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: TEMPORAL SHIFTS IN ENDOPHYTE BACTERIAL COMMUNITY COMPOSITION OF SESSILE OAK (QUERCUS PETRAEA) ARE LINKED TO FOLIAR NITROGEN, STOMATAL LENGTH, AND HERBIVORY
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment here.
Experimental design: Why did you use three leaves for functional measurements and five for endophyte characterizations?   Were the same leaves used for both functional and endophyte analysis?  Were the leaf samples evaluated independently?  If multiple samples were taken from branches and within trees and evaluated independently, this study is pseudoreplicated and the samples from each branch and tree should have been combined (I see that you did this properly for stomatal measurements).  But I feel that this is not the case for endophyte analysis, because the authors state that 45 samples were taken from only 5 individuals. This is important to specify.

Moreover, if all five individuals occur within a 15-m radius, your conclusions might be limited and potentially confounded, because conspecifics in closely spaced habitats can share microbes, even endophytes that disperse on the leaf surface and ultimately gain access to leaf interiors (Griffin & Carson 2015).
Validity of the findings: The Results and consequently the Discussion sections are too short and do not offer much insight on detailed taxa-specific results and how these results may impact plant hosts and tree populations at larger scales.  Sure, one would expect that bacterial community (richness?  What about entire community structure?) changes with season, but which particular taxa drive these differences?  What is known about these taxa?  Are they pathogens, mutualists, are they correlated with herbivory or potentially have effects on other trophic levels and ultimately plant performance?  The ecology of the results and how they are important are needed.

And what temporal-plant functional trait interactions are there?  For instance, it appears that endophyte communities are particularly structured by stomatal length (SL) in spring (Fig. 2).  There are many other trends to speculate and explore in the Discussion.  This type of synthesis is needed and will greatly increase the quality, scope, and contribution to the field.

It was quite surprising to see that even though the authors concluded that nitrogen content and herbivory were important in structuring endophyte communities, there was little mention other than fixation of the potential physiological effects of nitrogen or herbivory.  What might be happening?  This should be explored further in the Discussion and possibly even mentioned in the Introduction.  For a starting point, look at Dordas 2008 review from the agricultural literature about nutrients.  What are the herbivores in the system, and how are ways herbivores drive endophytes?  Are they vectoring bacteria among plant hosts? See recent paper by Vannette & Fukami (2017) or reviews by Biere & Bennett 2013 and Griffin & Carson 2015.

Overall, this paper is skeletal and needs a lot more meat, particularly in the Discussion.  These are good results and the authors should do this paper justice by discussing some of the important implications of the findings.
Additional comments: This study aims to determine the relative importance of temporal variation and plant functional traits in structuring bacterial endophyte communities of Quercus petraea.  The plant microbiome and the factors that structure these communities are timely important areas of research, particularly among forest trees.  While the scope of the study and the results are interesting, there are significant issues with the experimental design, scholarship, and overall skeletal prose of the manuscript.  My detailed comments are below.

Why did you use three leaves for functional measurements and five for endophyte characterizations?   Were the same leaves used for both functional and endophyte analysis?  Were the leaf samples evaluated independently?  If multiple samples were taken from branches and within trees and evaluated independently, this study is pseudoreplicated and the samples from each branch and tree should have been combined (I see that you did this properly for stomatal measurements).  But I feel that this is not the case for endophyte analysis, because the authors state that 45 samples were taken from only 5 individuals. This is important to specify.

Moreover, if all five individuals occur within a 15-m radius, your conclusions might be limited and potentially confounded, because conspecifics in closely spaced habitats can share microbes, even endophytes that disperse on the leaf surface and ultimately gain access to leaf interiors (Griffin & Carson 2015).

The Results and consequently the Discussion sections are too short and do not offer much insight on detailed taxa-specific results and how these results may impact plant hosts and tree populations at larger scales.  Sure, one would expect that bacterial community (richness?  What about entire community structure?) changes with season, but which particular taxa drive these differences?  What is known about these taxa?  Are they pathogens, mutualists, are they correlated with herbivory or potentially have effects on other trophic levels and ultimately plant performance?  The ecology of the results and how they are important are needed.

And what temporal-plant functional trait interactions are there?  For instance, it appears that endophyte communities are particularly structured by stomatal length (SL) in spring (Fig. 2).  There are many other trends to speculate and explore in the Discussion.  This type of synthesis is needed and will greatly increase the quality, scope, and contribution to the field.

It was quite surprising to see that even though the authors concluded that nitrogen content and herbivory were important in structuring endophyte communities, there was little mention other than fixation of the potential physiological effects of nitrogen or herbivory.  What might be happening?  This should be explored further in the Discussion and possibly even mentioned in the Introduction.  For a starting point, look at Dordas 2008 review from the agricultural literature about nutrients.  What are the herbivores in the system, and how are ways herbivores drive endophytes?  Are they vectoring bacteria among plant hosts? See recent paper by Vannette & Fukami (2017) or reviews by Biere & Bennett 2013 and Griffin & Carson 2015.

Overall, this paper is skeletal and needs a lot more meat, particularly in the Discussion.  These are good results and the authors should do this paper justice by discussing some of the important implications of the findings.

There were quite a few instances where the prose was not clear or grammatically incorrect.  I suspect that there were some difficulties in a language barrier.  For a future submission, I would recommend that the authors send the manuscript to a colleague whose first language is English for detailed comments.  I comment on (some) instances below.

Moreover, there were quite a few instances where important papers/citations were not used, or where more relevant and recent citations should be used.  This demonstrates a lack of scholarship, and makes the reader question whether the authors are up to speed on the literature.  See detailed examples below.

Recommended Title: Herbivory, nitrogen, and stomatal density structure endophyte bacterial community composition of sessile oak (Quercus petranea)

Line 43:  “In this sense…” What sense?  Incorrectly used
Line 50: Kembel et al. 2014 did not study endophytes
Line 54: Affect not affects
Lines 54-55: cite also Griffin et al. 2016, Griffin et al. 2017
Line 65: reviewed by Griffin & Carson 2015
Line 68:  Great point
Line 78:  I strongly suggest briefly outlining at least two hypotheses here.
Line 91:  Were branches randomly selected?
Line 93-94: I think there are some issues with the experimental design.  See my comments above.
Line 96:  “were” collected
Lines 108-112:  Citations for stomata counting and leaf herbivory?  Metrics for measuring herbivory have widely been scrutinized.  What are the enemies and their impacts among this species?  There is no natural history given here or even in the introduction.
Line 117: “Tween?”
Cite your protocols for surface-sterilization: Arnold & Lutzoni 2007, Griffin et al. 2016
Line 129:  I do not know much about ALISA, but after a quick search it appears that ARISA can either underestimate (multiple taxa sharing an ITS length) or overestimate (more than one copy of rRNA operon encoding ITS region).  At the very least, the authors should address this limitation with proper citations.
Line 206: cite Kembel et al. 2014 for phyllosphere bacteria, other citations needed
Line 207: also cite Doty et al. 2016 for N fixation in Populus
Line 220: need citation
Line 153: No information about how community structure differs, no info on particular bacterial taxa.  There is no biology here.
There is no discussion because there are no exploration of particular results.  What about particular taxa? What is herbivory doing?  What is time doing?
Line 215: over seasons rather than “along season”
Line 217: Impacts rather than impact
Line 220: needs citation
Line 223: This single sentence conclusion section is disparate and should either be expanded or incorporated into the Discussion.

How much variation is there within trees?  5 isn’t very well replicated for a microbial study.


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

Input:
Title: TEMPORAL SHIFTS IN ENDOPHYTE BACTERIAL COMMUNITY COMPOSITION OF SESSILE OAK (QUERCUS PETRAEA) ARE LINKED TO FOLIAR NITROGEN, STOMATAL LENGTH, AND HERBIVORY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall comments:
This paper suggests that temporal variation in bacterial assemblages is present within the leaves of sessile oak. The most interesting finding was that leaf herbivory was an important predictor of community divergence. I commend the authors on pursuing timely questions and presenting some interesting findings.

The main suggestions I have to improve the paper are:

1. The statistics employed do not appear to account for non-independence among samples imposed by temporal or spatial autocorrelation.
2. The introduction is very brief and does not give the reader much information regarding what to expect or why the study was performed. Providing more information here would make the paper read much better.

More detailed suggestions follow.

Title: The phrase “community structures” is somewhat vague. Perhaps using slightly different phrasing would be better.

Introduction
Lines: 36-37. This introductory sentence seems quite broad and somewhat inappropriate. Perhaps you could start by saying how not much is known about temporal variation in microbial assemblages (as you suggest in line 38). The appeal for interdisciplinary work seems unnecessary.

Second paragraph: no mention is made of the potentially harmful effects of endophytic bacteria. It may be worth providing a citation for the reader that shows how some bacteria likely interact antagonistically with their hosts.

Line 61: This sentence is unclear as written.
Line 69: This sentence seems to contradict itself, perhaps it would be best to rewrite.
Line 70 onwards: It may be worth setting up some expectations here for why certain plant traits may influence endophyte assemblages. For instance, perhaps SLA is important because it represents within-leaf habitat. Also, additional citations here would help many readers. Why do we think leaf age may be associated with shifts in endophyte assemblages?

Additionally, there is no information about why we should expect endophyte communities to vary with time, or the many studies that have shown temporal variation does exist for both endophytic bacteria and fungi. There probably should be a whole paragraph describing why temporal variation matters and setting up expectations.

Overall the introduction has some good background information but could be improved by better setting up expectations and justifications for your study.

Methods

Line 86: admixed does not seem like the best word here.
Line 137: Was a repeated measures approach taken when calculating the ANOVA to account for temporal autocorrelation? If not, then this should be performed.

Additionally, the statistics need to account for the highly nested nature of your data. You sampled multiple leaves from the same branch, and multiple branches from the same tree. These leaves are therefore not independent measurements and you will want to account for that statistically. A mixed effect model is an easy way to do this. Mixed effects models can be specified quickly in the R environment (see the lme4 package).

Line 140: the Bonferroni measure is very conservative. The Benjamini-Hochberg false discovery rate correction may be a better choice. It is possible that the greater sensitivity of the latter test might expand your inferences slightly.

It would be helpful to provide readers more information about the ARISA technique in the methods or introduction as I suspect many people will be unfamiliar with this method. Also the acronym is never defined.

Results

Line 156: I have used the phrase “community structure” in my own work, but have grown dissatisfied with the phrase because it is so vague. Could you perhaps say that “community composition” shifted?

Line 168: It is very interesting that herbivory was the most important predictor variable. I would like to see a bit more about this in the discussion if possible.

Discussion:

Line 173: The phrase “structure variations” was unclear to me. Perhaps reword.
Line 175: What do you mean by “robustness” here. Do you mean ARISA is a good way to detect large differences in community composition (as suggested by the citation)?
Line 177: Please reword slightly. I understood this sentence to mean that the bacterial assemblage differed in leaves removed from the trees in spring and autumn. Is that correct?
Experimental design: The questions addressed by the paper are timely and important. Not much is known regarding how plant traits affect microbes, or how microbial communities shift over time. The use of ARISA precludes taxon-specific analyses, but still provides some interesting insights.
Validity of the findings: The experimental design was highly nested with multiple samples taken from the same branch, and multiple branches from the same tree. There was no mention of how this was accounted for statistically, or how temporal autocorrelation was addressed. The statistical methods should be improved.

I would also like to see a bit more in the discussion regarding why herbivory may be linked to shifts in community composition. This was a very interesting result, but was not discussed in detail.
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: TEMPORAL SHIFTS IN ENDOPHYTE BACTERIAL COMMUNITY COMPOSITION OF SESSILE OAK (QUERCUS PETRAEA) ARE LINKED TO FOLIAR NITROGEN, STOMATAL LENGTH, AND HERBIVORY
Review round: 2
Reviewer: 1

Output:
Basic reporting: I commend the authors on adding a lot more useful content to their manuscript and reworking the statistical analyses. The paper is much improved. I have a few additional suggestions to consider. The most important suggestion is to be careful to not ascribe causality in cases where it cannot be determined due to the correlative nature of the data (see below).
Experimental design: Lines 175 onward: It is a bit unclear which set of leaves you sampled for herbivory? Did you look at the leaves that you sequenced or the leaves for which you measured traits, or some other set of leaves. Perhaps a sentence explaining this to the reader would be useful here.

Also, did you record each damage type as a categorical variable (i.e. either present or absent) or try to measure herbivory as a continuous variable (e.g. how much leaf was eaten)? I am guessing you used some continuous variable as you later mention that herbivory was a response in your linear mixed effects models. More detail here describing how you measured herbivory quantitatively and combined data from different types of herbivory would be helpful.

Line 226: The sentence, "Among the insect mediated damage types searched in our plots, the herbivory-mediated damage was due to the damage-types of hole feeding, margin feeding and sucking" is unclear to me. Do you mean that hole feeding, margin feeding, and sucking were the only types of herbivory observed?

Line 275: You say that herbivory was a significant association with shifts in endophyte assemblage over time as shown by CCA. However, it is unclear to me how "herbivory" was combined among the damage types observed? Was each damage type quantified in some way and these all added together? Why not analyze each damage type separately to gain additional insight?
Validity of the findings: The findings are interesting, but too much causality is ascribed in the wording of the results. The authors will want to rephrase sentences here and there to reflect the limitations due to the correlative nature of the data (see below).
Additional comments: Line 293 (and last line in abstract): Here you use the word "influenced" in relation to the association between stomata length and shifts in the endophyte assemblage. It would be better to be a bit more cautious here and perhaps use "associated" instead. Indeed, throughout the discussion it would be wise to make sure results are discussed as interesting correlations and avoid ascribing causality.

As another example, the last line of the abstract uses the word "drivers". Again, framing this result as an association or correlation would be more appropriate, as it is not possible to say if these traits cause the temporal shifts in the endophyte community or not. Any number of ecological contingencies shift from spring to autumn and would be associated with changes in the endophyte assemblage over that time period. Consequently, careful wording is necessary when discussing your interesting correlative results.

I suggest being more cautious in the conclusion statement as well. Your speculation that stomata and herbivory is important for endophyte colonization is well founded, and supported by your data, however much additional work will need to be undertaken before one can say what the "main drivers" of temporal change in endophyte communities are.

Even the title could probably be toned down. As an example: "Temporal shifts in endophyte bacterial community composition of sessile oak (Quercus petraea) are linked to foliar nitrogen, stomatal length, and herbivory" or something like that would be a bit more accurate given the correlative nature of the results.


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: BUILDING INTERPRETABLE MODELS FOR POLYPHARMACY PREDICTION IN OLDER CHRONIC PATIENTS BASED ON DRUG PRESCRIPTION RECORDS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Firstly, I congratulate to the authors! I consider that they had done a great work! Thank you for giving me the opportunity to revise this manuscript. I found this paper particularly interesting in terms of not only your focus of utility on an interpretable model of polypharmacy but in relation to any older chronic patients.

The authors present the differing aspects of your research in an appropriate way and this allows the reader to follow the study and understand the approaches, analysis and discussion of findings which are embedded within the aim of to build models for predicting polypharmacy for chronic patients.

I appreciate you will have put in a lot of effort in preparing your paper and there are a number of points which I offer to assist with further developing the manuscript. This points are listed under the subheadings.

Introduction:
1.	In line 19 appears the cite number “20” and in the line 40 appears the cite number “33”. I suppose that this is an error. Please, update the cites in order of apparition.
2.	Why did you focus on chronic cardiovascular disease and type 2 diabetes mellitus? Are they the most frequent? Are they the more associated to polypharmacy? I suggest that you explain it in the introduction section.

Methodology:
3.	In line 50 appears “The first dataset contained drug prescription records collected in Slovenia from 2008 to 2016” Can the authors explain what type of records contained? Did they belong to primary care, hospital or both?

References:
4.	Please, check the references! There are some references cited incorrectly.
5.	I think that your literature should be the most recent on this topic; there are 12 of 34 references belong to before 2012. Try to include the most up to date international literature!
Experimental design: You are building models for polypharmacy prediction in older chronic patients with a large sample of Slovenia older people, being very interesting for PeerJ readers.

The authors described with sufficient details all methods utilized.
Validity of the findings: I appreciate you will have put in a lot of effort in preparing your paper and there are a number of points which I offer to assist with further developing the manuscript. This points are listed under the subheadings.

Results:
1.	It would be interesting the authors offers a supplementary table with the demographic data of the participants.

Discussion:
2.	I suggest that you contrast your finding with more international literature.
3.	It would be interesting that the authors explain the implications of this study in the Healthcare system.

Conclusion:
4.	Could you identify future directions?
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: BUILDING INTERPRETABLE MODELS FOR POLYPHARMACY PREDICTION IN OLDER CHRONIC PATIENTS BASED ON DRUG PRESCRIPTION RECORDS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: First of all, I would like to congratulate the authors for the article that I find very interesting and important for the readers of PeerJ and for society in general, because with this prediction model can benefit the health of many people.
I am pleased with the opportunity to review the article and be able to contribute to its improvement in the observation of some data that could have created any doubt after reading it and could clarify me. I will detail them by sections:

Introducction:
It is observed that the citation does not follow a numerical order, since for example on line 40 it appears quote 33, on line 29 it appears quote 20 when it would not be the number that would correspond according to its order of citation

Methods:
- Is there a reason why the date of the data of the discharges included in the article is 2 years before the prescription data?
- What is the criterion that the "unique patients" have to have since from the total sample of 94,475,895 the unique patients are only 755,966.
- If the hospital discharges are a total of 174,061, how is it that 526,087 of unique patients are obtained? Would these patients be included in the 755,966? If they are included, what criteria were carried out to obtain these figures?
- In line 73-74, it shows that the data were different between 2006-2012 and 2013-2016 and used only the 2013-2016 data. The data from 2006 to 2012 are not taken into account? If this is the case, it should be clarified that only the data from 2013-2016 are used, as it would be convenient to clarify the total number that makes up the sample analyzed in the present work.
- In the calculation of the year of birth, it is not clear how the use of the date of the prescription can have a reliable result of the year of birth, do they establish some criteria of minimum or maximum age for the prescription of these medications in order to obtain a date of probable more reliable birth?

- On line 120, could it be incomplete?

Discussión:
Could it be that the differences you find with respect to the literature that increases polypharmacy with age is related to the approximate calculation of the birth date of the participants in your study?


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

Input:
Title: BUILDING INTERPRETABLE MODELS FOR POLYPHARMACY PREDICTION IN OLDER CHRONIC PATIENTS BASED ON DRUG PRESCRIPTION RECORDS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have correctly made the proposed revisions
Experimental design: The authors have correctly made the proposed revisions
Validity of the findings: The authors have correctly made the proposed revisions
Additional comments: I congratulate to the authors! There has been a significant rewrite of this paper. The issues of  references have been addressed this has positively impacted on the paper´s quality.


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: BUILDING INTERPRETABLE MODELS FOR POLYPHARMACY PREDICTION IN OLDER CHRONIC PATIENTS BASED ON DRUG PRESCRIPTION RECORDS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Additional information is suitable.
Experimental design: Additional information is suitable.
Validity of the findings: Additional information is suitable.
Additional comments: I would like to congratulate another one the authors for the interesant 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: BITE MARKS ON THE FRILL OF A JUVENILE CENTROSAURUS FROM THE LATE CRETACEOUS DINOSAUR PROVINCIAL PARK FORMATION, ALBERTA, CANADA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment.
Experimental design: no comment.
Validity of the findings: no comment.
Additional comments: Although bite marks are rare and difficult to interpretate, the authors made great effects to show some of the traces on the frill of a juvenile horned dinosaurs were caused by scavenging of a small-bodied theropod dinosaur based on a good review of previous studies and reasonable explanations. Therefore this is a contribution to our knowledge on dinosaur, esppecially to its paleoecology.
Two suggestions: 1) The discussions on traces ii, iv and v (paragraph beggining at line 201) seem to repeat what just said in previous paragraphs, and these may be combined together. 2) Can you describe what the mammal bite marks would look like as you did for crocs and lizards (paragraph lines 232-243)?
Minor changes can be found in the attached file.


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: BITE MARKS ON THE FRILL OF A JUVENILE CENTROSAURUS FROM THE LATE CRETACEOUS DINOSAUR PROVINCIAL PARK FORMATION, ALBERTA, CANADA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Background information is concise and relevant to the overall thesis, and the structure conforms to PeerJ’s standards.  The figures are clear and well labeled with legends that make sense.  The authors use clear English.  There are several typos within that must be fixed, which I outline below.  There is a tendency to use run-on sentences as well, with numerous conjunctions and transitional words.  This can be hard to follow at times.  Figure 4 could be modified further for clarity.  Consider labeling the marks with the same numbers as figure three.  Also consider outlining mark 3, so you can more easily distinguish it from mark iii.  I really like Figure 5!
Experimental design: The article is original primary research that has not been published before, and will add to the state of the science concerning Mesozoic descriptive taphonomy.  The authors clearly have an understanding of the Mesozoic tooth mark literature.  I would welcome the inclusion of more anthropological taphonomic literature, but this is not a "dealbreaker."  The work falls within the scope of PeerJ, as it is biological in nature and a research article.  The research question is well defined, in that it is a descriptive study of taphonomic traces with the attempt to describe them and identify the potential tracemarker(s).  The methods are replicable for the most part, but the way they determine that the fossil was from a juvenile Centrosaurus could use more elaboration.  The authors state they compared it with other centrosaurines and provide some data ranges, but they do not say which specimens.  The authors should add a supplemental table of the specimens sampled, or at very least state the collections or dig sites these specimens were taken from.
Validity of the findings: Data is robust.  The authors draw conclusions about the traces that are reasonable and well supported, and are very clear about what is speculation.
Additional comments: Abstract:
•	Line 11: this sentence is awkward with the position of the parenthetical statement.  Rephrase.
•	Line 13: the use of “and” seems inappropriate.  What is “hampered” exactly?  The ability to produce robust conclusions from traces?  Adequate sample?
•	Line 16: Fix typo “a s dromaeosaur”
Introduction
•	Line 23: missing an apostrophe after “dinosaur”.  Consider rephrasing the parenthetical statement to “including those that are healing, healed, and per- or post-mortem”
•	Line 29: “potential” to do what?
•	Line 33: change to “…described in detail”
•	Line 43: change to “…difficulties in interpreting the actions of the tracemarkers based on bite mark data”
•	Line 47: A bite is rarely made by multiple tracemarkers.  Specify you are talking about multiple bites on a single bone/carcass/assemblage.
•	Line 49: Run-on sentence
Materials and Methods
•	Line 64: Run-on sentence.  Consider breaking before “both”
•	Line 75: change to “…and, as a result, is”.  Eliminate the second “this is”
Description
•	Line 85: change to “…from a juvenile /subadult animal.”
•	Line 89: “in” should be “is”
•	Line 91: No comma after “loci”
•	Line 95: change to “they suggest” or “this suggests”
•	Paragraph beginning at line 98: see comments on fossil specimens in ‘Experimental Design” section.
•	Line 111: Last sentence of the paragraph does not make sense.  Rephrase
•	Line 126: what is “c.”?
•	Line 127: mention if this mark fully penetrates cortical bone here (you say it in other places).
•	Line 135: put a comma after “and”
•	Line 143: similar to above, state if this fully penetrated the cortex.
Discussion
•	Line 156: eliminate “of”
•	Line 158: I think there should be a parenthesis after “skeleton”.  Consider breaking up this sentence
•	Line 169: parenthesis after “marks”.
•	Line 171: you state you don’t know which side of the fossil is which, then how can you justify saying it is “dorsal”?
•	Line 173: there is some lit on trample marks you may want to consult before you conclude trampling.  Olsen and Shipman (1988: J. Archeological Science) wrote one of the first papers on the subject.
•	Line 179: Run-on sentence.
•	Line 181: Fix indent.
•	Line 187: put “it” after “so”
•	Line 188: should “and” be there?
•	Line 194: Confusing sentence.  Rewrite.
•	Line 207: You can either say “proximal to distal” or “medial to lateral.”  I think you mean the former.
•	Line 209: Do you mean expanded closer to the margin of the frill?  Can you use it as an anatomical reference point?
•	Line 213: change “no” to “not”
•	Line 219: Run-on sentence.
•	Line 222: reference the idea they were piscivorous
•	Line 233: Run-on sentence.
Conclusion
•	Line 288: “traces attributes” is confusing
References:
•	Line 323: italicize Alligator mississippiensis


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: BITE MARKS ON THE FRILL OF A JUVENILE CENTROSAURUS FROM THE LATE CRETACEOUS DINOSAUR PROVINCIAL PARK FORMATION, ALBERTA, CANADA
Review round: 1
Reviewer: 3

Output:
Basic reporting: “Bite marks on the frill of a juvenile Centrosaurus from the Late Cretaceous Dinosaur Provincial Park Formation” describes a set of different bone surface modifications on this skeletal element, with descriptions and interpretations of each. In general, the paper is well-organized and written (see my very minor comments listed below regarding spelling, punctuation, etc.). All information needed for replicating the results is included in the paper.

	The introduction and background are both generally well-written, but seem to be missing some highly relevant literature. The authors do cite D’Amore and Blumenschine, 2009, but while discussing the scarcity of papers describing theropod bite marks in the fossil record, fail to cite many of the papers listed in Table 1 of the D’Amore and Blumenschine study (a fairly exhaustive list of theropod bite mark papers, as of that year). Other relevant papers missing from the background and later discussion are Longrich et al., 2010 (not the same one which is already in the text), which covers an incidence of scavenging by a juvenile T. rex (a topic which is important to the findings of this paper), and Gignac et al., 2017, which itself describes and interprets T. rex bite marks, but also cites several other case studies and surveys of theropod bite marks which should be included in this manuscript. There was also an abstract by Fowler and colleagues in 2012, which addresses patterns of T. rex bite marks on several different Triceratops specimens, especially skulls. While this is gray literature, the authors might consider reading and citing it as well, because it specifically discusses frill-biting behavior, which is of special interest to the study at hand. In short, theropod bite marks actually are better known and better documented than this manuscript currently indicates, and this growing body of literature is allowing not just documentation of specific trophic events, but discussions of larger-scale patterns across clades. Including discussions of these other papers will not reduce the novelty of the presented findings, but it will provide more context for these bigger picture questions related to bite marks and feeding behavior/trophic structure.

	Perhaps a larger problem is the lack of any citations for the extensive, relevant anthropological literature on bite marks and other bone surface modifications. This is a fairly common issue in paleontological papers, which has resulted in our community reinventing the wheel with regards to many bone surface modification studies. I will discuss other specifics in more detail below, but in the context of the general framing and background of the paper, explicit guidelines for identifying and classifying bite marks relative to other bone surface modifications were erected by Binford in 1981, and their repeatability tested using blind inter-analyst studies of correspondence by Blumenschine et al., in 1996. Binford’s classification scheme has been widely used in anthropology ever since, and it is starting to be widely adopted in paleontology as well (see Njau and Blumenschine, 2006, D’Amore and Blumenschine, 2009, and Drumheller and Brochu, 2014 for examples, all papers which were already cited in this manuscript). These classifications predate the ones used in this study, but more problematic is that the authors use some of the same terminology (e.g. “score,” “furrow”) used in Binford’s scheme, but using different definitions. Being explicit with the classification scheme up front and avoiding these terms with conflicting or imprecise definitions (or simply using the Binford scheme) would increase the clarity of the background and descriptive sections of this paper.

	The topics addressed in the paragraph starting on line 43 would also benefit from including discussions of previous studies pulled from the anthropological or non-dinosaurian, paleontological literature. There are several published examples of multiple feeding trace makers interacting with a single prey item, with discussions on how to differentiate them and how to determine order of access to remains (e.g. Brain, 1980; Haynes, 1983; Selvaggio, 1998; Selvaggio and Wilder, 2001; Dominguez-Rodrigo and Piqueras, 2003; Delaney-Rivera et al., 2009; Drumheller et al., 2014). The authors mention that erosion or transport might be obscuring bone surface modifications, but do not cite examples of studies exploring the effects these processes have on interpreting surficial traces (e.g. Behrensmeyer, 1978; Behrensmeyer and Boaz, 1980; Behrensmeyer, 1981; Fisher, 1995). Difficulties in identifying scavenging are mentioned in the same paragraph, a discussion which could be strengthened by reading and citing some of the following papers: Hill, 1976; Shipman and Phillips, 1976; Shipman, 1986; Dominguez-Rodrigo, 1999; Forrest, 2003; Longrich et al., 2010. The addition of some or all of these studies would strengthen many of the subsequent interpretations presented in this paper.

	While I generally like the figures, I am a little concerned with the main description of Figures 3 and 4 being found only in the text, but not in the figure captions themselves. I had to flip back and forth between the description and the figures, which wasn’t ideal for ease of reading and comprehension. I understand that including all of that material in a figure caption would make it very long, and perhaps this issue will be lessened when the manuscript is formatted for publication, which will bring the descriptions closer to the figures themselves. Also, I am unsure what Figure 4 adds that could not be included (or isn’t already included) in Figure 3B. Lastly, some of the major bone surface modifications are visible in Figure 1, but others are not (or are at least difficult to see). Would it be possible to include higher magnification images for clarification in either Figure 1 or 3?

Minor issues with punctuation, grammar, etc.
        Line 16 – “as” has a space between the two letters
	Line 62 – the authors actually use the repository abbreviation before defining it
        Line 93 – extra “the” between “cross-sectional” and “thickness”
	Line 111 – “and understatement” should be “an understatement”
	Line 131 – delete indentation
	Line 185 – comma between “marks” and “but”
	Line 289 – comma between “dinosaurs” and “but”
	Line 323 – italicize “Alligator mississippiensis”
	Line 359 – hyphen seems to have been replaced with an error symbol
	Line 375 – “Njau” is misspelled
        Line 379 – check “?;” punctuation in article title
Experimental design: The fossil described in this paper is properly reposited, and the authors cite all relevant permits, demonstrating that the specimen was obtained legally and ethically. The authors provide very specific location information for where the specimen was recovered. I know that some authors (and repositories) prefer to keep these kinds of details out of papers, so as not to tip of fossil poachers. However, two of the authors work for the museum in question, so I am sure they are more familiar with their institution’s feelings on such matters.

	The analysis itself is a descriptive treatment of the fossil specimen with comparisons to other, similarly marked specimens in the literature. Other than the terminology and background issues I covered above, I think that this aspect of the paper is well done and certainly in keeping with other examples of similar studies in the literature.
Validity of the findings: Overall, the findings of this paper are largely supported by the data, as presented. The authors are conservative with their interpretations of the bone surface modifications they see, and do not go beyond their dataset. What issues I do have with this section relate to terminology (see the discussion of the Binford classification scheme, etc. above) and a need for more detail in places.

	The bone surface modifications on Side A, 4-6 are said to “resemble cracks” (line 129, and the paragraph starting on line 162). More detail here would be nice. Do they exhibit any crushing damage, which is an essential part of diagnosing bite marks sensu Binford, 1981 and Blumenschine et al., 1996? It sounds like they do not, and are more related to cracking along the fabric of the bone, as described in papers like Behrensmeyer, 1978, which discusses the details of taphonomic history which can be gleaned from weathering patterns. As the bone surface modifications which are not identified as bite marks are not discussed in much detail later, a few lines of discussion here would really add to the overall description of the fossil.

        The authors mention trampling as a potential source of mark A7 in the same paragraph, but do not cite or compare the features to Behrensmeyer et al., 1986, which describes trampling damage to bone in detail. Again, adding a brief discussion and a citation would be helpful. The paragraphs that starts on lines 185 and 194 has a similar lack of detail or discussion. Do the marks described exhibit signs of crushing or other impact damage? If not, they don’t meet the criteria for identification as a bite mark. Could they be other types of bone surface modifications instead (see Fisher, 1995 for several examples)? None of this is really discussed.

	The structures which have been more confidently identified as bite marks, starting on line 198, could also use a bit more detail in their descriptions. The drag mark (line 203) corresponds to a score, as defined by Binford, but detail beyond that could help bolster their association with a specific actor later on in the paper. What shape are they in cross section? U-shaped bite marks are characteristic of most bite marks, but add a bisection, and you have the defining characteristics of traces left by the highly carinated teeth of crocodylians (Njau and Blumenschine, 2006; Drumheller and Brochu, 2014; Drumheller and Brochu, 2016). More v-shaped traces might be related to the laterally compressed teeth of dinosaurs, especially if striations (associated with tooth serrations) are present (D’Amore and Blumenschine, 2009; 2012). Striations are not mentioned at all in the description. If they are absent, that is worth noting, but does not necessarily mean that the marks weren’t left by a typical theropod tooth. If they are present, then the authors might be able to better refine their association with an actor, following the methods presented in D’Amore and Blumenschine, 2009 and 2012. Striations and bisections should also be mentioned, if only to note their absence, in the section identifying the trace makers, starting on line 212. More details discounting mammals are also warranted too. On line 222, the authors say that none of the marks correspond with known bite marks attributable to Cretaceous mammals, but provide no further discussion or detail.

	Mark Biii certainly needs a more detailed description. The authors themselves say they are “not sure this is explained well here – hard to describe” on line 209, a note I am not sure they meant to leave in the submitted text. I believe that I understand what they are saying though. The surface margins of the feature are inset in comparison to the wider, underlying structure. Again, especially in the absence of crushing damage, this doesn’t sound like it necessarily is a bite mark. The sediment scouring they suggest as an explanation could widen and deepen any number of other bone surface modifications or damage. If there is crushing damage, adding a description of it would bolster their current interpretation. The fact that there is a similar mark on the opposite site is also potential support for their interpretation. I am not necessarily disagreeing with their interpretation, just saying that I think it needs a little more detail to be convincing. As mentioned in the figure discussion above, these features are hard to see and judge in the current Figure 1, so a higher magnification image of the most important of surficial structures might help.

	The paragraph starting on line 249 mentions the possibility of multiple actors leaving bite marks on a single bone. Please reference my suggestions above regarding similar studies that could be cited to bolster the arguments in this paragraph. The paragraph starting on line 272 addresses order of access to remains, or order of remains consumption. Please reference my section discussing scavenging above, and also add to that papers on scavenging/predation sequences, such as Hill, 1980, Binford, 1981, Haglund, 1997, and Behrensmeyer et al., 2003. The paragraph starting on line 272 might also benefit from a comparison to the Fowler et al study mentioned above, but again, that is from the gray literature, and I understand if the authors want to avoid citing it.
Additional comments: In general, this paper is well organized and conceived, but it is a little underdeveloped and could be strengthened considerably with the addition of more descriptive details, especially following (and citing) the findings of several of the additional papers listed in the previous sections. This will allow interpretations that are currently presented as speculative to be reframed with more context and support. With these additions, I think that this paper will be a strong addition to the growing body of literature describing and interpreting theropod bite marks.

Citations not already included in the manuscript:

Behrensmeyer, A.K., 1978. Taphonomic and ecologic information from bone weathering. Paleobiology, 4: 150-162.

Behrensmeyer, A.K., 1981. Vertebrate paleoecology in a Recent East African ecosystem. In Communities of the Past. Eds. Gray, J., A.J. Boucot, and W.B.N. Berry. Stroudsburg, PA: Dowden, Hutchinson & Ross, 591-615.

Behrensmeyer, A.K. and D.E.D. Boaz, 1980. The Recent bones of Amboseli National Park, Kenya, in relation to East African paleoecology. In Fossils in the Making: Vertebrate Taphonomy and Paleoecology. Eds. Behrensmeyer, A.K. and A.P Hill. Chicago: The University of Chicago Press, 72-93.

Behrensmeyer, A.K., K.D. Gordon, and G.T. Yanagi, 1986. Trampling as a cause of bone surface damage and pseudo-cutmarks. Nature, 319: 768-771.

Behrensmeyer, A.K., C.T. Stayton, and R.E. Chapman, 2003. Taphonomy and ecology of modern avifaunal remains from Amboseli Park, Kenya. Paleobiology, 29(1): 52-70.

Binford, L.R., 1981. Bones: Ancient Men and Modern Myths. New York: Academic Press.

Blumenschine, R.J., C.W. Marean, and S.D. Capaldo, 1996. Blind test of inter-analyst correspondence and accuracy in the identification of cut marks, percussion marks, and carnivore tooth marks on bone surfaces. Journal of Archaeological Science, 23(4): 493-507.

Brain, C.K., 1980. Some criteria for the recognition of bone-collecting agencies in African caves. In Fossils in the Making: Vertebrate Taphonomy and Paleoecology. Eds. Behrensmeyer, A.K. and A.P Hill. Chicago: The University of Chicago Press, 108-130.

D’Amore D.C. and R.J. Blumenschine, 2012. Using striated tooth marks on bone to predict body size in theropod dinosaurs: a model based on feeding observations of Varanus komodoensis, the Komodo monitor. Paleobiology, 38(1): 79-100.

Delaney-Rivera, C., T.W. Plummer, J.A. Hodgson, F. Forrest, F. Hertel, and J.S. Oliver, 2009. Pits and pitfalls: taxonomic variability and patterning in tooth mark dimensions. Journal of Archaeological Science, 36: 2597-2608.

Domínguez-Rodrigo, M., 1999. Flesh availability and bone modifications in carcasses consumed by lions: paleoecological relevance in hominid foraging patterns. Palaeogeography, Palaeoclimatology, and Palaeoecology, 149: 373-388.

Domínguez-Rodrigo, M. and A. Piqueras, 2003. The use of tooth pits to identify carnivore taxa in tooth-marked archaeofaunas and their relevance to reconstruct hominid carcass processing behaviors. Journal of Archaeological Sciences, 30: 1385-1391.

Drumheller, S.K. and C.A. Brochu, 2016. Phylogenetic taphonomy: A statistical and phylogenetic approach for exploring taphonomic patterns in the fossil record using crocodylians. Palaios, 31(10: 463-478.

Drumheller, S.K., M.R. Stocker, and S.J. Nesbitt, 2014. Direct evidence of trophic interactions among apex predators in the Late Triassic of North America. Naturwissenschaften, 101(11): 975-987.

Fisher, J.W., 1995. Bone surface modifications in zooarchaeology. Journal of Archaeological Method and Theory, 2(1): 7-68.

Forrest, R., 2003. Evidence for scavenging by the marine crocodile Metriorhynchus on the carcass of a plesiosaur. Proceedings of the Geologists’ Association, 144: 363-366.

Fowler, D.W., J.B. Scannella, M.B. Goodwin, and J.R. Horner, 2012. How to eat a Triceratops: large sample of toothmarks provides new insight into the feeding behavior of Tyrannosaurus. Journal of Vertebrate Paleontology, 32: 96.

Gignac, P.M. and G.M. Erickson, 2017. The biomechanics behind extreme osteophagy in Tyrannosaurus rex. Scientific Reports, 7: doi:10.1038/s41598-017-02161-w.

Haglund, W.D., 1997. Dogs and Coyotes: Postmortem Involvement with Human Remains. In Forensic Taphonomy: The Postmortem Fate of Human Remains. Eds. W.D. Haglund and M.H. Sorg. Boca Raton: CRC Press, 367-381.

Haynes, G., 1983. A guide for differentiating mammalian carnivore taxa responsible for gnaw damage to herbivore long bones. Paleobiology, 9(2): 164-172.

Hill, A., 1976. On carnivore and weathering damage to bone. Current Archaeology, 17(2): 335-336.

Longrich, N.R., J.R. Horner, G.M. Erickson, and P.J. Currie, 2010. Cannibalism in Tyrannosaurus rex. PLoS ONE, 5(10): e13419.

Selvaggio, M.M., 1998. Evidence for a three-stage sequence of hominid and carnivore involvement with long bones at FLK Zinjanthropus, Olduvai Gorge, Tanzania. Journal of Archaeological Science, 25: 191-202.

Selvaggio, M.M. and J. Wilder, 2001. Identifying the involvement of multiple carnivore taxa with archaeological bone assemblages. Journal of Archaeological Science, 28: 465-470.

Shipman, P., 1986. Scavenging or hunting in early hominids: theoretical framework and tests. American Anthropologist, New Series, 88(1): 27-43.

Shipman, P. and J.E. Phillips, 1976. On scavenging by hominids and other carnivores. Current Anthropology, 17(1): 170-172.


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: MOVEMENTS AND DISPERSAL OF BROWN TROUT (SALMO TRUTTA LINNAEUS, 1758) IN MEDITERRANEAN STREAMS: INFLUENCE OF HABITAT AND BIOTIC FACTORS
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are a few awkward sentences and minor grammatical and spelling errors (some of these are mentioned in the "Comments for the author" below), but overall the writing is clear. The objectives are stated clearly, and the manuscript organization, including the format of figures, tables and raw data, is appropriate.
Experimental design: The authors tracked movements of many individually marked fished over ~2 years in three streams. The spatial coverage of study reaches in each stream was extensive. The data set is a strong point of the study.
Validity of the findings: The analytical methods seem appropriate given the aims of the study. The discussion seems generally sound but the last sub-section, on management issues, seems too speculative and could be shortened substantially.
Additional comments: Ttile:

Consider replacing the subtitle with: influence of habitat and biotic factors

Abstract:

"...and the influence of habitat and biotic factors of Mediterranean brown trout" influence on what? Do you mean "...on Mediterranean..."? (see also comments on l. 60 below).

"Mobile brown trout were significantly larger than non-mobile individuals and exhibited significantly higher growth rates in two of the streams." Please avoid using "significantly" this way; the term is meaningless without reference to effect and sample sizes.

l. 20: "Fish movement (like other animals) are a choice": unclear meaning and grammar.

l. 62-63: "When all habitats required to complete fish life-history cycle are in spatial proximity, lower movement distances are expected." Please provide a reference.

l. 66: which activities does the 18-24 month period refer to, exactly? (see comment on l. 99-101 below).

l. 67: how does "degree of mobility" differ from "extent of movements"?

l. 68: seasonal variations of which variable(s)?

l. 79: is the Segre a river or a stream? You use both terms, but the reported features suggest that "river" is more appropriate.

l. 99-101: the chronology of activities should be reported more precisely. "Samplings" seems vague: when, exactly, were marking and recapture conducted at each site? (e.g., you should have no recaptures in the first sampling session).

l. 209-210: Tag retention was low and you mention "fish mortality" (l. 206; was it quantified?), so it is unclear what you mean by "The large number of tagged fish prevented both tag loss and mortality effects."

l. 218-220: Please avoid mentioning "significance" without providing effect sizes; those P values are devoid of meaning without additional context, including the fact that your sample sizes (from the reported degrees of freedom for F) are in the hundreds. Large sample sizes often yield "statistically significant" effects of trivial magnitude.

l. 238-239: "river" can hardly be called an "explanatory" variable, because it does not generalize to other settings. Perhaps it is a covariate which you included to adjust for unmeasured variation among rivers?

l. 239-241: "Interestingly, fish biomass was preferentially selected over density, despite the high correlation between them (Pearson’s r =241 0.94, N = 246, P < 0.0001)" There is nothing unusual here; since the effects of the two variables are more or less equivalent, their partial coefficients can be very different than their marginal coefficients. It is probably not a good idea to include both variables in a single model. Also, high density and biomass are presumably strongly related to habitat suitability, but the models do not allow you to untangle these effects because biotic and abiotic effects covaried naturally in your design. You would likely have to experimentally control the two types of factor to avoid confounding their effects. These comments also apply to the statement on l. 255-257 ("Surprisingly,..."): the "contrasting patterns" are likely a simple consequence of your examining partial coefficients in strongly correlated variables.

l. 258-260: Again, statements based on P values, but no mention of effect sizes.

l. 261-264: what are the values reported in parentheses? Mean and s.e.? s.d? Also, for the NV, is the difference in SPG between mobile and less-mobile trout biologically interesting? The differences in reported means seem negligible both for the NV and the NP.

l. 272-273: It seems unwarranted to extrapolate to "Mediterranean streams" based on results from three neighbouring streams.

l. 314-316: "Our results showed that departure rate was not consistently linked to particular habitat features, but depended on stream-specific characteristics. Consequently, habitat features are important in influencing movement behaviour when present above or below a certain threshold. For instance, fish inhabiting shallower sections in the FLM stream showed higher departure rates that those from deeper waters." I do not understand these statements. First, there would seem to be a clear effect of habitat; second, where does the notion of threshold come from?; third, how do habitat features differ from "stream-specific characteristics"?

l. 333: "Mobility appeared to confer an advantage on trout growth rate." But which is the cause and which the effect?

Table 1:

Report s.d., percentiles, or some other appropriate measure of sample variation. The standard error of the mean is not useful as a habitat descriptor.

The units for biomass are incorrect.

Table 2:

Provide units for the lambda parameter.


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: MOVEMENTS AND DISPERSAL OF BROWN TROUT (SALMO TRUTTA LINNAEUS, 1758) IN MEDITERRANEAN STREAMS: INFLUENCE OF HABITAT AND BIOTIC FACTORS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Lines 25-27: "Abundance" is not correct here.  These are fewer fish of the same population that demonstrate longer movements. They are not a different group of fish.
Lines 62-64: The wording “complete fish life-history cycle” is awkward. Consider revising, perhaps:  “..to complete the cycle of a fish’s life-history”.
Lines 64-65: errant use of a semicolon after “availability”.
Lines 65-76: Consider reordering this sentence to:  “The objectives of this study were to employ mark-recapture approaches over a  period of 18 – 24 months….”
Lines 76-78: delete “, it is the river”.
Lines 79-82:  This text should be moved up to the 2nd sentence of the study area.  Describe the Segre River first, then the tributaries.
Line 80: Is the 2,840 meters the elevation of the Pyranees or the change in elevation of the river? Unclear.
Figure 1. Caption needs to be improved to identify what the specific boxes are, and describe the abbreviations in the pictures.
Lines 95-98: How were the reaches and sections selected? Randomly? More information on the study design is needed.
Lines 99-101: Why the different sampling moths in 1993 in NP?  How are these data compared with the other seasons? (July-October).
Lines 101-102: Were surveys done each year in autumn?
Lines 104-106: How was sex determined? Is the approach accurate-perhaps  add a citation if available.
Lines 116-117: Consider breaking paragraph here.

Lines 118-119: Was substrate analyzed as a continuous variable? Was each category considered in the analysis separately?  Weren’t some aspects correlated?
Line 120: “1985” needs parentheses around it.
Lines 145-146: The comma does not work appropriately here. Change text after “recorded” to :”..recorded, and only fish captured during at least three surveys () were included in the analyses”.
Lines 154-158: Should this be a separate objective? This is essentially a comparison of how brown trout movements in this basin compare to other populations of brown trout.
Lines 175-179: Here, it seems like a more elegant approach would be to use river as a random effect.  Are there reasons this was not used?  Also, in this analysis, it would be easier to interpret the beta estimates across attributes and streams if they were standardized (e.g, z-score
Line 193: Here, the authors do not use a comma for numbers greater than 999, elsewhere they do. Please correct based on the  journal specifications.
Lines 193-197: How were the capture probabilities (with range) estimated?  Were there from the multipass surveys?
Lines 203-205: Wouldn’t it be more accurate here to simply refer to these as variability in recruitment and probability of capture?
Lines 209-201: This last sentence is not clear.
Lines 218-221: Is this for all sized fish?  It would be expected for larger brown trout making spawning migrations, but are smaller fish making these migrations?  Given the lack of understanding of movement in this region, quantifying movement patterns by life-stage (juvenile vs. adult) would be interesting to help identify habitat and life-history expressions across stages—i.e., to provide insights into the needs for the species.
Line 234: The use of the term “influence” is not appropriate-consider using “associated”.
Lines 238-239: The use of the term “best” here is not appropriate given the number of candidate models supported by the data. Also, the authors should provide a table with (at a minimum) all plausible models (<2 delta AIC). This could be in the supplemental, but right now it is hard to understand what “best” means.
Lines 239-240: Was density included with models using biomass? It seems like either using a correlation analysis prior to the analysis or testing for initial support  of one or the other via AICc, while including all other variables, would be the best approach. It is unclear if considered in the same model, which wouldn’t be appropriate given the correlation.
Line 241: it is unclear which “three variables” the authors are referring to.
Lines 245-247: Given that there was support for a stream effect, why do the authors discuss the “global” model that does not include a stream effect ( Lines 234-245)?  A more streamlined approach and discussion in the methods would help here. For example, “we initially evaluated an effect of stream…”.  If there is support, then all subsequent analyses should be performed with stream. Also, it is unclear why the authors do not consider size in this analysis?  Or it would be appropriate to use size as a group-here, perhaps juvenile or adult?
Lines 258-260: How is this possible?
Lines 278-281: Here, the authors seem to ignore the fact that the stream with the highest range for sedentary and mobile fish (FLM) is also the shallowest and not the largest in width.  While it does have slightly larger baseflows. How do these sizes actually compare with those cited from the literature?
Lines 299-303: Would the analyses differ here if the authors delineated their analysis by size?
Line 317:  “that” after “rates” should be changed to than?
Lines 333-336: Mobility also has its costs in terms of predation, which is not discussed.
Lines 339-359:  Given that the take home of this paper is that most fish don’t move, how is connectivity important?  I am being devil’s advocate here, but how do your results provide compelling evidence for connectivity and other management activities.  What about habitat restoration?
Table 3: The authors should change the wording from “best” in line 9. With so many models supported by the data, this terminology is not appropriate.
Figure 4 and corresponding analyses. In looking at the results here, it appears that a linear model was used, yet the authors claim that a 2-group exponential model was used. Are these lines from the exponential analyses?
Experimental design: Overall, the experimental design is appropriate.
Validity of the findings: Here, I suggest the authors consider 2 things:  (1) providing methods to describe a logical procession of parameters to be included in the GLM analyses.  E.g., test if there is a “stream effect”, then proceed with all subsequent analyses with stream effect included.  Here, the authors, consider the results of the model that does not include stream, then report the results of the stream. The neat part of this analysis is that it demonstrates that habitat appears to influence movement patterns. (2) the authors should delineate the analyses by size. This does get tricky with considering size of fish marked in year a and recaptured in year a+1 because fish are bigger and older in year a + 1. However, really trying to inform management would consider how movement varies by life stages and what factors may be associated with movement by life stage.
Additional comments: In general, a well written manuscript that does have interest to a broad number of fisheries biologists.  I do think the authors need to consider altering their approach in the statistical modeling (see specific comments) and comments above in “validity of findings”.  I also suggest the authors should  highlight the differences in movements across streams.  The dispersals and movement metrics are considerably higher in the FLM stream. These results should demonstrate the importance of place and while generalizations may occur (e.g., most fish don't move), the different movements and importance of habitat are interesting.  Finally, I think the authors could do a better job of explaining what these results mean in terms of management.  The implications are that most fish don't move, yet the authors discuss the role of connectivity?


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: MOVEMENTS AND DISPERSAL OF BROWN TROUT (SALMO TRUTTA LINNAEUS, 1758) IN MEDITERRANEAN STREAMS: INFLUENCE OF HABITAT AND BIOTIC FACTORS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
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: MOVEMENTS AND DISPERSAL OF BROWN TROUT (SALMO TRUTTA LINNAEUS, 1758) IN MEDITERRANEAN STREAMS: INFLUENCE OF HABITAT AND BIOTIC FACTORS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment reported here, but see below.
Experimental design: Lines 186-191: Why did the authors consider the MANOVA analyses to quantify "variations in fish density and biomass among streams.."?  This analyses, which appears to describe how biotic and abiotic factors affect these parameters are not in line with the objectives.   How does this link directly to the movement data?
Validity of the findings: Lines 225-227:  Why were these size classes used here and why different than in the previous results? The authors should align the information for consistency.

Lines 235-237:  Does this analysis only include those fish that moved? Or are those that did not move (i.e., did not leave home section; resident) included? If the latter, than perhaps a zero-inflated regression may be appropriate with length as a covariate as ~54% did not move.

Lines 241-242: How specifically was kurtosis measured?  This is not described in the methods.

 Lines 243-250:  These results are confusing due to the definitions presented early.  For example: (1) In Lines 160 -161, the authors stated that “Trout were classified as mobile (individuals leaving the home section) and non-mobile (sedentary individuals not leave the home section individuals).”; and (2) In Lines 148-149, the authors stated “A movement distance of 0 m was assigned to individuals captured and recaptured in the same section”. Thus, sedentary individuals movement must = 0.   Thus it is unclear how Figure 4 was created as the sedentary individuals do not move.   This is also true for lines 246-248-how are these values calculated based on the definition of sedentary?
It seems this confusion is clearly based on the definitions presented in the methods. The authors should provide clear criteria and justifications for describing individuals as sedentary or mobile.
Additional comments: Overall, a great improvement from the last version. A couple of questions linger. First, there are a number of details that need to be clarified and confusion in how ‘sedentary’ is defined, then used in the analyses (see below). Next, despite the consideration of length and use of an ANCOVA, the authors should consider breaking their analyses into juveniles and adults based on known information of sexual maturity. This may provide more insight into the observed patterns.  Specific comments are provided below.

Specific Comments
Lines 37-38:  Consider rewriting to: "Fish movement can be highly variable...". The current writing is given a sense of being-as if 'movement' is exhibiting this variation.
Lines 53-56: consider breaking this sentence into two.  The use of 'thus' is awkward.  Another option would be to simply eliminate ", thus, while' and replacing this with 'with'.
Lines 60-61: 'focussed' is mis-spelled.

Also, here, what did Vatland and Caudron find?
Lines 64-65: 'habitats' should be singular.
Lines 66-68: Consider changing the text from '..additionally predict a reduction' to 'predict additional reductions' and change 'distribution' to 'distributional'.
Lines 73-74: It seems contradictory to use the term 'resident' here. Are none of these fish "migratory".
Lines 75-77: How does the fact that the streams are small and with channel unit habitat that are close together mean that there is high habitat heterogeneity?

Why not change the text here to:  " The three study streams are small, have high gradient, and considerable habitat heterogeneity.  "

Lines 77-81: Consider moving this text to after the objectives and rewriting such that these statements are linked with your expectations/hypotheses.

LInes 77-81: Consider moving this text to after the objectives and rewriting such that these statements are linked with your expectations/hypotheses.

Lines 157-158: How specifically were these evaluated?  Using statistics? If so, the authors should report the alpha value.
Lines 161-162: Again, here and throughout 'samplings' should be singular. Here it should also be changed to 'sampling events' or 'marking events' or something similar.
Lines 168-173:  By definition, isn't the  λs = zero?  Given the definition of a sedentary is an individual that does not leave its home section (Lines 160-161).
Lines 193-194: The authors should consider breaking this paragraph before ‘The effects of biotic..” as this is a completely different analysis.
Also here, did the authors run separate analyses for each stream?  This is not clear.
Lines 217-219: Were these estimates of recapture probabilities from the depletion estimates?  This should be clarified here.  Also, the authors need to state in the methods that depletion estimates (I presume) were computed for different size classes in the methods.

Lines 230-232: The authors should report the samples sizes here. How many fish were recaptured and included in the movement analyses?
Line 231-232: Here the authors use ‘per cent’ (which should be percent), but lower the authors use ‘%’. The authors should seek PeerJ’s guide to authors and be consistent throughout.
Lines 235-237:  Does this analysis only include those fish that moved? Or are those that did not move (i.e., did not leave home section; resident) included? If the latter, than perhaps a zero-inflated regression may be appropriate with length as a covariate as ~54% did not move.
Lines 237-240: consider changing text  after ‘(Figure 3),’ to ‘..(Figure 3), but the seasonal differences were not  significant in the FLM stream…’.

Lines 254-157: The term ‘departure rate’ insinuates a temporal component.  The authors should consider a different term-preferably one that coincides with how others in the literature describe movement in this context.
Lines 258-260: Given the high correlation of the fish density and fish biomass, it would be inappropriate to include in the linear model (due to the assumptions of linear models). Were correlations evaluated prior to the analyses?
Lines 272-274: The text here “In the NV stream, together to fish biomass and season the most important variable was water velocity, both negatively related to departure rate.” is not clear.  Doesn’t the MANOVA approach consider both fish biomass and density?  Also, it would be helpful if the authors described the relationship in terms of actual biology where needed. For example, season is negatively related to departure rate? What does that mean? More in autumn?

In the same context, where years not included –i.e., seasons across years were grouped?

Lines 291-292: Change the text from “leave out” to either ‘move’ or something similar.
Lines 293-294: Consider changing “Movements of individuals are responses to..” to “Individuals often move in response to..”.
Lines 307-313: This text is ~redundant with the previous paragraph and should be combined with this previous text.
Lines 322-325: A word is missing between “because” and “did”.
Also, here, what is a “true spawning migration”?  If the habitats near fishes provide all of the habitat to meet the fish’s life cycle (spawning to rearing to spawning) is migration necessary?  This analysis would greatly benefit from splitting the movement analyses between likely juveniles and likely adults? Is this possible? This would provide more clarity to these results. The fact that length in the ANCOVA was not significant does not mean that juvenile and adult movements were not different. These are binary.
Table 2: There should be consistent use of significant digits in the columns.  Dispersal range should be 1 significant digit, particularly given the scale of measurement (~between median section differences).
Table 3: There should be consistent use of capitalization in the table-‘Water velocity’ is no capitalized but all others are all capitalized.  Also, the authors should consider using only 2 significant digits in the table as it is difficult to follow as is.

In addition, the use of the ‘bias’ analysis here is incorrect.  If the ‘full model’ has very limited support, why is it contrasted with the model averages?  The ‘bias’ information is not all that informative.  The authors should instead consider a table showing the plausible models (with AICc and Wi), and another showing the model-averaged values with the beta values with SE and the importance values.


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: EXPLORATION OF THE INVOLVEMENT OF LNCRNA IN HIV-ASSOCIATED ENCEPHALITIS USING BIOINFORMATICS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Indeed a good effort of using bioinformatics methods to reassign and shed light on different  already existing data of HIV associated encephalopathy.

however. this work falls short in concluding any new novel targets or new biomarkers that was discovered in the study.
The work only generally lists all the pathways associated with lncRNA .The discussion also excludes the expression level of the 17 lncRNA and thus the importance of which lncRNA should precede the other.
Please in ascending or descending order the lncRNAs and their targets genes which affect  HIV associated encephalopathy.
control, HIV, HIVS, HIVE datasets are some what not discussed in detail once the differential expression is found
Experimental design: no comment
Validity of the findings: The findings using webbased applications are indeed correlating with many references mentioned in the discussion however if finding the pathogenesis of  HIV associated encephalopathy is the aim of the work, then the broad results do not  allow to shed light on the role of lncRNA in  HIV associated encephalopathy.

Thus I suggest that the authors rank their finding , it may be the genes or the pathways , but ranking can certainly help in shedding light on the the role of lncRNAS in disease.
like the reference paper

Zhang C, Wang C, Jia Z, et al. Differentially expressed mRNAs, lncRNAs, and miRNAs with associated co-expression and ceRNA networks in ankylosing spondylitis. Oncotarget. 2017;8(69):113543-113557. doi:10.18632/oncotarget.22708.
give clear target genes for spondylitis. I suggest the authors use this paper as a standard as their works are similar.
Additional comments: Figure 3 can be made more clearer
Some references are cited asnumbers in the text while others as author names. stick to one.
Table 3 with an obscure pvalue is not discussed in text
English language can be checked for errors.
Hive abbreviation used both for disease as well as dataset is confusing sometimes.
Figure 2 says normal as a dataset instead of control


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: EXPLORATION OF THE INVOLVEMENT OF LNCRNA IN HIV-ASSOCIATED ENCEPHALITIS USING BIOINFORMATICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article "Explorations of the involvement of LncRNA in the occurrence and development of HIV-associated encephalitis using bioinformatics" have using publicly available data for suggest the involvement on LncRNA in the HIV-associated encephalitis.

The presentation in the paper too low on the concept and association with the earlier literature. Though the authors have mentioned that lncRNA have been found to be associated with the pathogenesis of HIV but failed to mention the motive behind the whole work. It can considered that apart from lncRNA there could be several other factors and there is no basis of considering only lncRNA for HIVE until it is proven in that context.

The English is satisfactory though at some place ambiguous. In introduction the author failed to explain the background of the work.

The table are mere mention the list without any detailing in the text which may have helped in some relevant conclusion. The authors failed to connect any specific finding with any results.
Experimental design: Though the research question was well defined but the authors failed explain the methodology clearly. In the methodology section the authors have not mentioned the methodology to find the exact method of their finding. Even though the data is found on the public database but that also require the statistical testing which is not mentioned in the section.

Also GO statistics is not explained to validate the outcome of the experiment.
the data in the public databases are raw and worked out in varied circumstances hence one cannot merely combine data to reach to a general conclusion. Due to high variability and varied platforms one may get high degree of variation which may influence the overall results. Hence the author should have used and mentioned the statistical approach to explain and bring the data to common platform for statistical analysis.
Validity of the findings: Since the methodology and not very elaborated and well explained hence one cannot rely on the finding of the data. In absence of any concrete results, all the finding seems to be too generalized and does not provide any basis for specific finding.

Statistics not explained. Conclusions are too general for any significant findings.
The conclusion provided does not connect to previous findings.
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: EXPLORATION OF THE INVOLVEMENT OF LNCRNA IN HIV-ASSOCIATED ENCEPHALITIS USING BIOINFORMATICS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is fairly easy to read in the most parts. Some major writing issues are: (1) Multiple times the authors use description such as "differentially expressed probes were screened out" to state that genes represented by certain probes were selected.  Their choice of words like "screened out" is confusing as that may imply that probes were left out.  (2) The Result section simply lists what is described in figures or simply state the approach once again.  The authors do not provide any reasoning/motivation for why a particular analysis was carried out, why did they choose particular datasets and tools etc.  Also, there is lot of repetition in Results and Discussion section.  For example, the lines 190-215 simply restate what ahs already been said in the results section.  This can be clearly seen when results from lines 138-148 are reiterated again in Discussion on lines 197-200 in a very similar manner. As pointed above, the second half the discussion has a clear disconnect with findings of the paper. Discussion should focus more on what the authors think the relevance of their results is in the context of existing knowledge. (3) The heatmaps in Figure 1 are not labeled at all. There is no way to tell what different rows in the heatmaps are representing. What is represented by red and blue colors?  What are the scales for the heatmaps? Were the genes shown here clustered in any way?
Experimental design: Overall, the research question is clearly defined, is meaningful and should fill a knowledge gap.  The most important issue is that there is no rationale/reasoning provided as to the connection between differentially regulated lncRNAs, miRNAs targeting them, and mRNA targets of these miRNA.  The authors should discuss why/how change in expression of lncRNAs may be linked to activity of miRNAs that target lncRNAs and mRNAs. The discussion lists several pathways and processes that are important for neural function and disease but the authors do not discuss how the lncRNAs they identified to be differentially expressed can be affecting these processes.  Also, is there a reason why lncRNAs may be more differentially expressed in white matter as compared to frontal cortex or basal ganglia? Is there anything known about heightened lncRNA function in the white matter?
Validity of the findings: Important issues to address: (1) Appropriate statistical evaluation of overlaps between differentially expressed genes in different samples in Figure 1 is missing. (2) How lncRNA expression changes in white matter can be linked to HIVE is not clear.
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: EXPLORATION OF THE INVOLVEMENT OF LNCRNA IN HIV-ASSOCIATED ENCEPHALITIS USING BIOINFORMATICS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The article in the present form is self explanatory and much clearer than the earlier forms.
the authors have clearly tried to implement the suggestions provided by this reviewer to their manuscript.The english has been significantly improved and significant literature to related work has been provided.However kindly address these minor queries
=>The HAD in abstract  is it same as HAND in the text - please elaborate.
=> -NMDAR- what is this.(Discussion)
Experimental design: the research problem has been well presented and all the questions that arose were nicely answered in the discussion part.The novelty of the paper lies in re annotation of microarray data which is nicely highlighted throughout the paper.Indeed a unique paper.
Validity of the findings: the paper tries to shed light on the pathogenesis of HIVE.the involvement of different nervous system patways indeed corroborates that the overexpression of lncRNAmay be causing multiple pathway to be unregulated , thus causing HIVE.
However ,the authors can also suggest the further research steps to be implemented in the lncrna area
Additional comments: overall a good paper in the present shape.
=>english can be double checked. usage of 'the' is unwanted in some areas
=> future prospective can be included
=> work references of lncrna microarray annonation in other diseases can also be included
eg.,
Guangde Zhang, Haoran Sun, Yawei Zhang, Hengqiang Zhao, Wenjing Fan, Jianfei Li, Yingli Lv, Qiong Song, Jiayao Li, Mingyu Zhang & Hongbo Shi ,(2018)Characterization of dysregulated lncRNA-mRNA network based on ceRNA hypothesis to reveal the occurrence and recurrence of myocardial infarction,
Cell Death Discoveryvolume 4, Article number: 35.


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: DISSOCIATING PREDICTABILITY, PLAUSIBILITY AND POSSIBILITY OF SENTENCE CONTINUATIONS IN READING: EVIDENCE FROM LATE-POSITIVITY ERPS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Meets the criteria, though see comments below about the raw data.
Experimental design: Adheres to the criteria.
Validity of the findings: Adheres to the criteria.
Additional comments: This manuscript describes a German version of DeLong, Quante, and Kutas (2014). As expected, the results replicate the earlier study, which was itself a double confirmation of a systematic literature review (Van Petten & Luka, 2012). In addition, the authors split the anomalous condition into semantically possible and impossible (uninterpretable) completions, which affected the frontal positivity to some extent.

The original study was important, so it is good to see how well the results hold up, although this study does not seem to contribute much beyond that. The manuscript is well written. My main issues are:

1.	There are limits to the interpretability of the post-hoc split of the anomalous items based on semantic possibility ratings. The possible/impossible conditions were represented by different words, which may differ in other ways besides possibility (indeed, Table 3 lists confounds of word frequency, length, neighborhood size). In addition, each participant saw only 17, 16, or 12 anomalous-impossible items, maybe fewer after artifact rejection. Ideally there would be a follow-up experiment with specifically constructed (counter)balanced possible/impossible anomaly items. But perhaps the authors can run a regression model to see if the condition effect survives when the predictors word frequency, length, and neighborhood size are included as predictors? I also recommend adding effect sizes and/or confidence intervals to at least the most important comparisons.

2.	The concepts of possibility and plausibility seem quite close to each other, in fact for plausibility ratings I would probably ask participants “how likely is it that the event described in the sentence would happen in real life?”. What were the examples with which participants were instructed? And how was the cutoff of 1.5 chosen for the possible/impossible distinction? How should future more controlled studies go about manipulating this dimension?

3.	I also verified the data. Reading the csv file required some find and replace operations first, among other things because each line started and ended with a quote. Also, there were some incomplete condition names, and condition names that seemed to differ only by a space:
A AN ANO ANOM ANOMI ANOMP E EX EXP EXP U US USP  USP
For example line 3687 says ““AN” and line 3688 say “”ANO”.

Keeping only the lines with complete condition names, I tested the possible vs. impossible comparison on the 7 left frontal electrodes and found a 0.60 microvolt difference, t(31) = 1.798, p = .082. The slight difference with the manuscript (p = .068) might be due to the samples with incomplete condition names. I recommend these be fixed for reproducibility, especially since the last letter of the condition name is critical (ANOMI/ANOMP). In addition, the basic ANOM condition would be helpful to add (this one cannot be reconstructed by averaging across ANOMI and ANOMP, because the trial numbers differed). It could also help to add an explanation of the columns and what kind of data these are (subject averages including all time samples, it turned out).

Minor comments

Discussion, line 363: “The data for the N400 from the two studies show a very similar pattern – ignoring the position of the zero line.” I agree the zero line is relatively meaningless, but it catches the reader’s attention. Would it help to leave out the bars and zero line and simply plot the data as points with error bars?

Discussion, line 394-396:
“The N400 effects show that relative to an anomalous noun, an unexpected noun that is nevertheless a perfectly plausible continuation shows a smaller negativity, because it is less of a surprise than an implausible, anomalous continuation.”
The interpretation of the N400 as reflecting surprise seems to ignore the literature from Kutas and colleagues indicating that the N400 is not an anomaly detector (including the seminal review cited a few lines later).

Figure 3 has a lot of white space. I would increase the size of the waveforms so the data are easier to inspect.

Figure 7 is not very insightful, because the error variance depicted is between-subjects while the design is within-subjects. If the authors want to show the relevant variability they could for instance plot the variation in difference scores between conditions instead.


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: DISSOCIATING PREDICTABILITY, PLAUSIBILITY AND POSSIBILITY OF SENTENCE CONTINUATIONS IN READING: EVIDENCE FROM LATE-POSITIVITY ERPS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Yes - for the most part - clear, unambiguous, professional English language was used. Exceptions are noted in the comments section.
Yes, the introduction and background section do a good job at providing context for the study. The literature was well referenced and relevant.
Yes, the structure conforms to the discipline norm.
Yes, the figures are relevant, high quality, well labelled and described.
Yes, the raw data was supplied. n.b. They supplied ERP data rather than the single trial EEG data, but I thought that this was fine.
Experimental design: Yes, the paper describes original research within the scope of the journal.
Yes, the research question was well defined, relevant, and meaningful. The authors state how the research fills an identified knowledge gap.
Yes, the research described in the manuscript involved a rigorous investigation performed to a high technical and ethical standard.
Yes, the methods were described with sufficient detail and information to replicate.
Validity of the findings: The findings provide meaningful replication, as noted below.
Yes, the data is robust, statistically sound, and controlled.
In general, the conclusions are well stated, linked to the original research question and limited to supporting results. The one exception is noted below.
Speculative conclusions did not feature prominently in this manuscript.
Additional comments: The present study involves a conceptual replication and mild extension of earlier work by DeLong, Quante, and Kutas (2014) examining ERPs to words in sentence contexts that varied in their predictability and their plausibility. The goal of the study was to examine claims regarding the functional significance of two putative ERP components elicited by words in sentences: a late frontal positivity hypothesized to be elicited by unexpected but plausible continuations of a sentence, and a late posterior positivity hypothesized to be sensitive to the plausibility of the continuation. There is no firm consensus on the functional significance of such late positivities in the ERP language literature and consequently the present study — while rather unoriginal — really does address a timely issue. Moreover, the authors have done two things to extend the earlier work from the Kutas lab. First, they have constructed materials in German modeled on the earlier work, and tested healthy adult German speakers. Second, they have conducted an additional analysis of their anomalous continuation condition, comparing ERPs to continuations that are implausible but possible with those that are implausible and impossible.

EEG was recorded from the scalp as healthy adults read short texts. ERPs were formed to critical words in sentences that comprised 1) expected continuations, 2) unexpected plausible continuations, or 3) unexpected implausible continuations. The latter category was divided into roughly 50 impossible continuations, and approximately 100 continuations that were simply implausible. During the N400 interval, 250-500ms post-stimulus, unexpected plausible continuations elicited more negative ERPs than expected ones; from 550-1000ms post-stimulus, unexpected plausible continuations elicited more positive ERPs over anterior left sites. Unexpected implausible continuations were more negative than unexpected plausible ones 300-450ms; unexpected implausible continuations were more positive than unexpected plausible items over posterior scalp sites 600-1050ms, but less positive than unexpected plausible continuations over anterior lateral sites 700-900ms.

Comparison of the two subsets of unexpected implausible stimuli (viz. implausible/possible versus impossible) revealed no differences during the N400 interval, and no differences over posterior sites 600-1000ms post-stimulus. Differences over anterior left sites 600-1000ms approached but did not reach significance. Other comparisons suggested that the positivity 600-1000ms over left anterior sites was similar in amplitude for unexpected plausible items and for the possible subset of implausible items, whereas the impossible implausible items resembled the expected items. However, as far as I could tell, the stats did not unequivocally support this characterization. If this is not the case, the authors should change the manuscript to better support their case.

The materials in this study have been constructed very carefully, and the quality of the ERP data is excellent. The analysis was quite careful, and I like the way the authors combine mass univariate tests with analysis of variance. The replication of the original DeLong et al. (2014) study with German materials and speakers is valuable for the reasons noted above. The dissociation between the two late positivities (frontal versus posterior) and their association with (respectively) unexpected plausible versus implausible sentence continuations is a valuable contribution to this literature.

By contrast, the novel contribution of the present study — viz., the comparison of possible versus impossible anomalous items — is its weakest component. There were nearly twice as many possible as impossible items, and the two groups of stimuli differed in word length, word frequency, and number of orthographic neighbors. These subtle confounds and the ambiguity of the analyses of the amplitude of the late frontal positivity limit the conclusions that can be drawn about differences in the way that language users process possible versus impossible events. The conclusion in line 500 of the paper is thus not fully supported by the data. Likewise, some of the discussion in section 4.4 should be toned down.

Overall, this manuscript is impressive for the quality of the data as well as the quality of the writing. My main issue is the treatment of the two kinds of anomalous continuations as being definitively different, when the data do not fully support this characterization. Minor revision to address this shortcoming would improve the manuscript.

Lines 62-63 are a bit awkward. Perhaps put “the EEG signal should reflect” right after the comma on p. 62 and revise accordingly.
The sentence in lines 64-66 is similarly awkward. It might help to start the sentence with “Van Petten and Luka” instead of with “Post-hoc assessment”.
Lines 128-129: It’s not clear what “siding up” means in this context.
Line 335: AMON should be ANOM
Line 411: shouldn’t ‘negativities’ be ‘positivities’?
Line 474: one of the ‘both’s should be eliminated (confusing because there are three arguments)
Line 497: ‘being both’ should be ‘both being’


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: DISSOCIATING PREDICTABILITY, PLAUSIBILITY AND POSSIBILITY OF SENTENCE CONTINUATIONS IN READING: EVIDENCE FROM LATE-POSITIVITY ERPS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Meets the criteria, but see comments about the raw data.
Experimental design: Meets the criteria
Validity of the findings: Meets the criteria
Additional comments: The authors have been responsive in dealing with most of my comments. However, one of the shared data files still has the incomplete condition names. As mentioned before, missing letters in the condition names are an issue because the final letter distinguishes between the critical ANOMI and ANOMP conditions. Also, from the newly added file I could not reproduce the results exactly.

1)	In the file with supposedly 4 conditions, here are the condition names and how often they occur (note the first line is a space only):

          2
A         9
AN       32
ANO      78
ANOM    146
ANOMI 16252
ANOMP 16249
E         6
EX       14
EXP      50
EXP   16314
U         5
US       20
USP      55
USP   16304

Not surprisingly, the stats for ANOMI vs. ANOMP excluding the incomplete labels, t(31) = -1.7979, p = .08193, are still different from those in the manuscript, which says “(t(31) = 1.89, p = .068)” on p. 17. It seems this is the same result I got in my previous review.

2)	The file with 3 conditions seems fine in terms of condition names:
ANOM 16384
EXP  16384
USP  16384

However, when I test “EXP “ against “USP “ as described in the manuscript, the t value I get is t(31) = -3.6639. This differs from that reported in the manuscript, which says “Paired t-tests revealed that EXP nouns differed from USP nouns (t(31) = -3.97, p < .001)” (p. 16). Perhaps this has something to do with rounding errors or with including/excluding the 1000 ms sample at the edge of the time window (I included it), but the authors will want to double-check their analyses and make sure they align with (and can be reproduced using) the shared data file.