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: MINING THE POTENTIAL PROGNOSTIC VALUE OF SYNAPTOSOMAL-ASSOCIATED PROTEIN 25 (SNAP25) IN COLON CANCER BASED ON STROMAL-IMMUNE SCORE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Zou et. al have attempted to provide the potential prognostic value of SNAP25 in colon cancer based. The paper though was well written need to be checked for grammatical errors and spell checks.

line 89

1) Lot of tools and software are not referenced in peerj format, change them to the required format.

Eg:
FunRich 3.1.3 (http://www.funrich.org/) can be reference with https://pubmed.ncbi.nlm.nih.gov/25921073/

3) Relationship between TILs and Survival should be outlined more to drive the point of why correlation between TILs and gene is important.

4) Conclusion should also include with limitation of the methods used.
Experimental design: 1) Database and estimation of stromal and immune scores - lacks information about the data such as filters to obtain specific data, you should shift the description of the data from this subheading  "The relationships between stromal/immune score and clinical features" to here

2) GEO data- why was only two GSE series was chosen? Also it would be good to show all the 15 genes survival outcomes of hub genes thus your selection of the two genes is justified

3) There is an information gap of how the RNASeq data was normalized?

4) why was the DEG from RNAseq (using counts or RPKM) values was also not considered to see how the 15 hub gene are expressed?

5) Also it would be good to instead information on the control samples that shows the DEGs are really DEGs in normal.

6) GSEA could have been done on all 15 hub gene, thus APQ4 and SNAP25 are prominent in survival.
Validity of the findings: 1) The manuscripts lacks the clarity of how only APQ4 and SNAP25 are best in survival outcomes - compared to other 13?

2) The transition from two gene APQ4 and SNAP25 to only SNAP25 focus is unclear? The GSEA was done on both, why was APQ4 not investigated further?

3) The usage of stormal/immune scores for 430 colon cancer patients is concluded with no statistically significant difference. This contradicts the usage of these score and the dataset? (line 145-146)
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: MINING THE POTENTIAL PROGNOSTIC VALUE OF SYNAPTOSOMAL-ASSOCIATED PROTEIN 25 (SNAP25) IN COLON CANCER BASED ON STROMAL-IMMUNE SCORE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is well written with clear and unambiguous language. The figures are well illustrated with clear descriptions.

There are minor errors to correct:
- Line 50: please remove the 2020 in front of the literature citation
- Line 89: please change flod to fold
- Line 158-163: please include the long form of CC, MF, BP (cellular component, molecular function, biological process/ biological pathway) because this is the first time the short form is used in the main text
Experimental design: The experiment is well designed and performed.
Validity of the findings: The findings and conclusions justify the results shown, and they are statistically sound.

One suggestion to improve data interpretation:
- Figure 5: it is not explained what the dotted blue/ red lines are. Are they the standard deviation of the Kaplan-Meier plot? Please indicate it on the Figure description or the main text.
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: CRANIOFACIAL ONTOGENY IN TYLOSAURINAE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is generally written well, but could use some editing to become less redundant and improve the readability. Specifically:

Line 36: remove "Literature Review" subheading as it is implied by an introduction.

Lines 43, 48, 55, 66, 73: instead of starting every line with "In XXXX, Author", use Author (XXXX). For example, Line 43 "In 2007, Caldwell published..." can be "Caldwell (2007) published". This will make the start of every paragraph less repetitive.

Lines 37 to 80: there is no need to cite the same paper multiple times in the same paragraph if it is the only one you are discussing.

Line 239: this paragraph is a bit difficult to follow for someone unfamiliar with size-independent ontogenetic studies. You're making two arguments here about size, (1) that size differences can be phylogenetic or ontogenetic variation and (2) size is variable and normally can't be used to reliably assess maturity beyond broad groupings. I suggest adding to this section to flesh out these separate ideas.

Line 269: you could cite Carr (2020) or Frederickson and Tumarkin-Deratzian (2014) for the definition of synontomorphy as well.

Line 270: "Kansas University" is technically the "University of Kansas". I'd use the Kansas Museum of Natural History here instead.

Line 282: there is no need for initials since you are the only author.

Line 311: those tables are results.

Line 329: put hypothetically before "will". I'll discuss this more in the next section.

Line 370: "one the other hand" should be "on the other hand".

Line 370 to 372: this paragraph is a bit confusing as it comes across like you haven't already done the analysis. I understand why you presented both, but in reality you only need to discuss the one you actually did.

Line 417: small and large are relative terms. If you can quantify them or show a figure (like in the SD), I would do that.

Line 427 (and throughout): less than or equal to is more easily shown as the symbol.

Line 690: All hypotheses can be refined with the addition of more data. A  similar line to this comes up many times in the discussion. I would move it to the conclusions.

Line 703: E in Figure 5 shows another possibility for dimorphism without bifurcation.

Lines 720 to 732: this paragraph seems redundant with the previous one. Consider combining them into one section.

Line 999: Royal Tyrrell Museum of Palaeontology.

The literature cited is comprehensive. I'd suggest adding Carr, 2020 to the manuscript as it was recently published. There are multiple errors in the work cited outlined below:

"and" should be "&" in internal references (throughout)
Comma needs to be removed after journal (lines 1054, 1068, 1079, 1085, 1134, 1148)
Capitalization errors (lines: 1060 Vertebrate; 1066 Reports; 1088 Science; 1159 & 1182 PLOS ONE; 1201 Functional...)
No periods for author initials (throughout)
No "and" in multi-authored papers (throughout)

The figures are great and the first three are the first time I've seen a visual description of the predicted outcomes outlined in other cladistic ontogeny studies. I would even argue that some of the important anatomical figures from the supplementary information would be appropriate to move to the main text.
Experimental design: SD character 1 and 10: Is there a reason for the character optimization for TSL and QH? The character states appear to be random intervals (e.g., Less than 400 [399], 400 to 799 [399], 800-999 [199], 1000-1499 [499].

SD character 1 and 10:  What happens if you run the analysis without the size characters? One could argue that using size characters and then a correlation for size is circular reasoning.

Line 262: unordered and equally weighted?

Line 264: and since no single juvenile specimen has a complete character coding of 0s.

Line 265: how did you handle coding for unordered, multi-state characters in the artificial adult?

Line 286: whole number to what length unit (e.g., centimeter)?

Line 303: what do you mean removed due to incomplete coding? It would be helpful to elaborate here on how you decided to remove these uninformative specimens.

Line 319: this is still hypothetical as nobody has yet shown how sexual dimorphism can alter the tree topology in cladistic studies of ontogeny. Though it is possible or even reasonable to assume it may bifurcate, I'd treat this as a working hypothesis by Frederickson and Tumarkin-Deratzian (2014) rather than a definitive test. Add some caution here (such as inserting "hypothetically" before bifurcate in line 329) and I think it is acceptable.

Line 454 (and multiple other places): What is the justification for defining stages that are not supported by synontomorphies?

Line 756: this is an interesting and clever way to test for anagenesis.
Validity of the findings: Overall, I see no serious concerns over the findings and interpretation. I have outlined two areas below where discussion could be added.

Line 680: see Hone et al., 2020 on sexual dimorphism and sexual size dimorphism. We would likely need an obvious character and/or a very large sample to distinguish. Though I agree with your interpretation for the current data set, it may still be too small to rule out.

Line 919: what does changing the size imply for the function of these neurovascular canals? Do you think this also relates to changes in niches between juveniles and adults? I am intrigued by the broader ecological implications of these findings.
Additional comments: This paper is an impressive and important contribution to our understanding of mosasaur ontogeny. I feel that this paper will be worthy of publication in PeerJ following the revisions and some elaboration outlined above.


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

Input:
Title: CRANIOFACIAL ONTOGENY IN TYLOSAURINAE
Review round: 1
Reviewer: 2

Output:
Basic reporting: My major issue here is that most of the important anatomical data the readers need to see are tucked away in supplementary information. The ontograms presented in this paper are built on the author's choices of characters and character states, so they should be front and centre in these figures. Fortunately there is space for this. Figures 2–5 do not really add anything to the manuscript (they are verbally explained in the text already). This frees up "room" to detail the ontogenetic characters and show the discrete variation in bones/sutures.

I am also unclear how any of the continuous variables (e.g. quadrate height/proportional characters) were partitioned into discrete states. Sometimes it appears to be arbitrary (e.g., dividing measurements into multiples of 50mm as discrete states). Are these partitions biologically meaningful? Please clarify this in the Methods, but also consider the extensive body of literature on the topic of partitioning continuous anatomical data into discrete characters for cladistic analysis.
Experimental design: This study appears to follow the rationale from previously published papers on how to construct ontogenetic trajectories using a cladistic approach. I do have some conceptual and technical questions throughout the manuscript, but I refer the author to the attached PDF for those.

The strength of the study is in the section on Tylosaurus. While the author includes over 100 specimens for this analysis, they have personally observed less than half of those. This is still an impressive number of personally observed and photographed specimens, but the manuscript overreaches by including two additional mosasaur taxa (Mosasaurus hofmannii and Tethysaurus nopscai) for which they have not collected any of the data themselves. These two additional analyses need to be removed.

Furthermore, I would re-run the analyses using the 45+ specimens of Tylosaurus that the author has personally observed. Do these ontograms match the ones the author augmented with images from other sources?
Validity of the findings: There is certainly validity and importance to reconstructing an ontogenetic series for well-represented mosasaur species, and the effort to do so is clear. Unfortunately, I think the manuscript overreaches from there. The core data are the specimens the author has personally observed and scored into their ontogenetic, cladistic analysis. These should be the focus of the results and discussions sections. There is too much discussion of anagenetic evolution and broad-stroke conclusions about mosasaur ontogeny. These are not only unnecessary, but misleading, because the data are too limited to make many of these claims (I have pointed these out in the PDF).

I think a major refocus of the paper could greatly improve these shortcomings.
Additional comments: I have included my major comments here, but please see the highlighted sections (with comments) in the attached PDF for more details.

-	Introductory figures: Figs. 2–5 are hypothetical scenarios that are already summarized in the text. We do not see the first image of a mosasaur bone until Figure 6. If this study is to provide a new character list for assessing ontogeny in tylosaurine mosasaurs, the bulk of the figures need to be devoted to illustrating this anatomical variation. After all, that is the data upon which all of this has to be based. This should not be tucked away in supplementary information.

-	Tethysaurus and Mosasaurus ontogeny: given that the author has not personally seen any of this material, this section needs to be removed. There is no primary data collection here and it therefore is entirely based on illustrations and images from other sources. Besides, this detracts from the bulk of the paper, which is actually about Tylosaurus. The paper needs to be re-focused there.

-	Discrete growth stage assignment: I have an issue with how growth stages were assigned here. How can a discrete growth stage be assigned without any unambiguous character states to define it? Does this not become an “absence” problem, particularly at the base of an ontogram? Are these discrete states defined by the fact that they don’t show any of the features of the subsequent stages? Moreover, how were all of the continuous variables (e.g. quadrate height, proportion characters) partitioned? Is there good statistical reasons to separate them into their bins, or was it arbitrary? I would highly recommend following the suggestions of Simoes et al. (2016): “Giant taxon-character matrices: quality of character constructions remains critical regardless of size” (Cladistics). They provide explicit guidelines for partitioning these kinds of continuous variables into character states.

-	We need to see the anatomical features in the main text for these ontogenetic stages. I am not a fan of relegating all of this important data to the supplementary information. It IS the information upon which all of this relies. The skull/bone images in Figures 6 and 7 are a nice asthetic, but we need to see what the discrete anatomical variation looks like and it needs to be clearly illustrated and labeled.

-     Branch support and robustness of the ontograms: these are very poorly supported topologies upon which the conclusions are drawn. This is likely a product of the low sample size and number of characters, but it is important to remember how tenuous such conclusions are from these types of cladograms. I would focus the text on "nodes" or regions of the cladogram for which you have the most data/specimens.

-	Postcranial data: this paper is strictly about cranial ontogeny and makes some very bold and broad statements regarding tylosaurine taxonomy and evolution. However, tylosaurines are quite well represented by postcranial data. How might this affect the interpretations made here? It’s a worthwhile thing to discuss, because all too often in mosasaur phylogenetic analyses/taxonomy, the skull (and particularly the quadrate) take precedence over other bits of mosasaur anatomy. Nowhere is this more obvious than in the attempt to reconstruct the ontogram for Tethysaurus: it is nearly entirely partitioned by the quadrate.

-	Assignment of “juvenile”, “subadult”, and “adult” statuses: in palaeontology, these are often completely arbitrary and relative terms. I do not know where along the authors’ ontograms I would place these labels, but I take issue with their use of these terms throughout the discussion, particularly when trying to re-diagnose several well-studied taxa. Please see my specific comments in the attached PDF for more detail. These modified cladograms reveal relative “relationships” of individual specimens to each other, but do not reflect the actual ontogenetic status of each individual included in the analysis. These are relative to each other and to an apparently “imaginary adult” and “embryo”. There are severe limitations in terms of what can be said from these analyses and it’s important not to overstretch those boundaries in the discussion.

-	Evolutionary and taxonomic implications: as it is currently written, the discussion section really seems to overreach. These ontograms are not really testing for anagenetic evolution or sexual dimorphism. Those data have to come from other sources. In fact, the ontograms contain absolutely zero evolutionary information without a phylogeny. Testing for anagenesis would involve detailed accounts and inclusion of georgraphic, geologic, and phylogenetic information. I would refocus this on the implications for assigning relative ontogenetic status of individual Tylosaurus specimens. There is no reason to go beyond that, given the data presented in the MS.


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: CRANIOFACIAL ONTOGENY IN TYLOSAURINAE
Review round: 1
Reviewer: 3

Output:
Basic reporting: To whom it may concern:

The study presents, first and foremost, a novel hypothesis concerning possible correlations between certain osteological characters and ontogeny in mosasaurs. This is the very first such an attempt to my knowledge for the taxon in question. The written English is clear and articulate throughout the manuscript, both in the main text and figure/table captions--it was very easy to follow, and I suggested very minor editorial corrections in the annotated PDF. The literature references are both adequate and thorough, and I was unable to make any additional suggestions for more references for the scope of this study.

As far as the article structure/organization was concerned, I believe that Introduction can be a little better organized to deliver the information in a little more logical manner. Specifically, under "Mosasaur ontogeny," the author appears to review both general and genus/species-specific studies on mosasaur ontogeny, yet part of that is found under the subsequent "Tylosaurus proriger" section and onward. I also found Introduction to be rather extensive, unless it's normal for PeerJ. Similarly, the author may consider eliminating Conclusions for the bulk of the contents are already mentioned in the preceding Discussions section, which happens to be also quite extensive and detailed.

As for figures, I find it more helpful that the author include a few representative specimen photos for both Tethysaurus nopcsai and Mosasaurus hoffmannii in their respective ontograms.

Finally, all relevant results of this work have been presented to address new hypotheses.
Experimental design: No comment, except I still find the process of determining ontogenetic stages using osteological characters seemingly circular. The author stated that such osteological characters are independent of absolute size of these mosasaur specimens, in which such characters were either confirmed or absent. At the same time, the author seems to present the logic that osteological traits deemed mature are generally found in larger specimens, and vice versa, which to me appears to introduce a potential circular argument. I don't believe that the proposed ontogenetic markers or traits are entirely independent of the sizes. See my comments on the annotated PDF file, line 288.
Validity of the findings: No comment, but see the above.
Additional comments: I look forward to the publication and continued refinement of this work into the future. I hope my comments will be of benefit.


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: CRANIOFACIAL ONTOGENY IN TYLOSAURINAE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The changes made improved the reporting style.
Experimental design: I believe the author addresses all of my earlier concerns.
Validity of the findings: I still see no issues with the findings. Limiting the scope of this paper was a prudent decision that strengthens the overall argument.
Additional comments: You were able to satisfy all of my concerns without sacrificing any of your major points in the paper. I believe it is now acceptable for publication in PeerJ.


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

Input:
Title: CRANIOFACIAL ONTOGENY IN TYLOSAURINAE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The basic reporting is clear, contains well-written hypotheses, predictions, and conclusions. Much improved over the first version, particularly after removing Mosasaurus and Tethysaurus from the manuscript. It feels much more focused.

In my opinion, adding figures of several of the osteological features in question to the main text makes it much easier for the reader to follow, rather than switching over to the supplementary information.
Experimental design: The experimental design is in line with other ontogenetic studies done by Carr and others. The methods are very clear now as well.
Validity of the findings: I was concerned that the discussion/conclusions of the first draft overreached a bit, particularly when addressing broader mosasaur ontogeny and evolution. This version is restricted to the core data from the first draft. As a result the findings and their implications are clearly stated and in line with the results from the author's cladistic analyses.
Additional comments: First, let me commend the author on taking the time to consider each of my comments (and those of the other reviewers). I was particularly happy to see the author explore the possibilities of how to partition their continuous variables into discrete characters for their cladistic analysis in the rebuttal letter.

Second, I think removing the sections on Mosasaurus and Tethysaurus makes the manuscript more focused. It flows and follows a single set of research objectives. I do not have any major content-related comments/edits to recommend for this draft.

I have only minor (mostly grammatical, I believe) corrections to the revised draft. I hope you find them helpful.

Sincerely,

Aaron LeBlanc


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: CRANIOFACIAL ONTOGENY IN TYLOSAURINAE
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: Please re-evaluate your argument for the paedomorphosis.
Additional comments: Dear Author,

I have tightened and provided editorial comments to the main text. Introduction and Results sections need least changes, and that is true with the Discussion section up to line 762. After this line, your Discussion section begins to steer away from the original data of your work, which have been well presented and discussed up to this point. Namely, there appear to be an extensive range of future work suggestions accompanied by review of the literature, that seem to stretch out and become defuse. In particular, I strongly suggest that the "Synthesis of ontogeny and phylogeny" section be taken out. I get your points, but this study doesn't answer these issues directly.

Aside from the aforementioned editorial suggestion, which I hope you kindly consider, please consider the following. First, please revise Figure 14 and eliminate any misunderstanding of what constitutes the basioccipital, which is distinct from the pair of exoccipitals, something you seem to consider part of the basioccipital. This is critical because the shape of the occipital condyle plays prominently in shaping your ontogram(s).

Second, I believe the justification for paedomorphosis as the mechanism behind the curved lateral borders of the parietal table in T. proriger may require refinement. Please refer to my comments in the relevant section.

Once again, please consider streamlining your Discussion, as well as addressing the two specific points I raised above--Fig. 14 and your paedomorphosis argument. Once these are addressed and corrected or refined, I believe this important and novel work concerning mosasauroid ontogeny is ready for publication, which I look forward to very much. Last but not least, I thank you very much for your patience waiting for my review.

Sincerely yours,
Takuya Konishi


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: MIR-29A-3P DIRECTLY TARGETS SMAD NUCLEAR INTERACTING PROTEIN 1 AND INHIBITS THE MIGRATION AND PROLIFERATION OF CERVICAL CANCER HELA CELLS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The research article by Chen et al. describes how miR-29a-3p directly targets Smad nuclear interacting protein 1 and reduces the migration and proliferation of cervical cancer HeLa cells. This is an important study as it opens up new avenue to target cervical cancer by inhibiting their proliferation and migration.
Experimental design: The experiments performed by the investigators are designed thoroughly and are interpreted clearly. There is sufficient details on the experimental procedures used and the author has clearly discussed the loopholes in the study.
Validity of the findings: However, I have certain queries and suggestions for the authors as given below:
1.	I believe the title of the manuscript sounds vague. I would title this manuscript as “miR-29a-3p directly targets Smad nuclear interacting protein 1 is directly 1 and affects the migration and proliferation of cervical cancer HeLa cells”.
2.	Figure 1E shows that the relative cell viability decreases significantly at 48 hrs post siSNIP1 treatment. However, at 72 hrs the viability seems higher than 48 hrs in the siSNIP1 treated groups. Please explain the possible cause of this effect?
3.	Also, in the Figure 1F, E- Cadherin expression should be significant as the expression has increased by 10 folds post- siSNIP1-330 treatment and it lacks * mark on the figure.
4.	Figure 2F blot is unclear and I would suggest it to be replaced with a clear one to see significant downreguation in SNIP1 expression at protein level.
5.	Figure 3D again shows all markers significantly downregulated except E-cadherin which seems significantly upregulated statistically and lacks * mark.
6. Can you show the effect in vivo by injecting the control vs the miRNa transfected cells in a mice model to show the effect on HeLa cell migration and proliferation?
Additional comments: The manuscript definitely requires lot of corrections in terms of language and grammar. It lacks proper scientific writing, for eg: terms have been vaguely used such as in line number 135  “related genes (CDK2) in HeLa cells (Wang & Chen, 2019) can also be regulated (Fig. 1F)”. It can be rewritten as downregulated or upregulated.


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: MIR-29A-3P DIRECTLY TARGETS SMAD NUCLEAR INTERACTING PROTEIN 1 AND INHIBITS THE MIGRATION AND PROLIFERATION OF CERVICAL CANCER HELA CELLS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this manuscript, Chen and colleagues report a novel regulatory interaction between Smad Nuclear Interacting Protein 1 (SNIP1) and miR-29a-3p with consequences on Hela cell proliferation and migration. Overall, I commend authors on doing a good job in putting together this concise and timely piece of work. However, I would recommend a few additional changes (also check Section 3)  before acceptance, which I believe could help readers grasp and appreciate the scope of the study better.

A. The foundation of the entire study relies on HeLa cells but authors pitch the potential relevance of their study in context of cervical cancer.  These claims should be toned down since authors don’t provide any data on levels of SNIP1 (and miR29a) from primary cervical cancer samples. While Hela cells are of cervical origin, at this point they have been growing in cultures for more than 5 decades, so it’s at best a cell culture model more than a cancer model.

B. Instead of the purported significance of the study to provide therapeutic solutions to cervical cancers, the highlight of the study could be the novel regulatory link between miR29a and SNIP and how this interaction plays a ‘master regulator’ role in controlling proliferation and migration. To me this is the most significant message from this work and authors could focus a bit more to highlight the same.

C. The manuscript is easy to read and generally written well. Introduction provides a good background of the miRNA and SNIP1 literature. But authors should provide more background on miR29a in the discussion.
Experimental design: As such, I find the primary research of this study lies within the Aims and Scope of Peer J. Regulation of SNIP1 is poorly understood and this work provides new mechanistic hints involving miRNA axis. The experiments are well planned  and executed, adequate controls have been presented and raw data has been shared. Overall, the method sections provide sufficient details.
Validity of the findings: The findings are generally internally consistent with the underlying hypothesis and narrative, but I have a few concerns for authors to address:

A. In Fig 1E,  viability of siSNIP1 drops significantly at 48h but recover to near-normal levels by 72h. Can authors comment or speculate on this peculiar trend. Is this because the effect of siRNA wears off by 72h. It would be good to support this finding by showing mRNA (and protein) levels at 48h v/s 72h for siSNIP1 scenario compared to control.

B.  The figure legend for Fig 2 could be changed to  ‘miR29a-3p directly targets SNIP1 to downregulate SNIP1 expression’. This change will reflect the data and its significance better for readers.

C. In Fig 3a, why do the NC condition also show poor migratory recovery in the wound-healing assay. Although, statistically significant, the effect size is very negligible between NC and miR29a case. Could authors comment on this?
Additional comments: The schematic in Fig 4B is not correct conceptually (at least to this reviewer).  The relation between miR29a and SNIP1 (negative regulation, symbolised by ‘inverted T’) is shown correctly. But, SNIP1 is a positive regulator of  HSP27, c-Myc and Cyclin D1 and they should be linked by ‘Arrow’ (indicating positive regulation) and not ‘inverted T’. Further downstream, arrows (or dashed lines) should link these 3 players to Cell Migration and proliferation. Dashed arrows/lines are best to use since authors don’t address any of these aspects in this study.

I hope authors will find these comments instructive and helpful in preparing their revised manuscript. If addressed suitably, I would recommend this manuscript for ‘acceptance’ at Peer J.


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: ISOLATION AND SEQUENCE-BASED CHARACTERIZATION OF A KOALA SYMBIONT: LONEPINELLA KOALARUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English used throughout this manuscript is clear and the literature cited is relevant.

I would, however, recommend incorporating this recent and highly relevant paper into the introduction (perhaps in the paragraph of lines 62-74):
Faecal inoculations alter the gastrointestinal microbiome and allow dietary expansion in a wild specialist herbivore, the koala (Blyton et al. 2019).

Additionally, on line 80, I would replace Brice 2019 with this reference:
Gut microbes of mammalian herbivores facilitate intake of plant toxins. Kohl KD, Weiss RB, Cox J, Dale C, Dearing MD
Justification being that Kohl et al. 2014 experimentally demonstrated the point you’re making.

In figure 1, I would recommend bolding and placing an asterisk on the UCD-LQP1 leaf for clarity.

In figure 2, I would again recommend annotation of the UCD-LQP1 track to help quickly orient the reader. The ANI heatmap confused for a while until I realised that perhaps it is incorrectly oriented? It makes sense to me for it to be rotated 90 ° counterclockwise.
Actually, I think the issue is that the y-axis of the ANI heatmap is missing from the provided figure (was present when viewing through Anvi’o).

Do the authors know the history of the koala they sampled? When was it brought to the San Francisco Zoo? Was it brought over from a Zoo (or the wild) in Australia? If so, which state/population, etc? What species of Eucalyptus is it being fed? Such information could be useful for future investigations comparing the author’s L. koalarum assembly to ones from different populations.

Overall, the level of reporting and availability of resources in this manuscript is commendable. I love that a Jupyter notebook was uploaded containing extra background and the scripts ran. I can also confirm that the Anvi’o databases they provided are working. However, I could not find the raw sequencing data anywhere. I would request that the authors upload this both for reproducibility, and for future use with improved assembly software/tools.
Experimental design: I see no issues with the methods and analyses used by the authors, and they are cited appropriately.
Validity of the findings: no comment
Additional comments: This paper is a logical extension from the authors’ previous work (Dahlhausen et al., 2018), and I think it’s great to see more work being done on the functional characterisation of host-associated microbes. Overall, I’m happy to recommend acceptance of the manuscript for publication on the provision that my comments are addressed.


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: ISOLATION AND SEQUENCE-BASED CHARACTERIZATION OF A KOALA SYMBIONT: LONEPINELLA KOALARUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors isolated a strain of Lonepinella koalarum and investigated genes that may be used for plant secondary metabolite degradation, carbohydrate metabolism, and antibiotic resistance. They compared the isolate genome to two other L. koalarum genomes from Genbank.

The article is well written and includes a sufficient introduction and background. Figures and tables are relevant to the article, appropriately described and labeled. Data is available from NCBI and permits for sample collection is provided. However, the NCBI accession number is missing from the manuscript.
Experimental design: The primary research is within the scope of the journal. A rigorous investigation was performed with well-designed, robust methods that could be reproduced.
Validity of the findings: All underlying data has been provided. Conclusions are well stated, linked to original research question and limited to supporting results.
Additional comments: The fact that you have an isolate means that you could test for antibiotic resistance but it is out of the scope of the manuscript and could be a future project.

The manuscript follows on from previous work that showed that L. koalarum could be used as an indicator of koala health. How common is L. koalarum?

Minor edits are included below:

Line 102: brackets around Phascolarctos cinereus.
Line 389: Supplementary Table S2 doesn’t refer to taxonomic names.
Figure 2: I find ‘private’ confusing. Maybe it would be better to refer to these gene clusters as ‘unique’.
Table 3 title: genome assemblies unitalicised.
Table 4: I’m not sure what the “no approved entry” means. It maybe best to remove it.


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: ISOLATION AND SEQUENCE-BASED CHARACTERIZATION OF A KOALA SYMBIONT: LONEPINELLA KOALARUM
Review round: 1
Reviewer: 3

Output:
Basic reporting: Clear and unambiguous English is used throughout and the literature cited is appropriate. The background and context presented in the introduction could be improved (see my point by point responses). The structure is generally appropriate although a section of the results is presented in the conclusions. The article is self-contained.
Experimental design: The research is original, performed to a high technical standard and the methods are well described. The research question is well defined, however, the knowledge gap that it fills could be better expressed. I suggest couching the genetic characterisation of lonepinella around what it tells us about its functional niche and how that related to koala nutrition and digestion. Tannin degradation may be one aspect but it is only a small part.
Validity of the findings: The overall findings are sound. I would, however, suggest a more detailed presentation of some of the outcomes. See my general comments for more details.
Additional comments: The manuscript by Dahlhausen aims to genetically characterise Lonepinella koalarum, a member of the koala gut microbiome that has previously been identified as able to degrade tannin-protein complexes and may improve koala survival during antibiotic treatment. The methods and analyses are appropriate to meet these aims and their presentation is refreshingly detailed. However, I think that the major findings of the study are not well described or elaborated upon.

There is a strong focus on the detection (or the lack there of) of tannin-degrading genes. Yet such genes are poorly characterised and not well represented in annotation databases. Additionally, the benefit of tannin-protein complex degradation to koala nutrition is questionable as it is thought that the liberated protein cannot be absorbed by the koala in the hindgut and may instead only serve to benefit the microbial community. Furthermore, phenotypic studies have already shown that lonepinella is capable of degrading tannin complexes and thus genetic determination of this function provides little additional information about the species.

Instead, I feel that the main benefit of this work would be to identify lonepinella’s functional niche within the microbiome and describe how its functions could benefit koala nutrition, digestion and health. While many of the analyses need to achieve such a characterisation have already been performed, they have not been presented in sufficient detail to build an overall picture of lonepinella’s role in the microbiome. The analyses also mainly describe how lonepinella differs from closely related bacteria but what about its overall all metabolic functions? More details and discussion is needed around specific degradation pathways, what section of these pathways are present in lonepinella and the functions these enzymes and pathways have. The manuscript would also benefit from placing these functions and pathways in the context of koala gastro-physiology and lonepinella’s proposed functional niche within the microbiome. See my point-by point responses for further details.

Point-by Point comments:

Abstract
L21: write species name in full at first mention
L23: What is meant by a “common member”. L. koalarum is found at very low relative abundance in the faecal microbiomes of koalas and is not detected in the majority of koalas (potentially due to it falling below the detection threshold in most cases, see (Alfano 2013, Brice 2019 and Blyton 2019).
L18-34: It would be good if the abstract included a summary of the studies major findings. What unique genes were found? Where did it fall in the phylogenetic tree? What plant secondary metabolite degrading genes were found? etc. It would also be useful to have a conclusion to indicate what these findings suggest for the role of L. koalarum in koala digestion and health.

Introduction
In general the introduction is very focused on PBMCs and their detoxification, however, the koala microbiome as a whole also plays an important role in macro nutrient digestion and fibre degradation (see Brice 2019 and Blyton 2019). This should also be covered in the introduction and be flagged as potential ways that lonepinella could contribute to koala digestion/health. These functions are covered in the manuscript’s analysis of the lonepinella genome and could be nicely given context in the introduction. It would also be useful to indicate why the genomes were screened for genes associated with antibiotic resistance.

L43: They can also cause negative post-digestive feedback by making the koala feel “sick” as discussed in Lawler, Foley and Eschler. Also many of these really are not toxins but rather anti-nutrient compounds. I think it is inappropriate to simply refer to them as toxins. I suggest referring to them as PBMCs.
L70: It is worth briefly outlining what tannin-protein complexes are and how they influence koala nutrition.
L72: You should give a bit more detail on this finding. Was it the abundance of L. koalarum before treatment that was predictive? The presence/absence of the bacteria? Or was it how well L. koalarum was maintained through the treatment that predicted koala survival?
L69-71: I think it is important here to provide a bit more background about what is known about L. koalarum given it is the subject of this study. For example, Osawa showed that L. koalarum may by mucosal associated in the caecum. If doing this extends to introduction too much then some of the detail on the Eucalypt toxins could be condensed.
L80: “well-being” isn’t a scientific term. I suggest revising.

Materials and methods
L207-226: Why was the phylogenetic tree assembled from the 16S gene sequences instead of constructing a full genome tree? What was the benefit of constructing this tree compared with the GTDB tree?

Results and discussion
L289: It is of interest what proportion of isolates from the culturing reported in the methods were found to be L. koalarum by 16s Sanger sequencing and what (if any) other taxa were isolated. Perhaps a short summary could be given in the results?
L290: What was the genome coverage?
L328: How many tannin-degrading genes are present in the database used for the genome annotation? In general tannases are not well characterised. For example, only one KEGG orthalog was present last time I looked.
L331: Was a clear zone present around isolate UCD-LQP1 on the plate? Bacteria without tannin-protein complex degrading capability are capable of growing on those plates if they are tannin tolerant. Only the presence of a clear zone indicates tannin degradation.
L338-340: Again how many tannases are present in the annotation databases?
L346-347: These enzymes can nonetheless play important roles in degradation. The identified enzyme and function of these genes should be summarised in a supplementary table. It would also be worth interrogating these functions and describing them in the text.
L348-349: Or because the tannases are not in the database.
L350-L354: It would be useful to map the identified genes onto these pathways (there are tools for this on the KEGG website) and determine if they form a continuous degradation/synthesis chain (i.e. are all enzymes necessary for conversion between two compounds present?). These are large pathways, what sections of the pathway are represented? What compounds are degraded by the genes identified in L. koalarum? This will give a much more specific indication of what functions lonepinella is performing.
L491: oligosaccharides in Eucalyptus leaves will be absorbed by the koala in the small intestine and only a small fraction would enter the caecum and colon. As you say, this means that the bacteria in the hindgut are most likely using these pathways to process the products of the degradation of complex carbohydrates with cross-feeding among microbiome members. The benefit of such activity to koala nutrition is not well understood.
L492-501: This is an interesting and important finding. Was there evidence that L. koalarum is capable of fibre fermentation and the production of short-chain fatty acids?
L502: reference required

Conclusions
L506-523: These are not conclusions and should be presented as a section on antibiotic resistance in the results section.
L528: This sentence does not fit with the previous sentence as in the first you say beneficial members need to be identified but then explicitly talk about L. koalarum without first justifying that it is one of these beneficial members. I suggest revising.


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: ISOLATION AND SEQUENCE-BASED CHARACTERIZATION OF A KOALA SYMBIONT: LONEPINELLA KOALARUM
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed the reviewer comments and suggestions. I'm happy to recommend the manuscript for acceptance.

I'd like to thank the other reviewers for their valuable feedback and 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: ISOLATION AND SEQUENCE-BASED CHARACTERIZATION OF A KOALA SYMBIONT: LONEPINELLA KOALARUM
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Just some minor comments:

Line 267: 16S rRNA gene sequences
Line 420 and Line 423: Citric acid cycle?
Line 527: phosphotransferase


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: ISOLATION AND SEQUENCE-BASED CHARACTERIZATION OF A KOALA SYMBIONT: LONEPINELLA KOALARUM
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I reviewed a previous version of this manuscript. I find the current version of the maiscript much improved and the authors have adequately addressed my previous concerns. I am particulary pleased to see that they have taken many of my suggestions on board.

I have only a few minor comments/suggestions on the current version and would recommend acceptance of the article subject to them being addressed.

point by point comments:

Introduction
L: 87-90: I think the salient point here is that tannin bound protein is not able to be digested by the koala or utilised by the microbes. Maybe simplify/clarify the current explination?
L94: Well I would assume they were alive at the beginning of the antibiotic treament. I suggest revising this sentence.

Materials and methods
L226: I don’t think the comma is needed in “i.e.,”

Results and discussion
L375: Here and elsewhere in the results and discussion the word toxin is still used when it is probably not the appropriate descriptor. I suggest carefully editing the manuscript to ensure that the word toxin is only used when referring to a compound that has a toxic effect in vivo.

Table 3: This table is quite large and could be moved to the supplimenry material if space limited.


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: GENERATION OF HUMAN LIVER ORGANOIDS FROM PLURIPOTENT STEM CELL-DERIVED HEPATIC ENDODERMS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors describe how peripheral blood-derived HuiPSCs can differentiated into hepatic endoderm.
It is basically a method paper with no further development or applications to address biological or molecular questions.
Most findings are morphological, while describing hepatic endoderm, hepatoblast and hepatocyte phases.
To make this kind of paper acceptable at least a single cell characterization or a geographical distribution of specific proteins by histochemistry or fluorescence should be done. what shown in fig 3 is not sufficient.
Experimental design: Very basic experimental design
Validity of the findings: I do not find convincing evidence of novelty or advancement of knowledge by this paper
Additional comments: I suggest to use the organoids to make functional studies with other cells or proteins, run single cells or matrisome 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: GENERATION OF HUMAN LIVER ORGANOIDS FROM PLURIPOTENT STEM CELL-DERIVED HEPATIC ENDODERMS
Review round: 1
Reviewer: 2

Output:
Basic reporting: look at general comments
Experimental design: look at general comments
Validity of the findings: look at general comments
Additional comments: The manuscript “Generation of human liver organoids from pluripotent stem cell-derived hepatic endoderms” by Kasem Kulkeaw et al. describes a method to generate liver organoid from human CD34+ hematopoietic cell-derived iPSCs. This issue is interest and update and the proposed technology gives the possibility, in the future, to generate human liver organoids with a less invasive procedure, i.e. a simple blood test. These findings are considered to be interesting and of potential clinical importance, the manuscript is well written and the data are clearly described. However, in my opinion, the authors show results that do not justify several of the conclusion that they reach.

General criticisms:
-In order to demonstrate that the generated organoids are differentiated, authors should evaluate liver marker expression at both mRNA and protein levels and/or by immunofluorescence in a quantitative manner and not only by standard PCR. In Figures 1E and 3D the authors should evaluate and provide the percentage of ALB positive cells calculated on many cell fields or by FACS, and this analysis should be accompanied by quantification of the albumin secreted in the medium. Also the decrease of staminality markers, such as OCT4, should be evaluated during the differentiation process. Accumulation of glucose and other metabolites should be evaluated during the differentiation process (in a time corse) in 3D cultures.
-The method developed by the authors is simpler and less laborious than those described so far because it provides the use of iPSCs differentiated in hepatic endoderm alone without co-culture with endothelium and mesenchyme. Anyway, the mesenchymal cells (fibroblasts and vascular endothelial cells) dynamically interact with differentiating hepatocyte cells to promote further differentiation and provide an extracellular microenvironment. In this regard, it would be interesting to evaluate whether the human hepatic organoids generated by the authors maintain their mature hepatic characteristics over long-term culture. Also discuss this aspect in the discussion.
Minor points:
-In each figure indicate how many experimental replicates have been made
-lane 179: The reference indicated by the authors describes the HuiPSC MUi009 cell line, not HuiPSC MUi019. Replace with Stem Cell Res. 2017 Apr;20:91-93. doi: 10.1016/j.scr.2017.02.013. Epub 2017 Mar 7. Generation of induced pluripotent stem cells from peripheral blood CD34+ hematopoietic progenitors of a 31year old healthy woman. Tangprasittipap A, Jittorntrum B, Wongkummool W, Kitiyanant N, Tubsuwan A.
-Figure 1: replace G with F in the last panel. Repeat PCR for actin with fewer cycles
-Figure 1G and Figure 3D: please provide the individual immunodecorations (alb., CD81, Dapi).


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: GENERATION OF HUMAN LIVER ORGANOIDS FROM PLURIPOTENT STEM CELL-DERIVED HEPATIC ENDODERMS
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1.	The manuscript is clearly written and is comprehensible. The introduction is sufficient to orient towards the aims and objectives of the work.
2.	The raw data supplied is not well-labeled.
3.	The resolution of main figures is perhaps low, enlarging the images compromises their quality.
Experimental design: 1.	The research question is well-stated but given the amount of research going on in this field, more rigorous investigation needs to be performed as elaborated below.
2.	Under the methodology section regarding 3D culture of organoids (Line 157-165), the method is not detailed enough. The authors should elaborate how the 3D cultures were maintained for 17 days. Were the organoids passaged? Or was simply the top medium replenished? And how frequently?
Validity of the findings: Major comments:
The study though simple and rapid (as claimed by the authors) suffers from some serious drawbacks, which should be addressed to rightfully claim the overall ingenuity of the work.

1.	There is no statistical analysis of the work performed. The authors have not mentioned how many time the organoid culture was repeated which would indicate the reproducibility of the data. There is no mention of the repeats for RT-PCR data analysis or immunofluorescence or glycogen accumulation.
2.	One important issue is that the data is only qualitative but not quantitative. This again questions the reproducibility of the data. The authors can perform quantitation of RT-PCR gels and the number of repeats can then be represented graphically or numerically with standard deviation and other statistical information.
3.	In the discussion, the authors have claimed the rapidness of their technique by comparing it to that of Mun et al., 2019. It is mentioned that Mun et al achieved spherical structures at day 22 of their culture. I would like to draw attention that the 22 day period in Mun et al paper includes all the stages of differentiation starting from Pluripotent stem cells. I f we take into account the initial stages then for the present paper it will be 10 days for reaching Hepatic endoderm and additional 12 days in 3D culture making it a total of 22 days when they see the spherical structures typical of blastocyst and then require additional 5 days to for maturation. How would you justify the rapidness?
4.	Also to justify maturation of organoids the authors rely only on Albumin and Cd81 immunostaining. The characterization of the organoids is not rigorous enough. The authors should do some additional experiments to justify the qualitative efficacy of their protocol as suggested below.
5.	Should perform Cyp activity assay or AAT/albumin section in medium to show full functional potential of the hepatocytes.
6.	The authors did not show glycogen accumulation in the organoids.
7.	There is no comparison of expression data to positive control like human liver tissue or primary hepatocytes to assess/compare the extent of maturation.
8.	As can be seen from figure 3D, not all cells in organoid express albumin or CD81, the authors should perform FACS analysis to depict what percentage of organoid cells are mature hepatocytes. This is important if the authors claim to achieve successful generation of liver organoid. It would be great if they are also able to assess the organoids for ductal epithelial cells and endothelial cells using FACs.
9.	An important point would be to highlight how the 3D cultured organoids are superior to the 2D differentiated hepatocytes. It can be emphasized by showing a comparison of hepatic and ductal markers in the two along with a positive control such as primary hepatocytes or human liver tissue as well as comparison of functional assays between the two.
10.	I know that the supplementary figures are the raw data for the RT-PCR data shown in Figure 1D, I still feel that the supplementary data should be sufficiently labeled, specially the DNA ladder information is missing. The base pair information of individual bands of the ladder must be indicated. Also the expected amplicon size for each primer set should be mentioned either in the primer sequence table or along with raw data.
Additional comments: 1.	The referencing syntax used is not consistent throughout the text. I think it would be appropriate if all references being mentioned at a particular instance are grouped within single brackets.
2.	An important error is the discrepancy in cell-line name. At line 110, the cell line mentioned is MUi009 while in the rest of the text it is referred to as MUi019.
3.	The table number is incorrectly indicated in text at line 153 as Table X. I couldn’t find table X in the file.
4.	At line 154 in methodology section, it is mentioned that the glass slides were covered with a glass slide. I believe the mounts are normally covered with coverslip, unless it was indeed mounted with another glass slide in this case.


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: GENERATION OF HUMAN LIVER ORGANOIDS FROM PLURIPOTENT STEM CELL-DERIVED HEPATIC ENDODERMS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This version of the manuscript is significantly improved and the authors have addressed all the issues raised in the first revision. I believe that the revised manuscript is appropriate for publication in Peerj.


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

Input:
Title: USING TRACE ELEMENTS TO IDENTIFY THE GEOGRAPHIC ORIGIN OF MIGRATORY BATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The goal of this work was to use the trace element composition of bat fur to infer geographic origins.  The paper is well written, logically organized, and should attract interest.  That said, I’m concerned about a number of issues.  First, the scale of the geochemical data.  As the authors point out, the original surveys were very coarse (one site per 1600 km2) and this seems to present a major mismatch with respect to the objectives, especially when precision is interpreted at the 10’s of km scale.  Further, the geochemical data surface is very different than the hydrogen isotope isoscape, which has much better data density and interpolation heavily based on known relationships (i.e. orography, elevation, etc.).  Such constraints on geochemical data are likely lacking.  Second, the training data (fur) seems very limited in both density and space; the actual sample size is never mentioned.  Additionally, the relationship between fur and soil is very weak, with the highest R2 explaining about 15% and only three elements yielding significant R2 values (most with very low R2 values).  Lastly, I’m concerned that the input functions for elements into fur were all treated similarly and this is likely problematic.  In other words, some elements bioaccumulate to a greater extent than others (for example, Ni accumulates more than Hg).  And to bring this back to hydrogen isotopes, the input function is used in assignment models.  I do note, however, that the authors disclose all of these problems early on in the results section and then adopt a multivariate solution to assess assignment accuracy and precision.  Despite the design issues, I do think this is worthy of publication because it highlights the knowledge gaps surrounding the use of elemental data for assignment purposes.  My recommendations are to discuss i)  the coarse spatial resolution of the geochemical data and how that might impact the efficacy of using such data for assignment purposes (this was not discussed, yet the early results demonstrate the problem in my opinion) and ii) better address the elemental input function issue (Al, Ba, Cu, Fe, Mg – three of the five are essential).
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: USING TRACE ELEMENTS TO IDENTIFY THE GEOGRAPHIC ORIGIN OF MIGRATORY BATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper sought to use trace element analysis results from fur samples taken from bats to assign origins (e.g. location of fur growth) to individual bats. The eventual goal is to use this technique on unknown-origin migrants, but this paper focused on developing and ground-truthing the method using known-origin samples. Results were promising, with the trace element profiles of the fur samples corresponding with those of previously taken soil samples at the location of fur growth. Assuming a probability of origin threshold of 0.5, bats could be assigned to their location of origin about 80% of the time and the total area from which bats may have originated was decreased to about half of the species total range.

The paper was fairly well written with a clear list of goals. There were some unclear parts and a quite a few small typos, which I itemize in the general comments section below. The introduction provided an appropriate and thorough background on the subject matter. The figures and tables were well done, although I do not understand Figure 4. It is not clear to me what it is showing and so I cannot comment on whether it is necessary; the caption needs to be clearer.

In my opinion, the discussion is the weakest part of this otherwise very strong paper. I thought that several parts of it could be removed. For example, the whole paragraph on assumptions about the timing of fur growth really repeated what was in the introduction and didn’t need to be there. Also, the paragraph talking about previous studies on genetics basically concludes that so far, we can’t use genetics at all to assign origins to members of the study species. This could have been summarized in one sentence. I think the section talking about the impact of diet on the trace element composition of tissues and the section talking about the future utility of combining multiple origin assignment techniques are the most important parts of the discussion. There could be more on diet – currently only one paper is cited that talks about the diet of the study species and one other species and this paper is quite old. Much more work has been done on dietary preferences of these species since then. Could the authors elaborate on the findings of this more recent work and talk about specifically which trace element measurements might be impacted by a broader diet? What about in other species?
Experimental design: The research questions are well defined and explicitly stated. The introduction makes clear how the study is contributing to filling a significant knowledge gap (adding to the scant literature about trace elements in bat fur, using these data for origin assignment). To my eye, the statistical approach was extremely rigorous and clearly explained. The paper worked through four separate statistical processes and these seemed logical and according to best practices based on my own experience, which has mainly been working with origin assignment models based on stable hydrogen isotope results.

My one criticism is that I found the methods/results explaining the linkage between fur and soil trace element profiles to be very confusing. The methods state that linear models were used to make this link and in the results, I see that there were no strong relationships between individual trace elements in fur and soil. The results then go on to describe the results of multivariate analyses and I’m a little fuzzy on the details (line 277). I understand that PC1 scores were used to summarize the trace element profiles of the fur samples. Were sPCA analyses also done on the trace element profiles of the soil samples? Were the linear models looking at the relationship between PC1 of fur and PC1 of soil? Or am I misunderstanding? I would appreciate this being explained more clearly.

With respect to ethical considerations, the paper should state that the Smithsonian Museum approved the present use of their samples for trace element analysis (as the paper indicates that fur samples were taken for a previous project in 2014 on stable hydrogen isotopes and museums often approve destructive sampling of specimens for specific projects and require additional explicit permissions if those samples are to be used for other projects).
Validity of the findings: All data are provided, but I have a suggestion: I really like figure 3 in the manuscript and recommend it be retained as it is, however in the spirit of sharing all data (as requested by PeerJ), the authors might consider providing maps like the ones in figure 3 for all individual bats in the study (in a supplemental file). The conclusions are appropriate. Based on my own experience, analyses appear well done, but I do not have experience in trace element analysis and cannot critique the description of the laboratory techniques.
Additional comments: Overall – Personally, I do not like the term “tree-roosting bats” to refer to the trio of bats that are the focus of the introduction (eastern red bats, hoary bats, silver-haired bats). There are many other bat species that roost in trees and in many instances where the focal species have been found roosting out of trees. I realize that “tree roosting” is a fairly common term in the context that the authors are using it, but I’ve seen pushback on this terminology in other places and I tend to agree. I would recommend simply referring to “migratory bats in North America”. I’ve also seen “latitudinal migrants” used (to differentiate from hibernating species who may migrate in all directions), but more recent work looking at the movements of these three species even suggests that “latitudinal” is an oversimplification.
Line 19 – I think “source” should be plural
Line 39 – You might consider citing Rodhouse et al. (2019) here as well, as they come to similar conclusion.
Line 45 – I would clean up the sentence that states that “most bats that die are migratory”. In fact, I don’t think there is a lot of direct evidence that bats that die a wind energy facilities are migratory (cite the few papers that do demonstrate this). The main evidence for the bulk of the mortality being migrants is the timing of the mortality: during fall the migratory period. Be precise in wording: e.g. “Most bat mortality occurs during the fall migratory period and many of these individuals are likely engaging in migration.”
Line 52: In talking about migratory animals, it is very important to use clear and replicated terminology throughout. For example, here, the use of “local populations” is not clear. In the context of this paper, “local” is referring to animals at their summer site of residency (e.g. where they grew their fur). But they could be called “local” to other places at other times of the year. Include an explicit definition and use throughout.
Line 56: Remove “or are”
Line 60: “goals” should be plural here, I think.
Line 75: This seems like an improper use of “relative”. Reword?
Line 80: What is this list of references demonstrating? Just paper that have looked at “migratory tree bats” using stable isotopes (in which case Fraser et al. 2012 should be replaced with Fraser et al. 2017) or all papers looking at bat migration using stable isotopes (in which case many references are missing – much of the work from Dr. Voigt’s lab, for example)?
Line 103: Similar to my comment about line 52 – clarity is needed in the wording here. When you are referring to “sourcing” bats, what time frame is being addressed?
Line 152: I am not at all familiar with the details of trace element analysis and found this confusing. If some of the concentrations of some of the trace elements are calculated/inferred based entirely on the concentration of other elements, then what are these secondary (inferred) element results adding to ultimate analysis that isn’t already provided by the primary (measured) ones? I don’t doubt that this method is appropriate, but I would appreciate a little more explanation.
Line 172: I recommend adding a #5 here (or maybe adding to #4) stating that the paper assesses the accuracy and precision of the origin assignments.
Line 169/170, 173: I think it is more appropriate to say that the study is assessing variation “among” individuals as opposed to “in” them, as “in” suggested intra-individual variation.
Line 229: I think this reference should be Fraser et al. 2017
Line 269: Change “between” to “among”
Line 294: Change “is” to “are”.
Line 312: Awkward sentence, reword
Line 322: I think it is inferred, but I recommend explicitly stating that all precision measurements are based on >0.5 probability accuracy threshold.
Line 333: Grammatical error here, reword
Line 354: I recommend stating somewhere in the paper the dates when the bats that were sampled were collected. I think that the readers are referenced to the Pylant paper for this info – it would be more convenient to have the dates in the present paper.
Line 370: Change “use” to “using”
Line 388: Awkward wording, reword
Line 396: Some words missing here.
Line 418: Change “combing” to “Combining”
Table 3: I’m uncertain about what is going on with the samples that had a 0 probability of being from the collection location and 0 precision. The table says they were “incorrect”. Is this experimental error? If these results are real (e.g. trace element results are correct), then what is going on? It might be interesting to mention these two points in the discussion.


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

Input:
Title: USING TRACE ELEMENTS TO IDENTIFY THE GEOGRAPHIC ORIGIN OF MIGRATORY BATS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This papers deals with the use of trace elements for assigning the likely spatial origin of bats killed at wind turbines in the US. Previously, geographic assignments were mostly conducted via the use of stable hydrogen isotope ratios in fur keratin. Here, the authors used a novel approach by analyzing trace element concentration in bat fur. Overall the paper is well written. It is widely assumed that trace elements show up in consumer tissue without any offset compared to the baseline enrichments of food items. The authors make the point that their methods allowed the assignment of 80% of the carcasses, while reducing likely geographic locations in half.
Experimental design: It would have been instructive to do a spatial analyses based on stable hydrogen isotope ratios in fur keratin to see if the maps look similar, or to assess which of the approaches provide a more fine-scale resolution.

Line 135: the authors should specify from which part of the torso they collected fur. Previous molting studies focused mostly on fur from the interscapular region of the back. If authors varied in the area from which fur was collected, they may vary in the time period of molt as well, since this is specific for specific parts of the body.
Validity of the findings: Line 195: For geographic assignments, the authors created basemaps by extrapolating values. Usually, the  method of choice is some kriging approach. they need to specficy this. Importantly, the authors' approch does not take intra-site variation into account. Reference sampling sites are unknown, which could simulate a fine-scale resolution. yet this might be an artefact of ignoring intra-site variability.

Line  244: the authors chose a 50% cut-off point for accepting a geographic assignment as correct. This approach is not very conservative and thus error-prone. A higher cut-off point of around >80% seems to be more desirable from my point of view.
Additional comments: The paper starts with some alarming numbers that in Northamerica about 70 bats are killed per year and wind turbine. This is a very high number indeed and suggests that populations of affected bats will likely collapse at some point soon. The authors need to provide good documentation for these numbers.

Line 43: the authors should specify that they are talking about the Northamerican scenario. Obviously, other species of bats are affected in Europe, Latin America etc. The authors should go through their manuscript and check if they make generic statements for bats, but mean Northamerican bats. They should specify which geographic background they are referring too, since PeerJ is an international journal (not the Midwestern Naturalist) and therefore it is read by an international readership. I suggest to broaden the geographic focus by citing international papers.

In the introduction, the authors should double-check if they considered all publications on bats and trace elements. One paper about mineral-drinking bats from the Amazon comes into my mind (Ghanem et al. 2013 Journal of Tropical Ecology; Hernout et al. 2016 Chemosphere, 2016 Environmental Pollution; Rahman et al. 2020 Environmental Chemistry and Ecotoxicology among others). I am sure that there are others and therefore, it would be good to review the literature on this topic in some additional section of the introduction.


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

Input:
Title: USING TRACE ELEMENTS TO IDENTIFY THE GEOGRAPHIC ORIGIN OF MIGRATORY BATS
Review round: 2
Reviewer: 1

Output:
Basic reporting: NA
Experimental design: NA
Validity of the findings: NA
Additional comments: The authors did a fantastic job of reconciling all reviewer comments.  The manuscript is much improved and should be of interest to those studying bats as well as those interested in the topic of geographic assignment.  Well done.


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: SPATIOTEMPORAL EXPANSION OF HUMAN BRUCELLOSIS IN SHAANXI PROVINCE, NORTHWESTERN CHINA AND MODEL FOR RISK PREDICTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: This is an interesting and important paper. In terms of content it is well written and makes an important contribution to the body of work on brucellosis and public health.
Additional comments: The manuscript is well written. Some grammar, however needs to be checked: For example:
Line 26, grammar – with more than 90% of these cases were reported in the northern – “were” needs to be removed
Line 52 – please remove “allergic” as this brings a different connotation
Line 54 and 55 – what is common about clinical presentation of brucellosis is the undulant fever and not necessarily asymptomatic as the author puts it. Please revise this
Line 62 – please replace animal husbandry to livestock keeping.
Line 63 -64 – there is problem with grammar, “including many countries in Latin America, Middle East, and South and Central Asia, which occurred more than 64 500,000 cases every year”. You may consider breaking this from line 62 at livestock keeping.
Line 65 – “with more than 90% of these cases were reported in northern” – remove “were”
Line 66-67 – the author mentions the: apparent geographic expansion” but does not follow up to say a bit more about what this is. So the statement is just hanging


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: SPATIOTEMPORAL EXPANSION OF HUMAN BRUCELLOSIS IN SHAANXI PROVINCE, NORTHWESTERN CHINA AND MODEL FOR RISK PREDICTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors conducted a retrospective epidemiological study in Shaanxi Province from 2005 to 2018 to explore the association between meteorological factors and transmission of human brucellosis according to differences in geographical distribution and seasonal fluctuation in northwestern China. In China, the affected area of brucellosis did expand from northern pastureland provinces to the adjacent grassland and agricultural areas, then to southern coastal and southwestern areas. The findings may be used to predict the seasonal fluctuations of human brucellosis and to develop target prevention and control strategy in the study area.
Experimental design: Line 116, in the part of 'Data collection', given that there are several temperature indicators provided by the Chinese Bureau of Meteorology (http://data.cma.cn/), the authors should indicate the exact temperature index involved, e.g., average air temperature or maximum air temperature.
Validity of the findings: Only one row of data cannot form Table 4, thus there is no need to indicate the GAMM model result in the format of table, text description is enough.
Additional comments: The following typos should be corrected.
1) Line 171, 'Zizhou country' should be 'Zizhou county' ;
2) Lines 187, 244 and the legend of Table 3, 'lag times' should be 'lag time';
3) The article number for reference [2] should be added.
4) Title page, the authors should check the second affiliation of First author, now it is indicated as 'Centre for Disease Prevent and Control ……'，is here 'prevent' should be 'prevention'?


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: SPATIOTEMPORAL EXPANSION OF HUMAN BRUCELLOSIS IN SHAANXI PROVINCE, NORTHWESTERN CHINA AND MODEL FOR RISK PREDICTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: All of my concerns have been addressed properly in the revised manuscript.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: According to my knowledge of PeerJ, the references should be arranged in alphabetical order of the first author of each article.


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: CHEMICAL PATTERNS OF COLONY MEMBERSHIP AND MOTHER-OFFSPRING SIMILARITY IN ANTARCTIC FUR SEALS ARE REPRODUCIBLE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is exceptionally well written and appropriately structured, making it very easy to read and understand. The text flows well and the concepts are thoroughly explained. The knowledge of the authors on the background of the study is evident and the references are appropriate and up to date.

Below I have listed a few minor comments about the background and the general outline of the publication that I hope the authors will find the following useful in improving their manuscript:

At the moment, the introduction and therefore the framing of the whole article is focused on replication.
1) Please rephrase the title to reflect this more. After reading the current title, I expected a very different introduction to the article, which was slightly confusing at the beginning.
2) I fully support replication studies and consider them an extremely important part of research, as outlined in the introduction. However, the article seems to have two separate goals: a) replicating a subsection of results presented in Stoffel et al. 2015 and b) adding additional information about chemical profile differences among colonies. Adding original results to the study (and their discussion) causes the replication section to lose importance, as it creates the feeling of a side research project that was difficult to publish due to the lack of novelty and was then restructured into a study highlighting its replication aspect. I realise the difficulties of publishing replicated studies and wanting to publish all available results, however I think the paper would benefit if just one, clear aim was presented – the replication study. The analysis is well executed, well explained and provides enough content for a publication and can be used as guide for future studies of this sort. The additional results, presenting chemical profile differences among multiple colonies, are interesting and worth publishing. However, I think it would be better to publish these as a standalone short article or note.

L54-62: Rather than providing quotes from the referenced papers, please summarise and rephrase the content, leaving just the reference at the end of the sentence.

The current introduction contains 5 paragraphs on replication. While most information is relevant to the current study and revisited in the discussion, paragraphs 4 and 5 could be made more concise.

L101: Please remove the abbreviation - it is not used later

L133-140: Please also mention the inconsistencies/lack of appropriate reporting/lack of automated (and therefore reproducible) peak detection and alignment methods. This creates many inconsistencies and difficulties in replicating results using GCMS data.
Experimental design: The experimental design followed the excellent study of Stoffel et al. 2015 and have no major concerns regarding it. The authors also clearly pointed out how it differed from the original paper and how that could have affected their results, which I greatly appreciated.
The code and raw data from the original as well as the replicated study are made available making it transparent and reproducible.

Minor comments:
L192-193: Were mother-pup pairs caught at the same time/on the same day/when together? If they were, the mother-offspring similarity found in the study could be a result of animal touching and transferring compounds from one another directly prior to capture and may not be a reflection of ‘stable’ similarity.

L228: Why was the PERMANOVA based on 99999 permutations? This seems like a lot. The default and what is used in most publications is a lot less. Did lower permutations result in insignificant values?

Table 1c: It seems that you re-analysed the raw data of Stoffel et al. 2015 using a PERMANOVA. Please add this information to the text. Did you also realign the raw data using GCalignR (to keep it consistent with your analysis)?

L237: It is not clear what you mean by ‘we did not re-align the dataframe of Stoffel et al.’. Do you mean that you did not use GCalignR and kept the original alignment? If so, please make this clear (as it is not stated that you realigned the data from the original paper for the PERMANOVA in Table 1c (see above)).

Supplementary materials: the code that was provided imports data with peaks that are already aligned. It would be useful to provide the code for aligning peaks in the supplementary materials (rather than just the github repository) or briefly describing how this was done in the text.
Validity of the findings: As mentioned before, I agree with the authors that replications studies are important and needed. In the field of ecology, this may be particularly difficult, and I commend the authors’ effort of collecting an impressive dataset and conducting this analysis again. The rationale and benefit of this research is clearly stated and the methods are well developed and sound. The discussion is well explained and flows well.

I have only one major concern with the interpretation of the results – the significant result of the test for homogeneity of group variances (L274-277). This result could mean that the significant results of the PERMANOVA are actually an artefact of differences in within-group variability, rather than between group differences, which is a problem and theoretically puts the entire results into question. In lines 267-278 you mention a post hoc test – this is not included in the code in the supplementary materials. Considering these are the main results of the article, I would like to see more justification and support of why you think significant results of the betadisper analysis do not indicate issues and potential unreliability of the results of the PERMANOVA as well as explanation for considering the post hoc test results more reliable than the original test.

A few minor comments:
Since you included age in your model, you may consider running betadisper for scent_factor$age

Figure 2B – There are a lot of colours and shapes making it difficult to find pairs. Please make this plot clearer, maybe by adding lines connecting mother-pup pairs. You could then merge 2A and 2B into one plot, by keeping the colour and shapes of 2A and connecting mother-pup pairs with lines.

L291-296: As mentioned above, I think the replication study is enough for this publication and this section could be left out.

L382-387: This statement is too much of a reach. Just because mother-offspring similarity and colony differences persist does not mean that this is related by microbiota. While this may be true and your findings do not contradict this possibility, what you have shown in this study does not relate to this enough to bring this up, please remove.

L402-403. There are a lot of other factors that may play a role in this and there is no need to make broad speculations. Especially since the main goal of the publication was to replicate a study. Please remove.

L405-425: This was not within the scope of the study and I do not see the need to discuss it here. Considering that the main body and framework of the study focuses on replication of results, the whole section on mechanisms is more appropriate in the discussion of the original paper.
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: CHEMICAL PATTERNS OF COLONY MEMBERSHIP AND MOTHER-OFFSPRING SIMILARITY IN ANTARCTIC FUR SEALS ARE REPRODUCIBLE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is very well written and a pleasure to read. The authors have provided ample background, both of the issue of replication and of pinniped olfactory signatures. The article is well structured and the methods are clear. The results relate directly to the hypotheses and the conclusions are well supported.

Specific comments:
The reference to Ling on line 146 appears to have a typo in it.
In the reference list, some of the binomial names are not italicised.
Experimental design: The research question is well defined and very relevant. Chemical ecology is a developing field with many different methods being trialled by different labs and the reliability and comparability of those results have not yet been established. This study is an important step in showing that, at least using the methods of Stoffel et al., findings are robust and reproducible.

One additional detail I would request in the methods is the duration of time from sample collection to freezing, and the length of time samples were stored before analysis. This is not a critique of this study, but a detail that I think is useful to other researchers as the stability of chemical samples post collection is poorly understood and providing this information establishes a benchmark.
Validity of the findings: The authors have taken great care with the statistics in this study. The results are clearly presented and the conclusions are supported by the results.
Additional comments: Thank you for this very interesting paper. It provides both important findings about pinniped chemical communication, and about methodological approaches.

I find it interesting that Johnsons Cove and Natural Arch were similar to each other (as they are the furthest apart), while LB, SSB and FWB were all different yet close to each other. It is probably beyond the speculation of this paper, but it will be interesting to see more investigation in the future into the drivers of similarity (or diversity) between colonies and individuals.

Given this study was a replication of Stoffel et al, it isn't appropriate to introduce new methods, but with the potential environmental influence in mind, have you considered testing environmental control samples? Wierucka et al., used environmental controls in an attempt to remove some of the contribution of other odour sources in the colony. Given these methods are relatively new, it would be good to determine if such controls are necessary, and/or if they contribute to our understanding of the sources of diversity among colonies. Again, this is probably beyond this paper, but a potential avenue of future research.


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: CHEMICAL PATTERNS OF COLONY MEMBERSHIP AND MOTHER-OFFSPRING SIMILARITY IN ANTARCTIC FUR SEALS ARE REPRODUCIBLE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Thank you very much for this new and improved version of the manuscript. I am happy with the changes made with regard to my comments about the experimental design and validity of findings. I especially appreciate the additional analyses conducted to explore certain topics in depth. I believe that the reworked sections of the introduction make it clearer why the two parts of the paper were combined.


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: PHOTOSYNTHETIC PERFORMANCE AND STEVIOSIDE CONCENTRATION ARE IMPROVED BY THE ARBUSCULAR MYCORRHIZAL SYMBIOSIS IN STEVIA REBAUDIANA UNDER DIFFERENT PHOSPHATE CONCENTRATIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: Report on ‘Phosphate modulates arbuscular mycorrhizal symbiosis and improves photosynthetic performance and stevioside content in Stevia rebaudiana’

This is a very well written, clear manuscript, that builds on those of  the cited publications of Mandal et al. Vafadar et al., Tavarini et al. It deserves publishing because it provides evidence for the type of colonisation structure, for the mode of uptake of PO4 and usefully links the data on photosynthesis [fluorescence and pigments] with growth and SGs [but see my comment below ref Reb-A and stevioside concentrations.
A number of small issues need to be addressed, and then I believe it will be suitable for publication.
I have annotated the text [attached], and herein indicate some of the more important issues that must be addressed.
Title: as it read it implies that phosphate improves photosynthetic performance and stevioside… so either add ‘the latter’ or rewrite completely.
Also, I disagree with the use throughout of ‘content’ when indeed the authors mean concentration’ For content = concentration * mass, and at no time is mass information given in the text. So, change all uses of ‘content’ to ‘concentration’ [except of course in the references!].
Line 52 Rhizoglomus irregulare or Rhizophagus irregularis I am not an expert on this but ensure the correct one is used.
See line 97, do not start a sentence with an acronym [and define at first use in the text [separate from the Abstract].
Likewise, Line 117.
A little more detail in line 138.
Line 345 any reason the root fwt was higher in M+ than M- at 1000 µM?
Line 383 compared to what..? Be explicit.
Line 460 indicate if significant or not.
Lines 497-509 need some clarification. For a start, Reb-A is more preferable from a taste perspective than stevioside, and indeed the total SGs is the same with or without M+ at 200 µM. So this needs some extra discussion. And reconcile lines 499 and 505/6.


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: PHOTOSYNTHETIC PERFORMANCE AND STEVIOSIDE CONCENTRATION ARE IMPROVED BY THE ARBUSCULAR MYCORRHIZAL SYMBIOSIS IN STEVIA REBAUDIANA UNDER DIFFERENT PHOSPHATE CONCENTRATIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English version is acceptable, although some modifications are required.

The literature references are not always referring to the original literature, e.g., for the Synthesis of steviol which has been published by Totté et al. already in 2000

The structure of the paper is OK

The results are sometimes rather weak, due to the lack of repetitions of the whole experiment.
Experimental design: The intention of the authos is good, but the way that they organised the experiment is not. Only 6 plants per treatment were used, but interesting information on the plants is missing, e.g., the number of leaves, the position of the leaves that were used. It is not reported whether the leaves were dried or not, the amounts used for the extractions are not always given.
It is not reported that validated methods of analysis were used. Not sufficient information is given to repeat the experiment.
Validity of the findings: It is a good point that the authors used microscopic techniques to see what happens within the plants. However, no information is given on the number and/or condition of the chloroplasts, which are the starting point of SG biosynthesis.

In some figures, some outlyers are visible, probably due to sampling methods and/or lack of repetitions of the experiment. (e.g., Fig; 3, 500 µM with colonisation; Fig. 7: A control.
Additional comments: The authors studied the colonisation of mycorrhiza in Stevia. This part of the work seems well-done.
PreIn the introduction, original research papers should be cited, e.g., the first report of the synthesis of steviol by the MEP pathway is by Totté et al. (2000) Tetrahedronn lett. 41, 6407-6410 (not: Tetali 2019). The mention of SGs in Stevia is not from Wölwer-Rieck (2012), etc...
1) Stevia is not an easy plant to work with.
2) The experiment is done only once, and per treatment 6 plants were used. No repetition of the experiments has been done. Therefore, the results reported should be considered as preliminary as more experiments should be done.
3) The number and size of the leaves are not given.
4) Were the leaves used as such or dried before the different extractions? How exactly was the leaf sampling done for the measurements in the different assays? How much material was used?
5) line 182: why is the amount of P and Mg given as a percentage, and not just µg/g fresh weight?
6) line 186: how was the leaf tissue sampled for the pigment analysis? Dry or fresh wt?
7) Extraction of SGs: What is the quantity of leaves extracted (dry or fresh weigth)? Were 3 extractions done on 3 different (weighed) amounts? As shown by Ceunen & Geuns, Plant Science (2013), 198, 72-82, the photoperiod and leaf position on the plants is very important for the SGs content. To obtain the best results, it is advised to dry a huge number of leaves before and grind them to a fine powder. Thereafter, at least 20 mg dry powder should be extracted to avoid extracting a leaf coming from just 1 position of the plant. This should be done at least 3 times.
Was the method for SG analysis validated by the authors?
8) Figure 3 (growth) and Fig. 7 (ST and RebA). The authors did not check the number of chloroplasts in the leaves treated with 200 µM phosphate. Probably, the number did not change after 30 d treatment. The first steps of SG biosynthesis are dependent upon the chloroplasts. Therefore, results should be carefully analysed. The growth increase by 200 µM of about 70 %, and the decrease of Reb A content is about 50 %. Is it possible that the decrease just reflects the “dilution effect” of rebA concentration by the larger cell volume? Of course, for ST this is not the case, but the value for the control is extremely low. Is this due to the one-time experiment, the more as the ST content of the 200 µM treatment with colonisation, as well as of both 1000 µM treatment are not different? A similar problem might exist in Fig. 4 with an “outlyer” of Mg at 500 µM with colonisation.