especially cm^2) out to 2 significant digits after the decimal. Same with body mass.

I am unsure why the authors chose to use MMI to abbreviate for moment of inertia, considering I is the well accepted abbreviation of this term (and is actually used quite often in the paper).

In the text it is stated that Table 4 gives tail dimensions and cross-sectional areas for the caudofemoralis muscle, but I do not see this in Table 4.
Experimental design: Methods:
The methods section mentions how some outlines were modified based on recent reconstructions, and that for some taxa, there was no dorsal view, so a dorsal view from a close relative was utilized. It would be helpful to know for how many of taxa this was the case. For instance, if only one tyrannosaurid had a dorsal view, and you substituted that dorsal view in for all others, then maybe the signal that was picked up is a methodological issue. Similarly, in the paragraph starting on line 165, it says “if only the skull was available”. I assume this to mean if only a dorsal view of the skull is available, because the specimens that were chosen were supposed to be fairly complete. I think wording here should be changed to make this clearer. But, even so, I would like to know for how many taxa this was an issue, where the entire body plan had to be scaled to the differential between skull measurements. In addition, the following sentence (166-168), implies too much confidence in this method. Not having measurements, and just scaling differences in skull width does not “avoid subjective judgements of widths elsewhere in the body”, it in fact is a process that is a subjective and simplistic judgement of width everywhere else in the body. Furthermore, what does “reconstructs width adequately for MMI comparisons” mean? How do you evaluate this statement, we don’t know what the actual moment of inertia of these animals were, so how can you say that you’ve reconstructed them accurately. This type of language actually pops up quite often (language which implies a degree of confidence in the data that is not there) and I have tried to point some of those instances out.

Reconstructions of the legs:
In the manuscript, it is said that the legs were extended, and the soft tissue outlines were digitized, but how were these soft tissue lines determined or verified? I understand creating a soft tissue outline for the upper body, but for the lower limbs, how was the amount of musculature reconstructed. Furthermore, I understand how an ellipse can then be fitted to the limb in the A/P direction, but how was the minor axis determined in the M/L direction?

I was also initially confused as to the equation for calculating the volume of a frustrum. Eq 1 does not match Fig 1 d, or the equation used by Arbour. I now see that this is a generalized equation that you then simplify to Eq 3, which is utilized. I think the derivation of equation 3 is confusing and unnecessary. Lines 191-204 can essentially be removed without any problem. Just cite Arbour for Eq 3 and move on.

In lines 223-230, it might be worth mentioning that including bone densities would shift the CoM further posteriorly, since it was assumed that the tail and legs were solely muscle density.

The paragraph in lines 238-245: I’m unsure why you have a paragraph dedicated to the comparison of Acrocanthosaurus’ body mass compared to that of Bates, when in the results, you actually compare body masses of several taxa to several other studies. Why is the study of Bates so special as to deserve a whole paragraph dedicated to the fact that you will compare it? However, if a special technique was needed to model the fin then you should put that in the preceding paragraph.

Calculation of center of mass:
In the preceding sections, it was mentioned that the volumes of the legs were calculated in an extended position. In this section, it seems as if the legs are still fully extended (i.e. vertical). Is this true? How did you position the legs when calculating the center of mass of each segment? Were they still vertical, and if not, how did you chose the sagittal plane angles of the lower limbs from which the CoM position would be calculated? This will affect the resultant vertical position of the CoM. It is also unclear from the section starting at line 266 if the legs were included in the body Iy calculation. Is this why the term “axial body” is used?

Agility Metrics:
The follow paragraphs are my biggest methodological concern with the paper:

The authors utilized two metrics of ‘agility’ to test their hypothesis. The first Agilityforce, was used on the basis of the human studies, (which as I pointed out were not in the bibliography, and I was not able to figure out what they actually showed), and as mentioned by the authors in the discussion (lines 593-597) looked at a different system altogether. Also, in lines 336-338, I am totally unable to understand what an agility/force correlation is. Agility is not a set physical quantity in the way that force is. Regardless, the equation for Agilityforce was Agilityforce = Ailium/I(y about the CoM). Since τ(yaw) = I(yaw)*αyaw, and  τ(yaw) = r(from ilium to CoM)*F, and if Force is proportional to Area, then this can all be simplified to Agilityforce =  Ailium/I(y about the CoM)  = αyaw/r (from ilium to CoM). So the measurement of Agility here, is essentially equal to the maximum potential angular acceleration that can be created about the CoM, divided by the lever arm r (from CoM to Ilium), assuming that all the muscles coming off of the ilium are directed perpendicularly to the plane of the ilium. But, this is not how torques which would ‘yaw’ the body would be created. In other words, the body does not rotate about the CoM. Instead, in its simplest case, a standing position, a yaw rotation of the body would occur via lateral/medial rotators of the hip (about the hip). Therefore the most important variables would be the cross sections of the hip rotators, and their lever arm relative to the acetabulum, not relative to the CoM. From this, you could estimate maximum angular acceleration potential (I.E Agilityforce) based on rotations about the hip, not about the CoM. Furthermore, this would be done using the moment of inertia of the body about the hip rather that moment of inertia about the CoM.

The second metric, Agilitymoment is just a more direct way of calculating the torque about the CoM, but without lumping the moment arm into the equation above (i.e. the equation above boiled down to Agilityforce =  r (from ilium to CoM)/ αyaw). In this new equation Agilitymoment = (r*A*20)/Iy. Since the numerator in this equation is equal to Torque about the CoM, and since torque divided by Iy is angular acceleration, this would boil down to Agilitymoment= αyaw, which essential the same as r/Agilityforce. However, the difference between the above equation for Agilitymoment= αyaw, and what was done in the paper, is that r was not directly used in the calculation, instead, a proxy of body mass was used for reasons which I don’t quite understand. The authors had calculated the CoM position in the anteroposterior direction, and assuming these specimens are fairly complete, they could have just calculated the distance between the centroid of the ilium (the resultant muscle force of iliac muscles), and the distance between the CoM. I’m not sure why the cube root of body mass was used instead. While moment arms should scale with the cube root of body mass, you can’t just substitute the cube root of body mass in an equation instead of using a moment arm. In addition, contra to the point 2) on line 354, doing this would still leave you with the allometric effects discussed on line 352. Furthermore, this approach still has the same fundamental issue as the first equation, which is that it assumes that rotations happen about the CoM, and Iy is calculated about the CoM. Rather, the cross sections of the medial and lateral rotators of the hips should be utilized, moment arms of these muscles should be utilized, and Iy of the body about the hip should be utilized.

Finally, in both approaches there is a fundamental issue that ilium area is taken as a direct measure of muscle production. In other words, this assumes that there is a single muscle, with a cross section the size of the ilium, whose fiber emanate directly perpendicular to the plane of the ilium. But, given the discussion of caudofemoralis longus, it is clear that caudofemoralis longus must travel into the tail. In which case, its fibers are not directly perpendicular to the plane of the ilium. So even if the approach taken above were appropriate (calculating torque and angular acceleration about the CoM), these muscle forces must be resolved perpendicular to the moment arm between the CoM and the resultant force vector. Not all iliac muscles which have a force vector perpendicular to the plane of the ilium. Which leads me to the question, does the caudofemoralis act as a femoral rotator in extant animals that have it?

For these reasons, I find the results of this study very difficult to interpret in any physical sense. Im not sure what ‘Agility’ here is telling us. I have a feeling that if one were to just regress iliac are on body mass, the same image that is shown in figure 4 would emerge.

Phylogenetic Methods:
The authors describe the statistical methods from lines 359-459. I think this is overkill. The method section is already necessarily long because of the modeling section. The statistics are not so complicated that they need to be several pages long. The non-phylogenetic methods are discussed first, and then the phylogenetic methods. I would like to think (though I know the older generation of paleontologists may not agree) that we are at a point where we do not have to justify using a phylogenetic method over a non-phylogenetic one. I would advocate that this section be severely reduced in length (lines 359-459). I think its sufficient to state that both OLS and PGLS regressions were performed, phylogenetic signal was detected via Pagel’s lambda, and therefore Phylogenetic ANCOVA’s were used, with perhaps a brief explanation of how they work. I would also caution that in line 373-374 phylogenetic ANCOVAs were mentioned as a way to overcome small sample sizes, which I don’t believe is true. Also, in lines 378-380, I don’t understand how this description is actually different from that of a regular ANCOVA. Both need two separate groups, you could have done the same partitioning of groups that you did in this study in a regular ANCOVA. I would suggest taking this sentence out or re-wording it. Again lines 400-417 can almost all be replaced by a single line about testing for phylogenetic signal. Lines 445-460 simply state that you used family-wise error rates to reduce the threshold for significance.
Validity of the findings: Because of the issues mentioned above, I have a hard time reconciling what the Agility metrics in this paper are actually telling us. What they are not telling us, is what the potential torque or angular acceleration about a hip could be in these dinosaurs. The authors premise the use of agility on these humans studies, but I was unable to locate them because they were not in the bibliography.

Furthermore, while I think the question that the authors are investigating is super interesting, I would have liked to see some discussion about how complicated turning is. I can understand how difficult it would be to calculate these kinds of variables, but in real life, when animals turn at high speeds, the also lean in, which changes the orientation of everything (as the authors pointed out in the intro). How would this affect the interpretations drawn in the current study?

A nit picky comment: In lines 582-583, it is said that the current study “… indicates strong relationships between morphology, agility, and invasion of a distinctive performance nice by tyrannosaurids.” The former two points are valid to say, but the third (invasion of a distinct performance niche), is not indicated by the current study; it is hypothesized on the basis of the results of the current study.
Additional comments: Due to the unfortunately ordered nature of the comment boxes in peerJ, I hope that the authors find this section first, which is that I am a fan of this paper. I think it was really a fun exercise in playing around with a way to model aspects of locomotor performance (i.e. turning performance, maneuverability) that may actually be very important in assessing an animal’s prey capture methods, the type of prey that they might be able to capture, and other aspects of fitness. Furthermore, I think the figures were all very beautiful, and I greatly applaud the use of phylogenetic ANCOVAs utilizing Smaers and Rohlf (2016). I think that method was a perfect way to test the hypotheses that the authors sought to investigate. I sincerely hope that my commentary was helpful, and that the authors find ways to address what I perceived as some of the issues with the study, and that it will ultimately be published. I think that it will be of interest to many fields of paleontology and biomechanics.

Following below is a series of more minor comments and suggestions for changes in wording.

Lines 65-67: Sentence: “Here we quantify biomechanical evidence that …”. This paper is not quantifying biomechanical evidence, this paper is presenting a biomechanical model, which suggests that tyrannosaurids could turn more rapidly, I would suggest rewording this.

Lines 69: Suggest removing “locomotor” and just leaving “muscle force”. Moments about joints don’t care if the muscle function is “locomotor” or anything else.

Line 101: “a proxy for muscle cross section area and force” I would change to “… cross sectional area and maximal force production”

Line 120-121: I’m not sure what the line “Most other taxa were allosaurioids to enforce some phylogenetic consistency for other large theropods” means.  Do you mean that you just need a sufficient number of outgroup taxa to tyrannosaurids?

Lines 123-125: These sentence refer to taxa that were omitted and I think is unnecessary.

The two sentences on lines 140-146 are basically a repeat of one another.

Lines 178-179: I would suggest this edit: …. Tyrannosaurids would lower their relative MMI as compared to the larger forelimbs….

Line 231 : Take out the word “Furthermore”

Lines 234 -235, I would add something like: “…than those previous estimated by the method herein employed for dinosaurs”

Lines 236: Suggest replacing “to obtain the upper end of the range for tail” by “to obtain an upper estimate of”. It could always have been higher in extinct taxa.

Line 248: What does “axial bodies” mean?

Line 294-295: How can you be sure that it’s a good estimation? Change wording to “an estimation”. Also Im not sure if the term CFL was ever defined.

Line 297: Is it a leg, or femoral retractor?

Line 350: I would like to see a citation for the 20 N/cm value.

Line 470 and elsewhere: NURBS is never spelled out.

Lines 486-488: This is an oddly worded sentence and I couldn’t quite get the gist of it.

Lines 531-533 are unnecessary, and it shouldn’t be expected that the R value is the same between the two regressions. The takeaway is it is high in both.

Lines 534-535: I don’t quite understand this sentence.

Lines 536-538: I see one blue dot that does fall within the PI on Figs 5 and 6, which point is this?

Lines 554: Figs 3 and 4 should be 5 and 6.

Lines 557: The method you used isn’t novel, it’s recently published.

Lines 593-596: Again, here is reference to the human study, which is not thoroughly described or in the bibliography.

Lines 617-618. Take this sentence out, the timing of who did what first is irrelevant.

Line 639-640: Is this fact relevant to the current paper?

Lines 641-645: It is good that you tried this multiple ways, and have that data in the appendix. That is where figure 3 should be as well. Furthermore, the final sentence in this paragraph is perplexing. If the simpler method is adequate, why do you only mention it at the end of the discussion?

Lines 651-653: This sentence is an assumption that we all hope is true. I would reword it as such.

Lines 700-702: This is the second time this is mentioned, but isn’t it actually disproven in line 706-707? Unless Dakotaraptor at 374 kg is smaller than a wolf.

Lines 709-710: I applaud the authors for having a very illustrative form of writing, but I have no idea how many kilograms a lion is, or a jackal is, or an African wild dog is. I would say just stick with the previous sentence on the 17-24 x bigger. That I can visualize.

Column z in Table 3 is unnecessary.

In Table 4, I would suggest changing the last three columns to percentages instead of 1.xxx.


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: LOWER ROTATIONAL INERTIA AND LARGER LEG MUSCLES INDICATE MORE RAPID TURNS IN TYRANNOSAURIDS THAN IN OTHER LARGE THEROPODS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Basic Reporting is sound.
Experimental design: The Experimental Design is excellent. My primary concern while reading the body of the manuscript was the potential for sensitivity to body mass distribution estimation and modeling bias in the proportions. Both of these have been well addressed in the appendices through cross-method comparisons and sensitivity analysis. My only comment would be that some mention of these additional results earlier in the manuscript may be warranted, so that readers are not distracted throughout by the worry that these issues have not been addressed (until the end).
Validity of the findings: As with all modeling studies, the validity of the findings pivots entirely on the strength and precision of the initial model. The design is sound, and therefore the confidence in the results is valid. The connection to macroevolutionary trends is speculative, but it is a level of speculation I found quite reasonable (after all, it really is a bit weird that tyrannosaurs have so much of the Late Cretaceous predator ecology to themselves). It would be interesting to consider the potential impacts of pre-existing adaptations in the ancestral state for tyrannosaurs that might have predisposed the clade for exceptional locomotor performance (i.e. is there a phylogenetic reason why tyrannosaurs ended up with a high-agility, high-speed body plan that scaled well to large size?)
Additional comments: My one gripe with the manuscript, which is easily fixed, is the issue of maneuverability vs agility. Technically, the former is typically used in the technical literature to mean minimum radius of turn, while the latter refers to maximum rate of turn. Based upon your parameters, I think the parameter you're really estimating is relative agility, so it makes sense that this is what you mostly use. However, there are places where maneuverability is referenced, instead.

I realize that there are more informal usages for these terms, and that is likely why you use them both. However, I think it is important that both terms are defined early on (even if that means just clearly indicating that you are using them in a general, interchangeable manner). I also think it's worth indicating what components of turning performance your model is likely to estimate (i.e. is your model mostly predicting rate of turn performance, radius of turn performance, or some combination of the two that you don't expect can be separated? - as noted above, I suspect it is mostly rate of turn)

One very minor point (address at your discretion):
“Relative maximal muscle force is straightforward to estimate directly and consistently from fossil evidence, compared to musculoskeletal moment arms that vary with posture, or physiologically variable factors such as muscle power (Young et al. 2002)”

This is true, but the catch is that for measures which intrinsically involve a rate (such as agility - i.e. rate of turn), power is likely a key variable. Of course, maximal relative muscle force will still be a strong predictor in most cases (since physiological muscle differences will only vary so much, especially when comparing animals with similar mass and ecology), and a valid way of dealing with the force vs power problem in the context of turning performance is to use a comparative approach - which is exactly what you’ve done. I do think a brief additional note about this additional advantage of the comparative approach is warranted. This paper will draw a fair bit of interest from readers who are new to biomechanics (because tyrannosaurs), and they might not all recognize the full range of problems you are solving by using a comparative approach with relative metrics.


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: LOWER ROTATIONAL INERTIA AND LARGER LEG MUSCLES INDICATE MORE RAPID TURNS IN TYRANNOSAURIDS THAN IN OTHER LARGE THEROPODS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have made a number of changes which I believe have improved the overall manuscript. In particular, they have added more details about the assumptions of their hypotheses, and added various other methodological details which I find makes the manuscript easier to read and interpret. I appreciate the authors’ diligence to addressing my previous comments! I think this is an interesting study, but there are a number of issues that should still be addressed, which I have no doubt the authors will be capable of addressing. There is one larger issue however, which I detail in the experimental design below.
Experimental design: My larger comment pertains to the underlying assumption/link between muscle force and agility. After consulting the Peterson, Thomas and Weiss papers, I would strongly suggest the authors be a more careful about their wording associating muscle force to agility in humans. The authors are using this as the justification for looking at muscle force (i.e. cross sectional are) as a predictor of agility in dinosaurs. But the cited studies (Peterson et al., 2006; Thomas et al., 2009; Weiss et al., 2010) don’t quite show what the authors claim they show.

All three of these studies are human studies correlating performance on agility tests with either other exercises (squats) or different training regimes. In these contexts it’s not surprising that people that can squat heavier amounts, or train for several weeks, are better at agility tests. But importantly, throughout this manuscript, the authors explicitly make the statements (or variants of the statement): “Muscle force…. is a direct correlate of agility in humans” (Line 40 and elsewhere in the paper). However, none of these studies measure muscle force, nor maximum muscle force, nor any prediction of any muscle forces (despite the somewhat misleading title of Peterson et al., 2006). This statement is not supported by the cited studies.

I see in the authors view the best evidence probably comes from Peterson et al 2006, but this is simply correlating T-test agility scores with 1RM max squat load. While its assumed this is related to muscle mass, Thomas et al., (2009) actually state that the improvements in agility they measured were likely not muscular: “The adaptations to both forms of training are likely to be neural because these predominate in the early stages of strength and power training (29) and have been shown to be the main adaptation to plyometric exercise (15)”. While of course at some level, if agility is correlated with max squat load, and presumably max squat load is going to be dependent on muscle mass, then muscle mass will be correlated with agility. But how much so, and of what muscles? The cited studies don’t address this, but as they are cited by the authors, it gives the sense that they do, even though this is dispelled later in the discussion (lines 734). This tends to permeate in language in other sections as well, such as line 463 (“We developed two indices of relative agility for theropods: Agilityforce based on agility/force correlations in humans (Peterson et al. 2006, Thomas et al. 2009, Weiss et al. 2010)”. But I don’t see how the metric here is in any way related to the cited papers, nor do the cited papers show that muscle force is correlated with agility (again because they did not measure or estimate muscle force). I think this kind of language gives a false sense of confidence about the relationship between muscle mass and agility that is not supported with the citations included. Now, I do not criticize the authors for developing their own metric, nor do I think this obviates the point of the paper; I do think though that the authors should more clearly delineate what the cited studies actual show, and how they are using some of these assumed relationships as a springboard to develop their own metrics, that hopefully tell us something about turning ability.

As a final thought on this topic, in this manuscript, agility is used as an indicator of turning performance; in Peterson et al., (2006), they measure agility as a T-test, which actually doesn’t involve any turns.

I would strongly encourage that the authors remove or edit the sentence “Relative (not absolute) maximal muscle force is straightforward to estimate directly and consistently from fossil evidence, compared to musculoskeletal moment arms that vary continuously with posture in three dimensions, or physiologically variable factors such as muscle power (Young et al. 2002).” First of all, I don’t think that this is true. Yes, moment arms vary with posture, but muscle force is still harder. You need PCSA, which in and of itself involves fiber length, muscle volume, and pennation angle, and only one of these (muscle volume), can be approximated in a straightforward way from a fossil. Furthermore they change with age and health and other factors. I also don’t quite understand the second qualm about muscle power, nor does Young (2002) seem to have anything to do with muscle moment arms. I understand the logic behind wanting to use muscle cross sectional area for the current study; I don’t think it is necessarily to criticize muscle moment arms (criticism with which I don’t agree) in order to get that point across. If muscle force is straightforward and easy to measure in therapods, then great, I think its sufficient to leave it at that.
Validity of the findings: I would take an additional look at the PGLS/ANCOVA results that you show in Fig. 4–5. PGLS sometimes makes the regression lines look weird when plotted on the raw data, but it seems a bit weird that for the ‘Therapod’ line, all but one point is above the regression. I know I’ve played with datasets where the slope looks funky when plotting the PGLS line on the raw data, but I haven’t seen one where nearly all the points have one-sided residuals. I would just double check this. Similarly, I’m not sure what the statement on lines 664–666 means about ‘under-predicting’ agility.
Additional comments: One burning question I still have stems from the introduction; that tyrannosaurids have “tall ilia for leg muscle attachment”. If you were to create two separate plots similar to Fig 3, for both Ilium Area, and Iy separately, do they both show the same trend, or is this all just a matter of pelvis size?

I know I mentioned this in my first review, and the authors have added a line in the paper, but you are using two abbreviations for moment of inertia (MMI and I). Mass moment of inertia is commonly abbreviated I, and it distracting to have two different abbreviations for the same thing in one paper. Either use I, or MMI, but don’t switch back and forth.

Line 111: Divided ilium area by what?

Line 151: Is the COM set to be directly above the foot? Assuming that this was during locomotion, the COM during single stance would probably be medial to the stance leg. Just something to think about, though I doubt it would affect the results.

Line 311: Though they are technically results, it might help to have the inter-observer error results (or %’s) at the end of the paragraph on line 311, so we don’t have to be in suspense!

Line 398–404: I’m not sure what these examples provide; they are stuck in a section describing the accuracy with which muscle scars preserve actual muscle size, but neither of the examples seem to directly address this. Perhaps re-word or remove this section.

Lines 474–484: There are a few things that could be done to make the units more consistent. In Equation 13, is Iy measured in kg*m2? And if so are you mixing cm and m measurements? Similarly in equation 14 are cm and m units being mixed?

I would move the subsection “Statistical comparison of group differences: phylogenetic ANCOVA” to after the section “Determining strength of phylogenetic signal and appropriateness of phylogenetic regression”, or combine it with the section “Phylogenetically informed analyses”.

Check for consistency in the numbers of significant digits in the tables and throughout the text.

Line 711: “uniquely superior” is a pretty subjective statement that don’t really mean anything. Can you be more specific?

Lines 715–717: I would suggest changing this sentence. It is a bit of a stretch to claim that you found a strong relationship between something and “distinct performance capacity by tyrannosaurids”. You are inferring a performance difference given a metric you’ve created that you believe to be informative.

The discussion would be a good place to further expand on what specific is driving the difference in ‘agility’. Is it all Ilium area, or a bunch of factors?

Minor comments:

Line 78: Perhaps after the line ending “…(=rotational inertia).”, preface the sentence that you are about to talk about turning strategies aside from simply increase torque.

Line 87–88: “When limbs are planted on the ground, the body can pivot with locomotor muscle alone”. I’m not entirely sure what this sentence is trying to say; is it separating the situation of both legs planted on the ground? Also, I would suggest changing ‘locomotor muscle’ to ‘muscle force’.

Check the number of significant digits in tables and text for consistency.


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: LOWER ROTATIONAL INERTIA AND LARGER LEG MUSCLES INDICATE MORE RAPID TURNS IN TYRANNOSAURIDS THAN IN OTHER LARGE THEROPODS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comments
Additional comments: I have (finally) read through the new version of the manuscript in detail. All of my prior concerns were handled, and I note that significant improvements were made in response to the comments of the second reviewer (who caught some potential issues that I missed and/or was less concerned by). I did not find any errors or new problems introduced by these additions and revisions. I note that additional equations and tables were now required to explain the new analyses. These are warranted and necessary in the new version. I also wish to apologize to the authors for the delay in my review. You deserve to know that it was my review that held this up, and the delays had nothing to do with the quality of the manuscript or my interest in the 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: COMPARATIVE STUDY ON THE COMPOSITION OF FOUR DIFFERENT VARIETIES OF GARLIC
Review round: 1
Reviewer: 1

Output:
Basic reporting: Methods of comparison of samples are acceptable, with some details needs to be improved, such as using standards for identification compounds ore quantification of concentration of peaks.

Language is understandable

Format of Tables are ok, Raw are acceptable.

For conclusion of this article, results form only one batch samples are too weak.  More data needs to be compared for samples from different resource (such as different growing area, different harvest season or storage condition samples....
Experimental design: Line from 84-90
Q: Why using 80% of ethanol for extraction of soluble sugar from garlic mashed tissue?  Does this have reference of the method?  My understanding of "soluble sugar" in plant is water soluble sugar.

Figure 2
Q: Suggest giving evidences of the m/z trial (mass spectrum) for each of the 7 identified peaks.
Validity of the findings: Line 173-184
Q: Identification of these compounds from GC-MS was based only from Nist library need more support evidences. Such as standards for the 7 key chemicals listed in the article . For quantification,  internal standard or external standard (standard curve) should be required

Table 2
Q:  Suggest using retention index for peak identification, rather than retention time.
Additional comments: For comparing difference of contents in biological samples, ripening stage, harvest time, storage time and temperature, growing area, soil pH et al…. are all the factors influenced in the testing results and needs to be considered.  This article compared only one batch each of samples from supermarket .  More experiments or evidences for different conditions or treatments of garlic samples are suggested to be compared for supporting the conclusion.

Suggestion: data from more batches of samples from different growing areas for each variety, or freshly harvest samples from similar storage conditions (similar storage time, temperature, et al) are supportable for this.


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: COMPARATIVE STUDY ON THE COMPOSITION OF FOUR DIFFERENT VARIETIES OF GARLIC
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper explores difference of nutrients, compounds composition, antimicrobial and antitumor activity among four varieties of garlic. The authors claim to find that there are many distinctive differences between “Hongqixing” and “Ershuizao”, which are unique to Sichuan Province of China.
Experimental design: no comment
Validity of the findings: This is quite significant discovery and may improve the cultivation of garlic.
Additional comments: However, some slight points are missing in the manuscript, which are very important for a publication.
1.	The author mentioned that “the garlic juices were mixed with deionized water at pH=3.0 at a ratio of 1.2 g/mL” in 2.5. It is not specific enough. The author should supplement the detailed conditions such as time and temperature.
2.	Why did the author choose the two tumor cell lines SW480 and HCT116 to verify the antitumor activity of the extracts? A valid explanation should be given.
3.	The author only tested the membrane permeability and leakage of protein in X. campestris pv. malvacearum. How about other microorganisms?
4.	Why did the author choose deionized water at pH=3 to extract the garlic juices?
5.	However, pH itself might influence the growth of microorganism. Therefore, the author should test the water control with pH=3.
6.	Previous researches reported higher levels of sulphide components in garlic by GC-MS. Why is the content of sulphide components lower in this paper?


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

Input:
Title: COMPARATIVE STUDY ON THE COMPOSITION OF FOUR DIFFERENT VARIETIES OF GARLIC
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I enjoyed reading the new version of the manuscript, which has addressed my concerned.
Therefore,  I have no further comments to add.


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: SEASONAL VARIATIONS OF THE ICHTHYOPLANKTON ASSEMBLAGE IN THE YANGTZE ESTUARY AND ITS RELATIONSHIP WITH ENVIRONMENTAL FACTORS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript analyzed seasonal variations of the ichthyoplankton and the relationship between the community and the environmental factors. The results are interesting and material and method were reasonable for the present study. However, the English writing and grammar should be modified by a native English speaker. It would have been interesting to compare in detail previous work and previous studies in detail, to see if there were long term trends and so on. This should be done using clear tables and figures comparing present and past data. The results did not state the exact relationship between ichthyoplankton community and environmental factors.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: SEASONAL VARIATIONS OF THE ICHTHYOPLANKTON ASSEMBLAGE IN THE YANGTZE ESTUARY AND ITS RELATIONSHIP WITH ENVIRONMENTAL FACTORS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article needs to be edited by a native English speaker.
More literature references should be added to explain why you develop the research and to discuss the different rusults with the prior literature.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: The manuscript is well and clearly written and provide comprehensive results. I have provided one major concern and several minor comments. I hope my comments improve this manuscript.
     In addition, because I am not a native English speaker, I cannot any comments about English grammar. But I recommend authors ask a native English speaker to confirm English of this manuscript.

Line 23-26, the sentence was not closely connected with the last sentence. Maybe can change to "And historical data was also collected to compared with ...".
Line 34, the authors told about "abundant", but I can't find the data.
Line 38-39,  "...affecting the ichthyoplankton in 2012" , affect ichthyoplankto what? it's not complete.
Line 40-42, "Compared with previous ,,, a great change", how is the change, or the sentence is meaningless.
Line 52, Insert "but or however"
Line 59, add a close sentence, like "So it's necessary to ...."
Line 60-61, the sentence is not natural, it's not usually to say "the major study", you can change to "It has been widely reported..."
Line 61, after "marine ecology", please add the references.
Line 65, "however, the recent researches was lacking" you can't say like this, and it's not the necessary reason to research.
Line 67, "characterized"?
Line 68, "analyze the relationship between,,," the purpose of the research is not to analyze the relationship, it's to find the main environmental factors through the relationship analysis. please rewrite the sentence.
Line 79-81, since you have Fig 2, how do you calculate the abundance, please add the formula.
Line 81-84, how do you measure the data? please add the equipment or methods
Line 98, how do you calculate IRI, can't find the formula.
Line 117, the structure of the results is too complicated, please simplify and be clear. maybe 3 or 4 parts as composition, diversity, spatial and temporal variation and CCA analysis.
Line 120, "the results indicated,,," you can't use indicate here, change to another word.
Lien 121, "Abundance and biomass" where is the biomass? how do you calculate? Since the authors said abundance, but I can't find a data in the results, I advise to add some important data.
Line 123-124, "4 taxa" it's not clear, rewrite the sentence.
Line 148, change "," to "."
Line 151-152, "...up to 7 species....of the total species..." too complicated, and not clear, rewrite.
Line 183-184, "After the calculation,,, among four seasons.", delete.
Line 185-186, "The statistical ,,, not significant", delete.
Line 194, "significant difference." add F, p
Line 202, "structuring" change to another word, is not proper use.
Line 204-205, "...displayed a higher correlation with axes 2 than axes 1", how do you know? add the data please.
Line 230, "In past researches", delete, and change to in the last decades; "studied" changed to "reported"
Line 231, add the references after "...environmental factors".
Line 234-236, "Zhang et al. (2015, 2016),,,environmental factors" the sentence here is not closely connected with the text.
Line 245, "salinity" is the main factor, but in the research, Chla has the significant effects. As seen in Line 305, "... was not salinity but Chla...", Please discuss it further.
Line 318, the conclusion should be rewritten. It is similar to the abstract, but not. It should have some data in it.
Delete "In the summary"
Line 320, "quantity" ? please check
Line 323-326, "With the rapid development,,,, Yangtze estuary" Sine the research did not have data about the fishing intensity, you can't say. And the results said Chla is the main effecting factor, the data was related to industrialization and urbanization.
Table 4, many useless data. Would you please give a table about the summary statistics for the first two axes? such as percentage, cum percentage, cum constr. percentage for variation.,,,,


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: SEASONAL VARIATIONS OF THE ICHTHYOPLANKTON ASSEMBLAGE IN THE YANGTZE ESTUARY AND ITS RELATIONSHIP WITH ENVIRONMENTAL FACTORS
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1.	Basic report: This paper reports the results of ichthyoplankton collections in the four seasons in the Yangtze Estuary and found that the ichthyoplankton assemblage was different among the seasons. An important finding of this paper by comparing the results with the previous studies in the Estuary, is the recent changes in ichthyoplankton abundance and composition in the study area, which seemed to be associated with the decline of freshwater runoff from Yangtze River.
Experimental design: 2.	Experimental design: Ichthyoplankton samplings were conducted in 4 seasons, in May, August, November, and February at the 40 sampling stations including river mouth and estuarine areas, which has sufficient coverage in terms of area and season. The trawl net was towed on the surface waters and therefore mostly collected pelagic eggs and larvae. If the net was towed obliquely from the near-bottom layer to the surface, the authors obtained different results in abundance and in species diversity. When we talk about fisheries resources, demersal fish species are also important. So in the next step, the author better attempt collections of demersal fish eggs and larvae.
Validity of the findings: 3.	Validity of the findings: The findings of this paper are limited to the year 2012. But by comparing the results of the previous papers, this paper showed an important change in ichthyoplankton abundance and composition in the Yangtze Estuary in recent years.
Additional comments: 4.	General comments: This paper is worth publishing in PeerJ after revising some points listed below.

The following points need to be reconsidered and revised if necessary.
1.	“the Yangtze estuary” better be written “the Yangtze Estuary”, like Yangtze River.
2.	Any difference between “ichthyoplankton community” and “ichthyoplankton assemblage”? In general, “community” has a structure like a kind of society but “assemblage” is only a simple gathering of animals. In this paper, description of abundance and composition of eggs and larvae collected by the trawl net seems to be in numbers and kinds of ichthyoplankton and nothing to do with the ecological relationship among the species. So the author better use “assemblage” rather than “community”.
3.	“Research voyages” better be written “research cruises”.
4.	No definite article to Latin names of animals.
5.	Usually a definite article is not applied to season
6.	Difference in ecotype is based on different habitats rather than ecological habit.
7.	Line 121: biomass of Perciformes, need to show in table 1 which families belong to the order Perciformes.
8.	Line 123: Should “4 taxa” be written as “4 ecotypes”?
9.	Line 133: “for breeding and development” better be written as “for reproduction and development”.
10.	Line 143: backish be corrected brackish. Similar in many of this word.
11.	Line 150: E. japonicas be written as E. japonicus . Similar in many of this Latin name. Be careful with that the word processor automatically misspell this name from japonicus to japonicas.
12.	Line 166: “in dominance degree of dominant species” be written as “the degree of dominance”.
13.	Line 236: “species construction” may be written as “species composition”.
14.	First paragraph of the Discussion: Are the authors mentioning that salinity in 2012 was higher than before due to decreased runoff of freshwater from the Yangtze River? If so, the author need to show salinity data in 2012 and in the previous years.
15.	Line 280: “reproductive period” better be written as “reproductive season” or “spawning season”.
16.	Line 287: “grown fish” is to be written as “adult fish”.
17.	References: Abbreviations of author names and style of cited paper descriptions are to be uniform.
18.	Table 1: Title of the table be “Presence (+)of species in ichthyoplankton samples in 2012.  Scombrida be written as Scombridae. Hemirhamphus sajori be written as Hemiramphus sajori.
19.	Table 3:  footnote be written as “numbers with different superscript are significantly different each other”.
20.	Figure 2: Sampling stations with no ichthyoplankton collection (0) need to be located by (x).


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: SEASONAL VARIATIONS OF THE ICHTHYOPLANKTON ASSEMBLAGE IN THE YANGTZE ESTUARY AND ITS RELATIONSHIP WITH ENVIRONMENTAL FACTORS
Review round: 1
Reviewer: 4

Output:
Basic reporting: In this manuscript, the language is very clear. Comprehensive and sufficient references were cited in this manuscript and describe background of this study very well. The structure of this manuscript and content of tables and figures are fine, which meet the criterion of Journal. The authors supplied the raw data, which also reach the requirement of Journal. The results finding are well described.
Experimental design: The experimental design section met the requirement of Journal. However, the question for the research field is not clear. There is no recent research to discuss the ichthyoplankton community structure since 2012. The survey method was followed the Specification of Oceanographic Investigation. The details of data analysis were well described, which can be easily repeated.
Validity of the findings: Because of suitable survey method and appropriate data treatment, the result is robust and reliable. The conclusion is well stated and respond to the question cited in the introduction section.
Additional comments: Although advantage in the manuscript, there are some points needed to improve before the publication
1.	In the introduction section, you cited the several references about the characteristics of ichthyoplankton community structure in the past. Please give major findings for the cited references especially references Liu et al, 2008; Wei et al, 2012.
2.	In the discussion section, different years species construction of ichthyoplankton  assemblages were compared, which showed a descending trend. The decline of ichthyoplankton species may relate the adult fish species variation. Please compare the adult fish assemblages of different years to support the variation in ichthyoplankton assemblages.


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: SEASONAL VARIATIONS OF THE ICHTHYOPLANKTON ASSEMBLAGE IN THE YANGTZE ESTUARY AND ITS RELATIONSHIP WITH ENVIRONMENTAL FACTORS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised Ms has been revised according to the suggestions. But the figs need a few changes.
Fig1, the map of  China is lack of the South China Sea.
Fig5 is not professial, the labels and captal, please revise.
Experimental design: It's no problems.
Validity of the findings: It's no problems.
Additional comments: I accept the revised MS with minor changes.
Fig1, the map of  China is lack of the South China Sea.
Fig5 is not professial, the labels and captal, please revise.


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: DUAL MECHANISM OF TRKB ACTIVATION BY ANANDAMIDE THROUGH CB1 AND TRPV1 RECEPTORS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Language is OK.
Literature cited does not cover early work on TRPV1, or the well conducted studies that show expression of the TRPV1 is low or absent in most brain areas. There is a bit of a disconnect between differnt studies of TRPV1 expression in brain, and given the to inherent problems of just using antibodies to define protein expression, this should be acknowledged, with not just mention of supportive studies.
Figures are OK.
Experimental design: Yes.
Yes, although the "knowledge gap" is invented, not real, and given all the data is obtained by adding drugs, everything may simply be a consequence of adding drugs, not a reflection of the underlying biological reality that normally operates.
Please see below for shortcomings (only the immuno really fails).
Probably.
Validity of the findings: OK
Additional comments: This paper explores the effects of the endocannabinoid anandamide on the activation of TRK receptors in cultures of embryonic rat cortical neurons, and then attempts to use the results to interpret the effects of administration of cannabinoid and vanilloid agonists on mouse behaviour in vivo.

The key in vitro experiments consist of anandamide and capsaicin concentration response curves for promotion of the phosphorylation of TRK. The curves are incomplete, with the investigators not testing concentrations of drug above the first 1 or 2 that produce any increase in pTRK. The CRC in response to BDNF indicate that it is highly unlikely that either drug has reached anywhere near its EC50 or maximum, which means that only a fraction of the possible effect is being tested. The authors show that a CB1 antagonist blocks the effects of 100 nM AEA, implying a CB1-dependent mechanism, but they do not test the effects of the drug against 200 nM AEA, to see whether CB1 is involved in the residual response in the presence of capsazepine. The authors should also make it clear what concentration of capsazepine was used – sometimes it is written as 20 nM (probably too low be believably effective), sometimes it is written as 20 µM (probably too high to be selective). More selective ligands for CB1 and TRPV1 are available, it would re-assuring to see that they mimicked or blocked the CB1- or TRPV1-dependent effects as expected. The authors should also comment as to why they chose AEA as their endocannabinoid – in the brain the major cannabinoid transmitter is probably 2-AG, which has higher CB-receptor efficacy that AEA, and is generally found at much higher levels.

The experiments illustrated in Figure 2F are meaningless without knowing whether pTRKB levels are correlated with those of BDNF without any drug treatment, or after antagonist treatment (with either and both TRPV1 and CB1 antagonists).

The in vivo experiments utilize single concentrations of agonist (with no indication of where they lie on dose effect curves), this makes it it is hard to interpret them.  It would be nice to know at minimum whether K252a blocked the effects of BDNF, whether local WIN55212 mimicked the effects of ACEA (why not AEA ?), and whether any of the agonist effects were blocked by selective antagonists. The authors may have simply chosen (or found through trial and error) doses that would give them the results that tell a story.

The immunohistochemistry “experiments” do not add much to paper. Without some sort quantification they are meaningless, without markers of glutamatergic or GABAergic neurons they cannot really support the hypothesis in Figure 6. It would also be helpful to know whether the (degree of) co-localization apparently seen in brain is also found in culture. Some comment as to why both TRPV1 and TRKB appear to largely intracellular (and diffuse) would also be useful.

No mechanism underlying the effects of the drugs are tested, no possibility that there could be synergy (or interference) between the 2 pathways tested, we don’t even know whether cell to cell communication us required for the effects in vitro.

There are a number of technical issues in the Ms. Controls for the specificity of the Ab should be included, details of how areas were chosen for immunohistochemistry and information about experimental blinding should be included. The paper lacks details about how some animals were euthanased – i.e. the mothers of the embryos, the animals that were used in the behavioural experiments. Details of post-surgical care and monitoring and the criteria for withdrawing animals from experiments should also be given.

The Results section is not written particularly clearly, the authors start with statistical statements rather than a brief description of the experiment and the result, and this comes across as stilted. Stats support science, they are essential, but should not lead description of the 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: DUAL MECHANISM OF TRKB ACTIVATION BY ANANDAMIDE THROUGH CB1 AND TRPV1 RECEPTORS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The present study aims to unravel the dual effects of endocannabinoids on CB1 and TRPV1 receptors through TRKB receptors phosphorylation and link this activity to behaviour. This is done both in cell culture from rat embryo cortex and in vivo. The overall approaches used are sound, and the conclusion of interest. The report is well written (though some errors in the text remain and should be fixed), and easy to follow.

The study capitalises on a dual, explained almost as opposite, effects of endocannabinoids depending on concentration via action through CB1 or TRPV1 receptors. If this happens to be true, it is of interest. Some clarifications are needed for the validity of the finding to be properly assessed.

Introduction:

1.	The description of the signalling pathways related to endocannabinoid via CB1 is weak and needs to be expanded. Gi/o is one of several possible mechanisms. Others include Gq and Gs. Gq is of importance here, as they cause, as for TRPV1 channels, an increase in calcium. Some agonists, such as N-arachidonoyl-dopamine, for example, are not only Gq-specific, but also a relatively potent ligand for TRPV1. Anandamide can also increase calcium through the RE via Gq.

2.	There appears to be some confusion regarding a bell-shaped effect of endocannabinoids and TRPV1, which should be better described, as two main concepts are mixed together, the first one being basic pharmacology, the second being behavioural outcome. From a pharmacology standpoint, an increase in the concentration of eCBs is not going to favour TRPV1 over CB1. An increase in eCB concentration will reach maximal efficacy on CB1 as well as start activating TRPV1 receptors (as eCBs possess a lower affinity for the channel). Furthermore, most of these effects are going to take place in different cells.

3.	It is not clear from reading this introduction what mechanism exactly links TRKB to CB1 and TRPV1, in fact there is no mention of TRKB to TRPV1 whatsoever. Is this interaction already known or part of the results of the current study? This is of great importance as not only is this paper stating that they are part of the same type of signalling mechanisms, but the authors claim that there is protein-protein interaction as confirmed from co-immunoprecipitation. The localization (pre-post synaptic) of these receptors need to be better determined as well.

Methods:

1.	In experimental design, line 211, “dose-response effects…”should be “concentration-response effects”. Please fix other mentions of in vitro work as dose-response throughout the paper.

2.	Line 218-220: the 2 sentences are confusing. First one is AM251 followed by AEA. Second one is AM251 but NOT followed by BDNF? Please rephrase.

3.	Overall please use µ instead of u. It could be good to use inverse agonist rather than antagonist as it is a more proper pharmacology term.

4.	The concentration/doses for local drug administration are very low overall. Most are below the known concentration for displacement of radio-ligand in cell-culture based assays. It would be judicious to comment on the reason for the choice of concentration.

5.	The reason why this study mostly focuses on endocannabinoids, but then use synthetic ones for the burying test needs to be assessed.

 Discussion:

1.	Line 347 forward: I am not certain I understand how this can be claimed. In figure 1a/b, AEA causes higher increase of pTRK compared to capsaicin. AEA is a very weak agonist to TRPV1 at best compared to capsaicin. This does not make much sense as far as pharmacology is concerned. There is nowhere in this paper where there is a clear result showing that “even if AEA has a higher affinity for CB1 than for TRPV1, the related efficacy appears to be inverted in favour of TRPV1”. I do not see this shown in this study. If anything, it looks like activity on CB1 and TRPV1 are different, and via different mechanisms as CB1 activity does not cause an increase in BDNF.

2.     The in vitro work is done is cell culture. The in vivo behavioural work is done acutely. This is a major distinction as endocannabinoids are involved in neural development. This needs to be properly discussed.

Figures:

The images and figures need a serious rework. Harmonisation of fonts, as well as higher quality of images are required. In its current state, they do not look ready for publication.
Experimental design: The overall experimental design is of interest, and original. The research questions are well defined and relevant, though they might be based on somewhat weak foundation (the bell shape effect of endocannabinoids on CB1 vs TRPV1). The technical level is overall good, though the immunohistochemistry images are not currently convincing.

1. Is the burying done in a clean box? This is a major stressor for mice and could be important for marble burying behaviour, especially when injecting cannabinoids which could further induce anxiety-like behaviours.

2. If high doses of endocannabinoids, as hypothesized, act through TRPV1, then one would think that high concentration of endocannabinoids would increase burying behaviour, especially when localised injections are involved (rather than systemic). Why was this not tested?

3. As mentioned previously, overall concentration used for endocannabinoids are low, and concentration response curve for pTRK levels incomplete. Please explain if higher concentrations were also tested.

4. Why were synthetic cannabinoids used for the burying test rather than endocannabinoids?

5. It would be good to provide lower magnification of the slices to have an overall idea of the PFC structure. Layer information would also be relevant.
Validity of the findings: Data is mostly robust, though some confirmations are needed for this manuscript to be accepted.

1.	Result from 1d does not look like a very convincing coIP. This is not helped by the omission of any statistical analysis, or sample size.

2.	If one does not look at the scale of the y-axis in 1a/b, one might be inclined to think that the effect of AEA and CPS on pTRK levels are very similar. % change from baseline should be mentioned in the text. AEA causes higher pTRK compared to capsaicin, yet one of the basis of this study is that AEA, a weak TRPV1 agonist, causes increased burying at higher doses. This should be discussed more properly, as it is a foundation of the paper. As well, none of the concentration response curve are complete. Were higher concentration tested?

3.	For 2a, did AM251 decrease basal pTRK levels? This is important to point out as it could hint at tonic activity.

4.	I can see from the provided Prism data that AEA was conducted for the burying test, but it was omitted from this report. This is quite surprising as this is an endocannabinoid paper. Justification for this choice is essential.

5.	I can also see from the Prism data that the two only excluded datapoints from the burying data are 2 zeros from the ACEA + 252a group. If these were included, there would be no significant rescue. If anything, the 9 marbles buried from this group is in fact the outlier. Justification for this omission is primordial for this study to be published. Same goes for the 9 marbles as possible outlier for the CPS + 252a group.

6.	For the immunohistochemistry images, it is not too clear what the white arrows are pointing at. Background levels are quite high for CaMK2. Were blocking peptides used as control? There is a lot of TRPV1 staining in the soma rather than the cell surface, which is not what one would expect from the literature. If this is PFC slices, please provide lower magnification for an overview of the structure as a whole. Better controls are required to assess the validity of the immunohistochemistry overall.

7.	Best practice for the use of colours for immunohistochemistry should be used. Arrows are not clearly showing what they should. Colour scheme makes colocalization dubious. Green/red is particularly to be avoided for colour-blind people.

8.	The schematic states that CB1 is on GABAergic neurons but this claim is not-substantiated in any way in this manuscript.. Is this to be taken from the literature? CB1 are on both excitatory and inhibitory neurons. Neighbour cells is also very vague term.
Additional comments: It is of great importance to explain why two values were omitted from the burying test for ACEA + 252a group.  The CP+k252a group is not too convincing either as the 9 marbles buried for one animal could potentially be an outlier. This is of great importance for the overall conclusion and validity of this study.


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: CHARACTERIZATION OF THE COMPLETE CHLOROPLAST GENOMES OF FIVE POPULUS SPECIES FROM THE WESTERN SICHUAN PLATEAU, SOUTHWEST CHINA: COMPARATIVE AND PHYLOGENETIC ANALYSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: English in the reviewed manuscript is good, however there are some parts of the text which needs revision/clarification (e.g. L. 90, L. 247, L. 311-313, L.319-320, L.321-322)

I have noticed two mistakes in reference citation in L. 345 – there is no such position in reference list like Zheng 2016 and Wang 2016, there should be Zheng et al. 2016 and Weng et al. 2016, respectively. I recommend more exhaustive reference check.

The article is well structured. Tables and figures should be self-explanatory therefore I recommend to explain the meaning of abbreviations used in the caption of Figure 8 and within Table 5 and Table S3.  Moreover, the caption of TableS4 should be improved - Synonymous (Ks) and nonsynonymous (Ka) substitution rate analysis of the five species, with P. xiangchengensis as the reference.

None of the reported cp genomes is accessible (yet) in GenBank (NCBI).
Experimental design: The reviewed paper reports the results of chloroplast genome sequencing of Populus species (P. cathayana, P. kangdingensis, P. pseudoglauca, P. schneideri and P. xiangchengensis). Complete chloroplast genome sequences were characterized and used for comparative and evolutionary studies. Based on the obtained molecular data authors propose the candidate chloroplast sequences suitable for further population genetic and phylogeographic studies. The presented chloroplast genomes help to resolve the phylogenetic relationships among Populus species

Objectives of the paper are clear and unambiguous. The methodology is correct and suitable for realization of the paper objectives. The results description is adequate and conclusions are generally well supported. Some additional minor flaws are marked within the manuscript or are addressed below.

Why did authors decide to perform the phylogenetic analyses based on the complete cp genomes instead of coding sequences only, although according to their statement (L.376-377): “…caution is necessary when using cp noncoding sequences for phylogenetic analysis.”?

How did the authors choose the model used for phylogenetic analyses in RAxML? Have you tested also other models for your data?
Validity of the findings: The reviewed paper is an example of an interesting and valuable study with well-planned and extensive but complementary methodological side, as well as clearly delineated objectives of the work. The described results perfectly correspond and are complementary to previous studies on history, evolution, and diversity of Populus. The applied methodology, high-throughput sequencing, provide a high-quality data with a number of applications. Here, authors not only report complete chloroplast genomes for five Populus species but also based on the molecular data revised the systematics of the genus. The observations included in the reviewed manuscript may become a valuable element of the discussion not only in case of studies on evolution and diversity of Populus but also for other closely related taxons.
Additional comments: The reviewed manuscript represents an interesting and valuable study which should be considered for publication in PeerJ but after minor revisions


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

Input:
Title: CHARACTERIZATION OF THE COMPLETE CHLOROPLAST GENOMES OF FIVE POPULUS SPECIES FROM THE WESTERN SICHUAN PLATEAU, SOUTHWEST CHINA: COMPARATIVE AND PHYLOGENETIC ANALYSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors report the findings of a study to characterize and compare five Populus plastomes, of which four are reported here first. The article covers the relevant background to evaluate the findings. I found the article interesting and timely. I suggest a restructuring of the paper so that the reason for the study, a phylogenetic assessment of the study species, could be emphasised. It is only stated clearly in the second to last paragraph of the discussion in lines 382-384. I believe reporting the findings from phylogenetic relationships to structure/characterization of the plastomes would provide a clearer narrative for the paper. This would also increase the relevance of the findings. Moreover, the characteristic of the genomes are more interesting in light of the relationship of the species.
The paper generally needs some restructuring as parts of the results should be in methods or discussion (see detailed comments below.). The figures are well designed, but see comments below for a few possible improvements.
Experimental design: The study fits well in PeerJ’s scope and the experimental design is suitable to answer the main question of the study. I could not find any evidence that the assembled plastomes are/will be submitted to GenBank. You could include the GenBank numbers (or a placeholder if they have not been issued with accession numbers) in lines 185-186 or Table 1.
Validity of the findings: See comments above
Additional comments: Line 74 What do you mean with ‘100 and more Populus species’?
Line 90 replace hybridization with hybrid
Line 91-92 It would be useful to include what data the Wan et al. 2009 study used to suggest the hybrid parentage of P. xiangchengensis. It would also be easier to follow this if you could include a diagram or a table of the suggested but disagreeing hybridization events that lead to P. xiangchengensis.
Line 95 delete ‘the’ before section Tacamahaca
Line 99 ‘as the uniparental inheritance’ is unclear.
Line 109 I would delete ‘the’ and ‘database’ around GenBank
Line 110 You should make it clearer that four of the listed species are sequenced for this study while the fifth is from a study currently in press
Line 115 I find selective breeding and crossbreeding overlapping to use both. Maybe you could use ‘resources for breeding’?
Line 127 genomic instead of genome
Line 128 What do you mean properly storing the DNA? -20 or -80?
Line 134 Are the 15.0 Gb data total for the four species or 15 Gb each?
Line 185 Whi,le we accept that plastome is made of double-stranded DNA as far as I know you can’t really see this from next-gen data. I think it would be best to just delete it.
Line 194-195 should be discussion
Line 205-205 These characters of the cp genomes are usual so I don’t think this needs reporting.
Line 210-211 How did you code the ATC start codon?
Line 217-218 should be methods
Line 223 Why is frequency of leucine and cysteine interesting?
Line 228-229 should be discussion
Line 233-234 should be discussion
Line 241-245 This is unclear. The copy of ycf1 in IRb is too short to refer to as gene. I think it would be more suitable to use pseudogene or a truncated copy of ycf1. Parts of the ycf1 gene (or pseudogene) are found in the SSC 15-158 bp at the IRb – SSC junction. The portion of the gene 1689-1707 bp is present in both IRs.
Line 246-247 should be methods
Line 248 the mean of 0.00210 is not in Table 3
Line 248-250 should be discussion
Line 251 I don’t think there is a valid intergenic spacer between ycf1 and ndhF. Its presence is entirely dependent on the structure of the IR junctions and based on Figure 5 missing from 3 out of the 5 species.
Line 252-254 should be discussion
Line 257-264 I found this bit too hard to read. It would be easier to report a general description or ranges of the SNPs and reference the table with the details.
Line 265-266 should be discussion or methods
Line 268 identified instead of uncovered?
Line 276-282 should be discussion or methods
Line 282-285 I don’t know what the 85 comparison refers to
Line 288-290 should be discussion
Line 289 undergoing instead of suffered
Line 293-298 should be introduction or discussion
Line 300 I would delete ‘occurred with high frequency’
Line 306-310 these are already in a table
Line 314-316 should be discussion
Line 316-320 this is a bit unclear
Line 322-323 should be in discussion
Line 327 I don’t think you need ‘further’
Line 326-328 should be methods
Line 328 Do you mean downloaded from GenBank instead of public?
Line 360-362: I think this might be the other way round: the different mutation modes are affected by the phylogenetic relationship, as in closely related species show similar mutation modes.
Line 365 I think calling the repetitive elements of inversions IRs are misleading as IR normally refers to the inverted repeat region of the whole cp geome
Line 367-373 This is a word by word repeat of Line 266-273
Line 384-395 This is a word by word repeat of Line 329-339
Line 398-400 What is debated about P. schneideri. I assume it’s whether it is a hybrid or not, but it would be useful to state this again here.
Figure 6 I would make the labels larger
Figure 7 I would include the species in which each loops are found in the figure or in the caption.
Figure 9 The caption needs to include the meaning of F, P, R, C. Also the similar patterns for panel A and B are confusing. If possible use colours here.
Figure 10 I would label the sections Populus on the figure. The caption needs to explain the meaning of the support values and the method the tree was generated.
Table 3 Is the pairwise nucleotide divergence averaged from the 600-bp rolling window over the length of the pairwise alignments?


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: FECAL MICROBIOTA TRANSPLANTATION RESEARCH OUTPUT FROM 2004 TO 2017: A BIBLIOMETRIC ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: It contained a relevant interpretation of data. It confirmed to the style and format of PeerJ.
Experimental design: Methods were enough to draw results to reply to the purpose of the study.
Network analysis was also good.
Validity of the findings: Results and discussion was well-described. the conclusion is simple and lucid.
Additional comments: I recommend the revision as follows:

 line 70 Core Collection (WoSCC) of Thomson Reuters
-->Core Collection (WoSCC) of Clarivate Analytics

106 number of national articles published each year were reported
-->number of articles according to country, published each year were report.

Otherwise, description was good.


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: FECAL MICROBIOTA TRANSPLANTATION RESEARCH OUTPUT FROM 2004 TO 2017: A BIBLIOMETRIC ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. The English expression should be clarified more to be clearly understood by the international audience.
    - Line 101 ~103, Line 328-330

2. Line 70/Line 394 : Thomson Reuters - Company name was changed as Clarivate Analytics(https://clarivate.com/)

3.Line 71: WOS is not a public database. It needs a subscription. It needs to be revised.
Experimental design: 1. Lin 85 : It is difficult to understand why you exclude the articles which cannot be acquired from WoS. As you mentioned in Line 83, most abstracts could be acquired from PubMed or the publihsers' homepage.

2. Line 112-116: It would be good to explain more clearly based on the overview of article selection process(Figure 1)

3. Line 113 : On the text, you mentioned 1,277 papers were excluded. However, on the Figure 1, you wrote 1,238. Please correct it.

4. Line 103-104 : It would be good to explain about Scopus search keywords and search date.(law data also could be uploaded)
Validity of the findings: 1.Line 225-228 : Needs to be added references to validate this sentence

2. Line 246-247 : Needs to explain why you select only top 100 highly cited papers

3. Line 251 : For not familiar with bibliometric analysis users, it would be good to explain the difference of "citation count" and "citation index".

4. Line 261-265 : Needs to write more clearly and explain more detail why you get this result(Line 265)
Additional comments: This paper examines an interesting topic using bibliometric analysis.
Although this paper shows some interesting findings, description of methodology is a little bit unclear to convince study findings related to the stated study purposes. For instance, you should mention more Figure 4 because it's quite a good visual diagram. In addition, you could explain more the differences between each bibliometric tools. It is good to add some benefits why you used bibliometric analysis, not a systematic review or meta-analysis.


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: FECAL MICROBIOTA TRANSPLANTATION RESEARCH OUTPUT FROM 2004 TO 2017: A BIBLIOMETRIC ANALYSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Figure 3 does not make a good sense, especially the linear line. Other reporting looks okay
Experimental design: Data extraction is okay but need further rigorous and in-depth analyses as outlined in the previous section
Validity of the findings: okay; most of the parts of the manuscript cover the basic reporting - it requires some further sophisticated data analysis to reveal any unknown findings
Additional comments: It seems the authors made a significant effort in this manuscript. However, most of the analyses they conducted are at very basic level. I would recommend the authors to follow these two articles as guidelines for further research analyses

Longitudinal trends in global obesity research and collaboration: a review using bibliometric metadata
A Khan, N Choudhury, S Uddin, L Hossain, LA Baur
Obesity Reviews 17 (4), 377-385

A Framework to Explore the Knowledge Structure of Multidisciplinary Research Fields
S Uddin, A Khan, LA Baur
PLOS ONE 10 (4), e0123537


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: FECAL MICROBIOTA TRANSPLANTATION RESEARCH OUTPUT FROM 2004 TO 2017: A BIBLIOMETRIC ANALYSIS
Review round: 1
Reviewer: 4

Output:
Basic reporting: •	English language grammar and/or punctuation is frequently incorrect or unclear. See lines 44, 64, 94, 99, 114, 115, 118, 128  for relevant examples.
•	Appropriate literature references to establish background research are sometimes omitted. See lines 57 through 60 for a good example.
•	Words/phrases unnecessarily repeated lead to awkward sentences. See lines 65, 47-49 for relevant examples.
•	Verb tenses and references to interactions are often incorrect. See lines 158 [American Journal of Gastroenterology… made contributions], 171 [extensive cooperation was carried out between institutions,], 180 [almost all the keywords appeared rising and falling fluctuations..] 212 [the increasing number of output indexed], 255 [was found, so does the relationship between].

Background: Unclear introduction as stated by line 26 [there has been no bibliometric analysis of FMT]. Analysis of what aspect of this literature and how does this relate to prominence of the literature? The meaning of “prominence” is vague and undefined. The reason for conducting a bibliometric analysis of an emerging therapy (FMT) is vaguely implied but not stated explicitly.
Methods: Line 28 states “cooperation of publications”. This is a confusing and grammatically incorrect sentence.
Results: Lines 33-36. Unclear statements of relationship and significance of keywords and domains.
Conclusions: Line 38 “Relationship between research performance of FMT” to “investigators master the trend” illogical as stated and grammatically incorrect use of English language active tense and transition. Closing sentence states a foregone conclusion “..which is also an ongoing hotspot of research”.
Experimental design: no comment
Validity of the findings: While there appears to be solid research presented the lack of idiomatic English and of clear explanations when needed make the article difficult to read. Native English readers could struggle through but be frustrated by incorrect grammar, sentence structure, and words that poorly describe meaning of the statement.

The conclusion is poorly stated and relates the purpose of the study to a foregone conclusion (e.g. that such studies aid undefined investigators)

Thorough editing of these elements would be required before considering publication.
Additional comments: The authors of this article have been able to generate a substantial amount of data appropriately using the tools selected for a bibliometric analysis. However, the errors and omissions as described in the previous review categories lead me to conclude that the paper is not acceptable for publication in the current form.


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: FECAL MICROBIOTA TRANSPLANTATION RESEARCH OUTPUT FROM 2004 TO 2017: A BIBLIOMETRIC ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Manuscript was revised according to reviewers'  comments appropriately.


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: FECAL MICROBIOTA TRANSPLANTATION RESEARCH OUTPUT FROM 2004 TO 2017: A BIBLIOMETRIC ANALYSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Made some effort, but not enough
Experimental design: Almost same as like the initial draft
Validity of the findings: Not quite sure
Additional comments: The author(s) do not follow my suggestions on the previous draft.


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: FECAL MICROBIOTA TRANSPLANTATION RESEARCH OUTPUT FROM 2004 TO 2017: A BIBLIOMETRIC ANALYSIS
Review round: 2
Reviewer: 3

Output:
Basic reporting: I am extremely pleased with the edits made to conform to conventional English language grammar and punctuation. Clearly the authors diligently worked to revise the problematic language and to clarify the meaning that was often unclear in the original submission.
Literature references that were added soundly supported the statements made to provide context to the meaning of the research. Due to the meaningful revisions, the questions that I posed regarding the conclusions drawn from previous studies are satisfactorily answered.
Figures are exceptionally striking and the enhancements highlight the most interesting results of the mapping.Tables are well organized and presented in such a way that subsequent studies will easily update the publication patterns. The highlighting used in Table 7 is particularly effective and I look forward to seeing followup data that will capture relevant terminology as the research base advances.

One slight edit needed due to improper tense in line 289: "These results suggested that it was challenging to published articles on FMT"
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Revision very well done. I commend the authors for the attention to recommended editing. I believe that this research is now presented in such a way that it is likely to significantly build the understanding of the status of research into FMT on an international 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: FECAL MICROBIOTA TRANSPLANTATION RESEARCH OUTPUT FROM 2004 TO 2017: A BIBLIOMETRIC ANALYSIS
Review round: 2
Reviewer: 4

Output:
Basic reporting: •	Lines 58-60: Run-on sentence. Also, what evidence do you have that systematic reviews fail to include all relevant research? What evidence do you have to prove publication bias?
•	Line 60-61: Provide reference.
•	Lines 70, 77: Clarify why you chose 2004 as your starting point.
•	Line 85: Correct grammar.
•	Line 97-98: Correct grammar. Maybe say, “…impact factors were also recorded using the 2017 edition of Journal Citation Reports (JCR)”.
•	Line 101, 102: Delete extra comma. Remove underline from “and VOSviewer”.
•	Line 103: the word “analyze” is used twice; replace one iteration with synonym.
•	Line 139-140: Add space between “top” and “100”. Also, what exactly are you trying to say here? Please clarify your statement.
•	Line 287: Correct grammar, say instead, “with the exception of one”
•	Line 371: Correct grammar. Say instead, “…. the inclusion of other databases, such as PubMed and Scopus, may have produced…”
Experimental design: •	Line 78: A librarian should have performed the search to ensure that you didn’t miss any relevant articles that may have used different synonyms. You mentioned other possible keywords resulting from your analysis in lines 221-223.
•	Line 86-87: Why was full-text downloaded from databases other than WoS? We don’t need to know where/how you got full-text.
•	Line 120: Explain things better and correct grammar: “….a total of 2,062 publications were identified through our search strategy….. 1,238 publications were excluded because they did not meet our exclusion criteria (misleading titles/abstracts; FMT not main topic; abstract inaccessible; duplicates)…. 28 additional articles were excluded because they were non-English language.)
Validity of the findings: •	Line 134: What do you consider “dynamic growth”?
•	Line 266 (and earlier): Did you include or exclude self-citations? You should mention this.
•	Line 276: H-index is the impact of an individual author, not a publication, so it is confusing/misleading to mention here without more context.
•	Line 284-286: You say that the top-cited articles are usually published in high IF journals….but this is a catch-22…. Maybe the articles are not higher quality but just get cited more because the journal is more ‘prestigious’ but this is a self-sustaining cycle.
•	Line 303: Define what you mean by “items”. Keywords? What about FMT?
•	Line 368: Additional study limitations include non-comprehensive search strategy (could have missed relevant articles that used other synonyms for each concept); articles without abstracts were excluded.
Additional comments: No additional comments