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

Input:
Title: THE EFFECT OF PUPIL SIZE AND PERIPHERAL BRIGHTNESS ON DETECTION AND DISCRIMINATION PERFORMANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The introduction explores the relevant literature clearly and in an appropriate level of detail. The paper itself is self contained with relevant results to address the hypotheses.

Overall the English is very good, with a couple of small exceptions:
1) most importantly, be very clear about the stages of light transmission, image formation on the retina, and processing/perception of the image ("vision"). There are some strange constructions that are produced by muddiness here.

line 50: "... veil of light that reduces [effective] image contrast", I suggest adding "effective" because of course the physical stimulus is unchanged.

line 54-55: "small pupils see sharper", I suggest omitting this clause entirely. Pupils don't "see" at all, and you've explained how size affects image formation already.

line 66: "participants attended the bright disk", I suggest replacing "attended" with "fixated", if this is appropriate. Attended allows for the possibility of covert attention, which may be shifted to different parts of the visual image without changing the input to the retina.

line 85/86: "a high signal-to-noise ratio of the image", this is confusing, because I think you mean high SNR of image relative to background, not the SNR intrinsic to the image (although these quantities are correlated in many cases). If my interpretation is correct, I suggest adding "relative to background" or something similar to clarify.

2) Several nouns that are semantically important to the structure of the study are capitalised throughout ("Detection", "Target", "Discrimination", etc...) this is not standard English, and capitals should be removed.

3) Please interpret the outputs of the Quest algorithm. Have you configured it to find a 75% threshold? i.e. "Final Quest Value" should be interpreted as the font size threshold: an estimate of the font size required for detection/discrimination at 75%.

I also have concerns with regard to the figures:

1) Figures 4 and 5 are not referenced in the text. All figures should be referenced in proximity to the results that they demonstrate.

2) The data figures are not as informative as they should be. This is mainly because the symbols and line styles are not explained. 2.1: What do the red/green lines/dots represent? If this distinction is important consider using colours that are accessible to a colourblind reader, or mark the category by varying symbol shape as well. 2.2: What does the dashed line represent in Figure 6?
Experimental design: This research is within the Aims and Scope of the journal, and the research question is meaningful and well defined. The role of the research in addressing holes in our current knowledge is clearly stated.

By my judgement, the psychophysical studies were conducted to a high technical and ethical standard. However, I believe there are gaps in the methods reporting that will preclude replication, and I have questions and suggestions with regard to the statistical models and presented data.

1) Methods reporting. Please include the following details:

line 116: ideally provide mean +/- SD for age and education level of participants in all experiments

line 120: what model of computer monitor? What refresh rate? Was monitor gamma linearised or native?

line 124: what was the viewing distance?

line 149: was the fade gaussian? linear ramping?

line 167: what was the monospace font? How large was the text displayed? I know you say later this was adaptive, but please indicate a range, and that the precise value was used to calibrate performance for each participant.

line 171: what was the range of the contrast used?

line 176: Please state explicitly that accuracy is the percentage of correct trials.

line 197: this section on how pupil size was converted from au to mm should be in the general methods, not the results. Also, it should include more detail. What was the function you determined?

line 237: Where were the peripheral tablets with respect to the participant? Please state in terms of distance and angle of visual field.
Validity of the findings: 1) Comments on statistics

line 177: you say d' was similar to an accuracy based comparison. Please indicate where this can be verified (supplement? script in code/data package?).

line 260: There does not appear to be any hypothesis driving this on-the-fly measure of correlation between pupil size and threshold. I recommend removing it, and references to it through the paper.

line 261: Taking the mean of intermediate Quest estimates of threshold is not statistically sound. The procedure is intended to produce one estimate, informed by the responses to all previous trials (see Watson & Pelli, 1983 for an explanation of Quest).

2) Reporting within-subjects results and variability

line 178/179, line 200: please give mean and SD

Optional: consider making a much stronger test for within subject effects, and reporting within subject variability. I understand that you measure one accuracy measure per subject, per task, but you still have many trials with which to estimate variability (i.e. through bootstrapping.

3) Ergonomics
This paragraph is very difficult to follow and contributes very little ("notifications should be dark, except the text should be on a light screen, so maybe this is a dilemma for display design"), and deliberately ignores the other cues that make notifications detectable (they aren't at detection threshold, they have a sudden onset, they often move or bounce, and they are often accompanied by an auditory cue).

This needs to be either thought-out better and rewritten or removed from discussion and abstract.
Additional comments: Overall, I think this is a strong set of studies that need a moderate amount of work on the manuscript to be considered valuable, rigorous publications. Mainly, the manuscript needs to be expanded to include far more methodological detail, and the results need to be reported with more context, including the variability of measures of central tendency and improved integration between figures and text.

Other notes on clarity:

line 146: the description of the discrimination task sounds like a go/no-go change detection task. Please be clear whether you are using two-alternative forced choice (by context, it seems like 2afc is the method you are using).


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

Input:
Title: THE EFFECT OF PUPIL SIZE AND PERIPHERAL BRIGHTNESS ON DETECTION AND DISCRIMINATION PERFORMANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors tackle an interesting question looking at the pupil size in relation to detection and discrimination performance. The language is professional and clear with detailed literature references. However there are a few improvements that must be addressed.

1) Some figures were not mention in the text at all! Figure 4 & 5 are included in the manuscript but not referred to in the text.

2) The "Discussion" are general summaries of results for each section. I would suggest to only use the Discussion heading for the "General Discussion".
Experimental design: The research question is well defined and falls within the scope and aims for this journal. The three experiments presented are defined and straightforward. However, there are a few issues with the analysis that needs to be clarified.

1) The statistical analysis (tests) for each experiment needs to be stated. "Conducted with the R package 1me4" isn't sufficient.

2) Why was results not normalised between subjects? If there is a good reason then it should be stated. Otherwise it seems that the difference in starting pupil size should mean the detection and discrimination would be affected due to the differences in light levels going into the eye. i.e. one with a starting pupil size of 2.5 mm compared to one at 4.5 mm.

3) How do you account for adaptation?

4) Have you considered testing with dilation drops (phenylephrine) and would you expect similar results?
Validity of the findings: The core question of this study is an interesting topic and should be visited. However the analysis needs to be clarified and in more detail in order to validate the results.
Additional comments: No additional comments


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

Input:
Title: THE EFFECT OF PUPIL SIZE AND PERIPHERAL BRIGHTNESS ON DETECTION AND DISCRIMINATION PERFORMANCE
Review round: 1
Reviewer: 3

Output:
Basic reporting: please see general comments
Experimental design: please see general comments
Validity of the findings: please see general comments
Additional comments: This is an important effort and certainly merits publication of all the reported results. There is considerable inaccuracy in recent pupil-related papers (notably, NOT from these authors), which often make unsupported claims on the impact of small pupil dilations/constrictions on visual performance - some taking for granted that larger pupil implies better vision, others taking for granted that smaller pupils imply better vision. Thus, the first important contribution of this paper is in its stating that increasing retinal illumination (e.g. by changing pupil diameter) do not have univocal consequences on visual performance: some visual tasks may improve, some may be hampered.

There are, however, aspects of the paper on which I have some criticism. I offer them in an attempt to further improve the positive impact of this paper on the community.

Main comments

The reported experiments attempt to evaluate the effect of pupil size by changing peripheral luminance, hence retinal illumination on contrast detection and acuity. This is a first very reasonable attack to the difficult question whether pupil size alone (irrespectively of luminance) can affect visual performance. However, it does have troubles that I would like to see discussed in more detail and addressed by additional analyses and revised figures:

1) plotting performance change as function of pupil size is misleading. The performance change is actually observed with a luminance drop of a factor of 10 and more. Achieving this drop by just changing pupil diameter would require a constriction of several millimeters: not the small changes that are reported on the x axis. For this reason, I suggest reporting both performance and pupil diameter as function of luminance (in addition to or in substitution of the current figures).

2) there are multiple reasons why visual acuity should improve with illumination. One is pupil size (as seen in Campbell and Gregory 1960), but this effect is minuscule compared with the change of contrast sensitivity and acuity that accompanies luminance increases and that is put down to properties of the retinal circuitry (here is my favourite picture for this line of work: https://webvision.med.utah.edu/wp-content/uploads/2018/05/KallSpat24.jpg). This factor should be discussed in the paper. Relatedly, I wonder whether there is any evidence that the improved visibility of black-on-white text (compared to white-on-black text) is partly dependent on pupil size. Is there any literature testing whether this advantage survives in conditions of Maxwellian view? My understanding of the work by N. Graham in the 70s is that such advantage for on- vs off- stimuli is still observed when pupil size is kept fixed (Maxwellian conditions), but I acknowledge that testing conditions used in those studies may not be directly relevant to the question presented here. Please comment.

3) given the above, and given the known effects of light scatter, it is expected that contrast detection and acuity should vary with retinal illumination. however, this is not the point of the paper, which is concerned with showing that pupil diameter has an effect on detection or acuity, in addition to or independent of the effect of luminance level.
One way to establish such independent contribution of pupil diameter is by looking at inter-individual variability: across subjects, illumination is kept constant, but pupil diameter may vary and this should result in across-subjects variations of acuity/detection performance. For experiment 3 (successfully measuring the acuity limit), such correlation is reported. However, the correlation is clearly influenced by an outlier (one out of the 20 subjects has both very low acuity and very large pupil diameter). Given the critical importance of this observation in the logic of the paper, please confirm that the correlation holds when this subject is excluded.
For the other experiments (where only the limit of detection performance could be adequately studied), there appears to be no such trend for correlating performance with pupil diameter.
what is the evidence that pupil diameter affects acuity/detection then?

Relatively minor comments

1) In the interest of precision, I would like the authors to clarify why they assume that larger pupils should improve detection by increasing light influx. I can see why increasing light influx improves absolute detection thresholds - the ability to catch single photons in scotopic conditions. I am not sure why increasing light influx should also improve contrast detection (which is tested in the reported experiments). The authors mention the concept of signal-to-noise ratio, but I don’t see how this should be affected (increasing light influx should equally affect both the signal and the noise, no?).

2) On the other hand, I think that increasing light influx should also increase light scatter, with a consequent detriment of contrast-detection performance. If so, perhaps the authors could stress that the two opposite effects will always combine, and whether performance increases or decreases depends on which of the two has the strongest effect. Considering this, I wonder whether the results from the contrast detection task could not actually be interpreted as evidence AGAINST pupil size affecting performance. If light scatter increases with pupil size, then detection should be hampered; however, he opposite is observed in both experiments 1 and 2.

3) It is increasingly common to read that pupil constriction improves visual acuity. Many authors use this to explain why pupil constrictions may accompany attention shifts, and some have gone so far as to suggest this as a possible confound that should be controlled for routinely, e.g. in EEG studies (Bombeke). In the face of this, another important contribution of this paper is to show how difficult/cumbersome it is to find an experimental condition where the acuity of central human vision can actually be modulated. Of three experiments, only the last one with very non-standard apparatus was successful in recording a measurable acuity change. I suggest that this point is emphasised further in the text.


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

Input:
Title: THE EFFECT OF PUPIL SIZE AND PERIPHERAL BRIGHTNESS ON DETECTION AND DISCRIMINATION PERFORMANCE
Review round: 2
Reviewer: 1

Output:
Basic reporting: Comment R1.5 - in the review guidelines, whether or not the article is written in "technically correct text" is not left as a matter of taste.

In the absence of a copyediting service at PeerJ, I recommend that the authors should revise which words they choose to capitalise to include only proper nouns, or those words at the beginning of sentences. Semantic importance is not grounds for capitalisation under any professional English standards.
Experimental design: no comment.
Validity of the findings: no comment.
Additional comments: The authors have done an excellent job integrating feedback into the manuscript, and I recommend it for acceptance.


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

Input:
Title: THE EFFECT OF PUPIL SIZE AND PERIPHERAL BRIGHTNESS ON DETECTION AND DISCRIMINATION PERFORMANCE
Review round: 2
Reviewer: 2

Output:
Basic reporting: no further comments
Experimental design: no further comments
Validity of the findings: The authors have addressed my concerns with additional analyses and further discussion.
However, the abstract and conclusions have been largely unaffected. My point was (and is) that luminance has very well known effects on visual sensitivity and acuity (and of course will change pupil size as well). The reported experiments manipulate luminance and find changes in visual sensitivity/acuity; relating these changes to pupil size is speculative, and should be presented as such. I agree with another reviewer that an effective way of manipulating pupil size independent of luminance, an thereby dissociate their effects, would have been a pharmacological intervention; however, I also agree with the editor that such investigation would go well beyond the scope of the present work. Thus, all I ask is that the authors rewrite parts of their text to clearly separate speculations (role of pupil size) from findings (effects of luminance). Small edits should suffice, for exampleP

abstract: "Small pupils lead to improved discrimination performance, consistent with the positive-polarity advantage" There is no evidence that small pupils *lead* to improved performance in these experiments. Rather, the performance improvement is observed at high luminance, and it is accompanied by small pupils. here, the only variations of pupil size independent on luminance are the inter-individual variations, and these do not correlate robustly with performance.

abstract & introduction: "The positive-polarity advantage is often linked to pupil size." the word "linked" suggests that a causal link between pupil size and positive-polarity advantage has been established by prior work, which is inappropriate. Perhaps the authors mean that the positive-polarity advantage is generally accompanied with small pupil size?

Similar instances are encountered throughout the text and in the conclusions, please rephrase
Additional comments: No additional comments


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

Input:
Title: THE EFFECT OF PUPIL SIZE AND PERIPHERAL BRIGHTNESS ON DETECTION AND DISCRIMINATION PERFORMANCE
Review round: 3
Reviewer: 1

Output:
Basic reporting: nothing to add
Experimental design: nothing to add
Validity of the findings: nothing to add
Additional comments: nothing to add


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

Input:
Title: BIOMARKER POTENTIAL OF REPETITIVE-ELEMENT TRANSCRIPTOME IN LUNG CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: In the article entitled “Biomarker potential of repetitive-element transcriptome in lung cancer”, Arroyo et al have attempted to identify potential REs as biomarkers for lung cancer.
I found the bioinformatics analysis pipeline well-conceived and the authors have highlighted the importance of RE transcriptome for potential biomarker search. I think the article is of value to the general cancer-diagnostics community and suitable for publication in PeerJ.
The authors might consider connecting the introductory paragraphs better to emphasize the motivation behind the present study. For example, can authors comment on if RE-transcriptome has been investigated for any other cancer type or if the REs identified in this study has been implicated in other cancer types?
Experimental design: No comments
Validity of the findings: No comments
Additional comments: No 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: BIOMARKER POTENTIAL OF REPETITIVE-ELEMENT TRANSCRIPTOME IN LUNG CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, this submitted paper is a good follow-up of their previous publication based on bioinformatic analysis of the transposable elements (TEs) for lung cancer. Overall the paper submitted to PeerJ is well-written with sufficient intro about the background of the transposons, REs and its potential relationship with cancer. Results and discussion are also informative and well-written. The abstract is clear and can summarize what they have found in this paper.
New potential bio-markers for lung cancer treatment are very important and always can draw attention for biologists and pharmaceutical scientists. I think the authors have provided good results (figures and table, etc.) to support their claims, with appropriate references. I only have some concerns about the experimental design and data shown in this paper. I will describe these concerns in the following parts.
In general, I think I recommend this paper to be published in PeerJ if the authors can address all my concerns.
Experimental design: The bioinformatic analysis is well-designed with a very clear workflow.
My first question is about the data pre-processing stage. The authors claimed (lines 174-175) that “All snRNA, rRNA and tRNA elements were removed from output because they can provide spurious differences due to the way each laboratory extracted the RNAs.” I am curious that how much difference you will get by incorporating these three elements? It seems that the RepEnrich (BMC Genomics volume 15, Article number: 583 (2014)) method does include all the small RNAs.
My second question is related to the samples you collected from the database and this is just on my own curiosity. Can you distinguish on which stage the lung cancer cells were collected and RNA-sequenced?  I am a little worried that the early stage cancer (Stage I) and late stage cancer (Stage II and III) may have differences in up- and down-regulations.
Validity of the findings: Overall, I think the paper have shown some interesting findings. My concern about the findings include:
1.	In Table S1, the upregulation in SCLC and LUAD are expressed as positive and negative values. Usually the positive value represents the upregulation and negative represents the down regulation. It is a little confused that the negative values are used to illustrate the upregulation in LUAD. This is also not consistent with the positive and negative values used in the main figures.
2.	In lines 219-220, the authors said, “only 5 were slightly (−1.063 to −1.39) up-regulated in normal cells from LUAD samples”. However, in line 231, log data in the same range (1.1-1.3, -1.1- -1.3) are named as “very significant fold changes”. These different claims are very confused. Appropriate explanations need to provide.
3.	In Figures 3 and 4, the authors claimed that “all box medians are close to triangles”, which are not correct in some Res, such as HERVK11D−int and LTR18B in figure 3, ERV24B_Prim−int and MER65−int in Figure 4. Again, Appropriate explanations need to provide in the figure captions.
4.	In lines 259-260, it seems in figure 4 there are only 21 Res are upregulated but 50 are downregulated, it is not consistent with the “46 differentially 260 expressed REs were down-regulated against 25 differentially expressed REs up-regulated” claim.
5.	In figure 5, why is ‘DNA?’ so tightly distributed? Where is the red box?
Additional comments: In general, it is an interesting, timely paper that shows good results of potential biomarkers in lung cancer using bioinformatic analysis. I recommend this paper published in PeerJ if they address all my concerns listed above.


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

Input:
Title: BIOMARKER POTENTIAL OF REPETITIVE-ELEMENT TRANSCRIPTOME IN LUNG CANCER
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: 1) In the introduction the authors emphasize that new bio-markers were required in the diagnosis of lung cancer and have rightfully explored the repetitive transposon elements that undergo oncogenic changes. However authors have not commented on the value of the novel bio-markers such as CBX3 and CRABP2 that have been similarly identified using biochemical methods and RNA-seq differential analysis of normal vs cancer tissue without using the global-RNA seq data. Can authors comment on the contrast of utilizing their method to the general transcriptome analysis (such as in Lung Cancer. Volume 84, Issue 3, June 2014, Pages 229-235) of the lung cancer and also explain if their method is superior to others and why or is their method just an alternative way of looking at more bio-markers?

2) Line 422, authors suggest the RE down-regulation could probably be due to methylation or genetic environment and are unsure how much does intrinsic RE transition contributes to the down-regulation. Can authors address this question in the current article? Specifically it is known that Alu/LINE-1 at specific gene-loci is an important information into the pathological states in cancer. It is not clear if authors  have studied the locus-specific methylation of the transcriptome that they consider will be useful bio-marker of lung cancer. Do authors have a comment to dispel the ambiguity?


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: BIOMARKER POTENTIAL OF REPETITIVE-ELEMENT TRANSCRIPTOME IN LUNG CANCER
Review round: 2
Reviewer: 1

Output:
Basic reporting: I think the revised manuscript is well-written and already addressed all my concerns. It is now suitable for publication in PeerJ and also can provide valuable information of potential biomarkers against the lung cancer.
Experimental design: I think the experimental design in current version is clear. I have no further comments.
Validity of the findings: The authors already addressed all the concerns I mentioned. I have no further comments.
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: BIOMARKER POTENTIAL OF REPETITIVE-ELEMENT TRANSCRIPTOME IN LUNG CANCER
Review round: 2
Reviewer: 2

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: GENETIC CHARACTERISTICS OF NON-FAMILIAL EPILEPSY
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a very ambitious, technically solid, manuscript that addresses the relevant question of the role of genes in non-familial cases of epilepsy. It has the potential to be a high impact paper. However, improvements are required to reach the target of readability that deserves. The first improvement is certainly in the language. The article must be written in better English and must use clear, unambiguous, technically correct text to conform to professional standards of courtesy and expression. I suggest that you find a native English language colleague to review your manuscript. Expressions like “Contrary to neonatal to childhood epilepsy”, “There might be hidden genetics in non-familial APEs”, and many others can be improved. The use of undefined acronyms, like mTORGs for “mammalian target of rapamycin (mTOR) pathway-related genes” or ICRGs for “ion channel-related genes” makes the manuscript less readable. The article includes a sufficient introduction and background to demonstrate how the work fits into the broader field of knowledge. Relevant prior literature is also appropriately referenced. The structure of the article also conforms to an acceptable format. Figures are relevant to the content of the article and appropriately described and labeled. All appropriate raw data have been made available.
Experimental design: The research question is well defined, relevant, meaningful, and within the aims and scope of the journal. The authors also make clear how their research contributes to filling an identified knowledge gap in the field. The investigation was also conducted rigorously and with a high technical standard, in conformity with the prevailing ethical standards in the field. Methods are described with sufficient information to be reproducible by other investigators.
Validity of the findings: Impact and novelty of the manuscript are potentially very high, however, the authors should discuss better their results and point to the novelties they have found. All underlying data are provided; they are robust, statistically sound, and controlled. The data on which the conclusions are based are solid. Conclusions are well stated but a little confusing, linked to the original research question and limited to those supported by results. Claims of a causative relationship are supported by clear evidence.
Additional comments: The manuscript summarizes an impressive amount of work that deserves a better presentation. Improvements in the language and the fluency of the manuscript require some additional efforts. This will certainly benefit the readability of the manuscript and will make it more appreciated by other investigators in the field.


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: GENETIC CHARACTERISTICS OF NON-FAMILIAL EPILEPSY
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: No comment
Validity of the findings: no comment
Additional comments: This is an interesting non-familial epilepsy study by using whole exome sequencing to study the genetic characteristics in a total of 243 patients. The study hypothesis and method were well written and relative good description in the results and discussion sessions. Some points need to be raised:

1.	It is pity that familial segregation was not performed in those 23 non-familial patients with presumed disease-causing variants. The mutation status in other family members can provide the information concerning whether the mutation was de novo or the gene penetration maybe incomplete.

2.	In patient SU023 having heterozygous CNTNAP2 p.Ile172Thr variant who presented with typical CDFES, I wonder if there is information showing large deletion or copy number variations from the WES data? Certain analyses (such as cn.mops (Copy Number estimation by a Mixture Of PoissonS)) can be performed to retrieve those information. Likewise, similar analysis should be considered in other individuals.

3.	I would like to know, for patients with TSC1/TSC2 variants, do they fit the diagnostic criteria of tuber sclerosis complex? What is the clinical presentation in other organ, including the skin, heart, kidneys, and lung?

4.	As stated, the identified pathogenic variant numbers were too small for further analysis in the drug sensitive and resistance, which was the original hypothesis of this manuscript.  This indicated that the goal cannot be achieved without international collaboration of epilepsy studies.


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: GENETIC CHARACTERISTICS OF NON-FAMILIAL EPILEPSY
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Through a large cohort of adult patients with non-familiar epilepsy, aim of the authors was to better understand genetic basis of this huge amount of epileptic patients without a definite aetiology. The paper is original and of great interest because in the last years most of articles have been published on DEEs, while genetic basis of adult and non-familiar cases remained unclear. Overall the paper is original, well written, fluent and clear. However, there are few comments consider before publication:

1. The definition of DR (drug-resistant) and DS (Drug-responsive) is not clear. There is the group of patients with less than 12 seizures/year that does not fit with both groups. Is this definition arbitrary or did you refer to literature? Please clarify.
2. Half of the study population is DR. This rate is higher (usually DR patients are 30%). Please comment this result in the discussion giving possible hypothesis for this result (age, aetiology…).
3. Ages at onset and at study should be of more precise also in the text (only in table 3). Please clarify the sentence “ages at recruitment and at seizure onset were approximately 40 and 20 years” including medians and ranges for each age.
4. Authors refer to “Epileptic Encephalophaties (EEs)”. It would be better to us the updated definition of “Developmental and Epileptic Encephalophaties (DEEs).


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: GENETIC CHARACTERISTICS OF NON-FAMILIAL EPILEPSY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper has been profoundly improved in the language that is now unambiguous and technically correct. It conforms to professional standards and is certainly more easily readable.
References, structure, figures, tables, and raw data are in excellent shape.
The results are now clear and better appreciated.
Experimental design: It is sharp and clearly defined. The authors have conducted their research rigorously with excellent technical standards. Language improvement has undoubtedly helped to understand better the experimental design and the superb work done.
Validity of the findings: The findings are relevant and original. Conclusions are well stated.
Additional comments: The paper is now in good shape and it is suitable for publication. The authors have done a good job. Their excellent work deserved an effort to improve the presentation.


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: GENETIC CHARACTERISTICS OF NON-FAMILIAL EPILEPSY
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors responded to my questions point by point. I am satisfied with authors' reply.


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: IDENTIFICATION OF TARGET GENES IN NEUROINFLAMMATION AND NEURODEGENERATION AFTER TRAUMATIC BRAIN INJURY IN RATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clearly written, it provides enough background and has the necessary citations.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this manuscript Zhao et al identified genes that had altered expression after traumatic brain injury. Using multiple bioinformatics methods, they identified several genes that may play key role in neurodegeneration after brain injury. The manuscript is nicely written and there are only a few minor mistakes that need to be corrected:
1.	Line 44: I assume that the (2012) is a reference. Please make sure to cite references correctly.
2.	Line 132: The authors state that they selected 20 genes of interest out of 6513 genes. Why these 20 genes? What was the criteria for selecting those 20 genes only? Please provide more details in this section.


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: IDENTIFICATION OF TARGET GENES IN NEUROINFLAMMATION AND NEURODEGENERATION AFTER TRAUMATIC BRAIN INJURY IN RATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this paper, the researchers have conducted an integrated analysis using published RNA-sequencing studies to determine differential expression of genes induced by traumatic brain injury (TBI), and identified thousands of genes which were relevant. Overall, although the researchers have provided lots of statistic analysis, the novelty of this paper is low and the results were too broad to provide valuable information which needs to be really focused on.
Experimental design: 1.	Most of the figures did not provide detailed legends to fully describe the figure
2.	In Figure 4, it’s hard to distill any useful information since there’s no information about the specific genes. It’s better to revise this figure with more details about the genes, otherwise it’s redundant.
3.	In Figure 5, it’s also hard to get really useful information since there’s too much. It’s better to just present a few of most relevant genes
Validity of the findings: N/A
Additional comments: N/A


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: IDENTIFICATION OF TARGET GENES IN NEUROINFLAMMATION AND NEURODEGENERATION AFTER TRAUMATIC BRAIN INJURY IN RATS
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1, The authors analyzed the gene expression changes using previously published data and concluded that FOXP3, APOE, MAPT and TREM2 are associated with neuroinflammatory and neurodegenerative disorders after TBI based on their analysis.

2, For Fig. 1, the authors should clearly label the data source and treatment in the x-axis, rather than just showing the file names. Also, I think the authors should show the Top50 or Top100 DEG (as well as the gene names) rather than showing all the genes in the heatmap.

3, The reference need to be double-checked. For example, author names for the first reference is missing.

4, For Fig. 4, the authors should at least clearly labeled the gene names of the largest circles so the readers can understand the conclusion made in Page 13, line 153.
Experimental design: 1, DEG analysis is critical in this study. Step-by-step procedures regarding how related data analyzed was performed should be clearly written in the methods section.  Else, the authors could included their original codes in the supplemental data.
Validity of the findings: 1, Raw data of all gene expression should be provided in the supplemental for the readers.

2, As a standard part of DEG analysis, a PCA plot showing a separation of TBI group and Control group will make this study more convincing.

3, The authors selected 20 genes of interest in table 1. Why these 20 genes are selected? Are these genes with highest fold change or p-value?

4, Based on the data provided in this study, I don’t think it’s appropriate or necessary to include the four genes in the title. The authors claimed that they found 6464 up-regulated genes in this study and the fold change of these four genes are less than 2 fold based on table 1.
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: IDENTIFICATION OF TARGET GENES IN NEUROINFLAMMATION AND NEURODEGENERATION AFTER TRAUMATIC BRAIN INJURY IN RATS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed all my concerns.


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: IDENTIFICATION OF TARGET GENES IN NEUROINFLAMMATION AND NEURODEGENERATION AFTER TRAUMATIC BRAIN INJURY IN RATS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors well addressed my concerns.
Experimental design: The work is well designed.
Validity of the findings: The findings are interesting and all raw data and methods are provided.
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: INSIGHT INTO PLANT CELL WALL DEGRADATION AND PATHOGENESIS OF GANODERMA BONINENSE VIA COMPARATIVE GENOME ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study investigated the CAZymes in G. boninense. Their results provide valuable information for the further studies on the fungal virulence and pathogenicity. Hemibiotrophic fungi have similar CAZyme contents to that of necrotrophic fungi, but obvious distinct infection process. Therefore, it would be of great interest to examine the expression patterns of CWDE genes in G. boninense in comparison with its necrotrophic relatives, which I think should have been done.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: 1. The dbCAN release has been updated to the version 6.0 (07/20/2017), why was only the version 1.0 used here?
2. Cutinase (CE5) is an important enzyme family related to the fungal virulence. It is surprised that both G. boninense and G. lucidum have no genes coding cutinase (Table S1). I think authors should re-examine their results carefully to check it.
3. Many conclusions were made in haste in part “Profiling of CAZymes in selected phytopathogenic fungi”, e.g., the authors cannot conclude that GH26 was not observed in other pathogens with necrotrophic behavior (line 294-295) because their comparison was based on only few fungi. Actually, some necrotrophic plant pathogens indeed have GH26 genes.Similarly, authors should conclude those carefully  in line 300-301, 325, etc..
     Zhao et al. (2013) investigated the distribution of CAZymes among fungi with different nutritional modes, and their results would be helpful for the comparative analysis in this study.
4. Fig.2 B and Fig. 2 C were wrongly referred to in lines 312 and 323.


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: INSIGHT INTO PLANT CELL WALL DEGRADATION AND PATHOGENESIS OF GANODERMA BONINENSE VIA COMPARATIVE GENOME ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper describes a genomics approach to understanding aspects of the pathogenesis process involved in Ganoderma infection of oil palm plants. The study focused on one aspect of the process, namely the so-called CAZymes involved in cell wall degradation.
Experimental design: the authors have done a good job in carrying out a comparative genome analysis of the CAZyme group of genes in a range of species and pathovars. Their methods are fine and the conclusions are sound.
Validity of the findings: Overall, the study provides useful basic information for the research community.
Additional comments: One cautionary aspect of the study is that so far only a draft version of the G. boninense genome has been published and it is still early days in terms of compiling a fully robust gene model of the species, although such efforts will be helped by the availability of the G. lucidum genome sequence that can be used as a reference genome. As with the oil palm genome, initially sequenced in 2013, it will take some time to come up with a fully reliable gene model and therefore studies such as the present one must be regarded as provisional. It would be useful to make these concerns more apparent by adding a short section in the Introduction.

Despite these reservations, the authors have done a good job in carrying out a comparative genome analysis of the CAZyme group of genes in a range of species and pathovars. Their methods are fine and the conclusions are sound. Overall, the study provides useful basic information for the research community.


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: INSIGHT INTO PLANT CELL WALL DEGRADATION AND PATHOGENESIS OF GANODERMA BONINENSE VIA COMPARATIVE GENOME ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have properly addressed all the issues I raised, and I have no new comments.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: INSIGHT INTO PLANT CELL WALL DEGRADATION AND PATHOGENESIS OF GANODERMA BONINENSE VIA COMPARATIVE GENOME ANALYSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: Having looked at the paper I am happy that the authors have done all the required amendments and the paper is now acceptable


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: CHARGE AND HYDROPHOBICITY ARE KEY FEATURES IN SEQUENCE-TRAINED MACHINE LEARNING MODELS FOR PREDICTING THE BIOPHYSICAL PROPERTIES OF CLINICAL-STAGE ANTIBODIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Line 79: The sentence that starts with ‘Clustering of…’ is unclear. Please rephrase it.
Line 136: Give a reference for ‘fitting to a priori approximation’.
Line 147: Give references for validation approaches.
Experimental design: Line 40: A reference for ‘excipient effect’ would be welcome here.
Line 97: Please explain the rationale behind the composite scores.
Line 108: Why did authors assume linearity in their models? What’s the rationale behind?
Line 142: Why 11 models were chosen, which were the selection criteria?
Line 229: How were the sequences concatenated? How did the authors deal with unequal sequence length? How does this translate into processing of an input for your online tool?
Figure 3: How was the heatmap constructed? Are we looking at plain Pearson-correlation coefficients?
Validity of the findings: Line 48: Authors should recognize here semi-empirical tools like mAb Rosetta, which benefit from data, but also theoretical calculations and optimization.
Figure 2: The HIC data, disclosed in Figure 2,  depict a non-linear, 2-state like model.
Line 80: The novelty of authors approach is not clear.
Line 238: Can a correlation of R^2<0.5 be regarded as an accurate prediction?
Line 240: Could authors compute the correlation coefficient for higher-HIC values sample?
Line 263: How do authors know the charge of CDRs? Do BVP contain negatively charged proteins, or perhaps vast amounts of negatively charged phospholipids?
Figure 4: How did authors compute the ‘absolute charge’ of a protein?
Line 305: How did authors arrive at this conclusion? What's the evidence supporting the intermolecular repulsion vs retention hypothesis. Have authors analyzed SINS-type of assays. Is there a correlation with these?
Line 349: The conclusion that ‘linear models can account for much of the variation’ is simply contradictory to the finding reported in Line 292.
Additional comments: I would like to commend the authors for uptaking a truly daunting task of building sequence-based models for mAb developability assessment. The online tool presented by the authors holds a promise of accelerating the rational design of therapeutic mAbs.

However, I do believe the manuscript is not suitable for publication in the current form.

The word ‘charge’ appears throughout the manuscript 42 times. However, it is evident that authors refer here to a relative number of titratable residues. Thus the manuscript needs to be rewritten to make it clear that no charge-charge calculations are done and that intrinsic biophysical properties of amino acids only are used in the design of the study.

The title of a manuscript implies that the said machine learning methodologies can be used in the prediction of biophysical properties, yet what is predicted are ‘normalized’ values of developability screening techniques, which are de facto distant proxies of biophysical properties, such as, self-aggregation or intrinsic solubility.

The study disclosed in the manuscript suffers greatly from a lack of description of the model selection process and (it seems) an arbitrary selection of ML methodologies. The study demands a question, why would one choose a specific ML methodology? Is there an added benefit, e.g. the ability of the method to capture a biophysical property that goes beyond an optimization against a simple R^2 metric?

The conclusions for HIC calculations are contradictory to the main takeaway of the results section: the HIC profile is not linear, in fact displays a two-state-like behavior, thus it begs to be fitted with (at least) two independent lines.

Finally, the manuscript does not explain the relative benefit of authors’ approach with respect to the existing sequence-based prediction methods. Could the existing tools be successfully used to arrive at the conclusions of this study?


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

Input:
Title: CHARGE AND HYDROPHOBICITY ARE KEY FEATURES IN SEQUENCE-TRAINED MACHINE LEARNING MODELS FOR PREDICTING THE BIOPHYSICAL PROPERTIES OF CLINICAL-STAGE ANTIBODIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I think this is a potentially interesting contribution on understanding of antibody biophysical properties and the web-server provided is functional and easy to use.

1. My main concern is the size of the dataset. There are only 137 proteins but 35 features are used which is very easy to get over-fitting using machine learning approaches. Is it possible to collect more proteins with experimental data from other papers?
2.  Are there any similar methods available to compare the prediction performance?
3.  In Uemura et al (2018),  it is reported that the molecular size and the solubility are negatively correlated. Could you also check the correlation between the protein size and biophysical properties? If the correlation is high, it might be used as one feature.

Could you also show the correlation between the experimental values and the most important features, e.g., charge and hydrophobicity?

4. For some datasets, for example, HEK and DSF, the machine learning models give worse predictions. Could you explain why?
5. I think the definition of ‘biophysical properties’ need to be better explained in the introduction. Which biophysical properties?
6. The figures in Supplement files are hard to read and need a higher resolution.


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: QTQDA: QUANTILE TRANSFORMED QUADRATIC DISCRIMINANT ANALYSIS FOR HIGH-DIMENSIONAL RNA-SEQ DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is well written, with the standard sections.

A comprehensive review of current methods is done, with a good comparison among them.

In several places it is said that a R library with the implementation is available, but the name is not given, although it is straightforward (qtQDA).

And the web page is also not given : https://github.com/goknurginer/qtQDA
Experimental design: The research question is well defined, it is important to have a way to classify samples based on its rnaseq results. An in-deph mathematical study is done.

But, in my opinion, it would be worthwhile to add an algorithm for the case where there are paired samples, that is, tumoral and healthy samples from the same person. That would make the results more precise, but would need a different processing.

And it would be interesting to know how it would be used if the whole RNA is used, so the repetitive elements are incorporated to the data used. But I can understand that that would be material for a new paper.
Validity of the findings: The cases and the comparison with previous work is very well done, and the results supports the authors in their findings.
The advantages are clearly exposed, but I think that being computationally fast is not a big advantage, as the whole processing needed to reach the stage where the classification is done is much bigger, as the reads must be aligned, etc, and this takes a lot of computing power.

But I would like to see an explanation of why so many genes are used for classification. Why not use only a few genes ? that would make the use of PCR technology feasible, as less genes would need to be used in the classification, making it more economical.
Additional comments: None


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: QTQDA: QUANTILE TRANSFORMED QUADRATIC DISCRIMINANT ANALYSIS FOR HIGH-DIMENSIONAL RNA-SEQ DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this manuscript the authors described a new classification method, qtQDA, that is based on a model where the data is marginally negative binomial but dependent. The authors compared their method with other existing approaches and found that qtQDA performs better in most cases than the other methods.
In my opinion this is a good work and the manuscript is written in a clear and concise manner. I tested the R package with the implementation of the method, and everything worked well.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: My only recommendation is that a user’s guide is included in the R package with the different options explained and practical examples given, similar to the edgeR users guide. I realize that each function is explained in the help section of the package but the integration of all the information in a single downloadable pdf file would greatly benefit the users. I especially would like to see a more detailed explanation on the three options for the dispersion estimates that even though are part of the edgeR package and are explained in their user’s guide, significantly impact the usage of the qtQDA method.


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: QTQDA: QUANTILE TRANSFORMED QUADRATIC DISCRIMINANT ANALYSIS FOR HIGH-DIMENSIONAL RNA-SEQ DATA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The comments have been addressed in the text.
Experimental design: No changes from the previous review, it can be published in its current form.
Validity of the findings: I continue thinking that selecting automatically a smaller set of genes would provide an interesting view of the difference among the samples, providing the opportunity to know better the underlying mechanism causing that difference.
But I understand that this can be out of the scope of the present work.
Additional comments: None.


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: QTQDA: QUANTILE TRANSFORMED QUADRATIC DISCRIMINANT ANALYSIS FOR HIGH-DIMENSIONAL RNA-SEQ DATA
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have answered my comments and I have nothing else to add.


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

Input:
Title: EVALUATING PROBABILISTIC PROGRAMMING AND FAST VARIATIONAL BAYESIAN INFERENCE IN PHYLOGENETICS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript describes the first application of variational inference for Bayesian phylogenetics. This work is quite pioneer work, which has the potential to have a strong impact in the phylogenetics comunity. The manuscript is well written and easy to follow, in spite of the difficulty of this topic.
Experimental design: The methods were carefully designed and relevant to the aims of this study. However, there are a few points that are unclear and potentially important to assess the utility of variational inference:

1- Fig 3 shows effective population size reconstructions using four methods. That from BEAST has higher uncertainty. This could be due to uncertainty in the tree topology, which is not accounted for in variational inference. Can the authors confirm whether the tree topology estimated in BEAST, or fixed as in the other methods. If it is the latter, is there a potential for biassed estimates using variational inference? How does this affect run time?

2- Fig 2 shows the posterior estimates of several parameters. A couple of variational inference replicates were different. I think some guidelines are missing here. For example,
how many times should one run variational inference? Should one take the mode or a an average?

3- I realise that an extensive comparison of methods to approximate the posterior distribution is beyond the scope of this study, but I do think readers would appreciate some discussion and comparisons with sequential Monte Carlo, which is an other alternative to MCMC that might be more amenable to large data sets.

4- The difference in computing time between physher and stan is over three orders of magnitude, and it has been attributed to the starting values, where physher uses an optimisation step whereas stan has random starting points. Would this be a problem for parameters with local optima or for those that are unidentifable? For example, when calibration data are not very informative, the posterior on root height and clock rate are rather flat and difficult to sample using MCMC.
Validity of the findings: The findings are easily replicated and the authors have made substantial effort to document their code and examples in GitHub.
Additional comments: I am happy to recommend this manuscript for publication after my points in section 2 are addressed.


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

Input:
Title: EVALUATING PROBABILISTIC PROGRAMMING AND FAST VARIATIONAL BAYESIAN INFERENCE IN PHYLOGENETICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is on fixed topology inference, but the introduction mentions NNI and SPR moves before backing down later. A reference to fixed topologies in the abstract would not bring up hopes, and would more accurately reflect the contents of the paper.

line 34: "etc" => "etc."

lines 108-109 suggest Gaussian distributions are used for GTR rates, branch lengths, but they are log transformed version of it, right? Otherwise, there will be support for negative branch lengths and GTR rates.

Figure 3 could be improved by either plotting all trajectories on top of each other, or at least add a grid across all backgrounds so that different trajectories can be compared more easily.

Figure 4: axis represent *log* posterior probabilities?

An omission is the way the tree priors are described -- since these are coalescent priors and even on a fixed topology suffer from discrete jumps. The trees ((a:1,b:1):2,(c:2,d:2):1) and ((a:2,b:2):1,(c:1,d:1):2) are two differently ranked topologies, so how does the tree prior, in particularly the derivatives deal with these?

A description of the parameterisation (if any) for frequencies and substitution model rates would be nice to have as well.

line 136 "requires an adjustment to the joint density" how exactly?

line 190: missing reference.
Experimental design: Line 58 promises "1000s of sequences", but the largest data set in the experiments is only 69 sequences. Please add a more substantial data set.

A coverage experiment (draw 100 parameter + tree sets from prior, count how often the true values are inside the 95%HPD of the variational distribution) would provide much more insight in the behaviour of the methods. Anecdotal evidence from a handful of datasets is interesting, but not as illuminating.
Validity of the findings: Results are hard to replicate due to missing BEAST XML files, alignment files, phylostan and physher runtime settings. Please provide these.

It is unclear from the documentation how to run physher for variational inference (assuming I can find it at https://github.com/4ment/physher, which was not clear from the manuscript, and the referred paper only mentions a google code archive). Please update the documentation.

How do we know variational inference in physher is correctly implemented? There is no evidence provided as for phylostan (through Figures 1 & 2). Adding these would make the results more credible.

A performance comparison with Zhang & Matsen (2019) would greatly enhance the paper.
Additional comments: line 91: Trees tend to contain the majority of the parameters: for n taxa, there are 2n-1 parameters for the topology (parents for all nodes) + n-1 heights of internal nodes + potentially n heights for tip nodes (if estimated). The number of parameters for the site model tends to be tiny compared to that of the tree, which suggests solving site model inference is just a small part of the solution. It would be good if you substantiate the claim that "Despite this limitation, implementing the type of model we describe here under a fixed tree is a useful step forward toward fast Bayesian in-ference of complex phylogenetic models, as it helps us understand the quality and speed of posterior approximation that can be achieved using a generic modelling language like Stan".

lines 243 ff: I find the discussion a bit confusing: the line seems to be that stan has significant costs, justifying implementations in other packages, which admittedly can be tedious because it requires gradients, which should be obtained from stan. Should we use stan or not? Can the improvement of the phylostan be attributed to more efficient gradient implementations or other parts? How do you know?


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

Input:
Title: A SYSTEMATIC REVIEW OF THE APPLICATION OF MACHINE LEARNING IN THE DETECTION AND CLASSIFICATION OF TRANSPOSABLE ELEMENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript seems to be a report, not a review article. The authors should carefully reconsider and revise the structure of the manuscript. For example, the chapters "Search strategy" and "Selection of articles" are lengthily but contain few information. It is not difficult to shorten them without loosing any information.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Orozco-Arias et al. reported a systematic review of 35 papers/reports that detected and classified transposable elements (TEs) in genomes by applying machine learning (ML) approaches. For each study, the authors summarized addressing the following 4 points:
1. Are ML approaches for TE analyses advantageous compared to bioinformatics approaches?
2. Which ML techniques are currently used to detect and classify TEs or similar data?
3. What are the best parameters and most used metrics in algorithms and architectures to detect and classify TEs?
4. What are the most used DNA coding schemes in ML tasks?

The manuscript contains something informative to the current studies of TE identifications; however, it is not well organized and insufficient as a review article. First of all, point #1 raised by the authors seems to be the most important part in the review, but it not well answered in this review. I would like to know how ML (and DL) approaches improve the identification and classification of TEs in various species compared to the conventional (i.e. homology-based) approaches. How much species have been analyzed yet, and are there any species that are in particular suitable for ML-based search? How did they distinguish whether the search results were true-positives or false-positives? In addition to that, please consider the following comments as well.

Comment #1
In the title, the word “deep learning” should be deleted because as shown in the Figure 6 and Table 3, many (almost all) papers mentioned in the review is not based on a deep learning approach. Or if the authors include it in the title, DL-based approaches should be mentioned more in this manuscript.

Comment #2
In the Introduction, Figure 1 shows a detail classification of TEs; however, no explanations were not provided. Due to the diversity of TEs, the identification and classification of TEs are difficult. Therefore, to understand the importance of this review, the more detailed explanations of TEs are essential.

Comment #3
Figures are not easy to read. In particular, now many researchers including me believe pie charts should be avoided (please see https://www.data-to-viz.com/caveat/pie.html, for example).

Comment #4
In the Table 3, data source is not clear. For example, what is “RNA” or “DNA”? What is the differences between “k-mer frequencies” and “oligomer frequencies”?

Comment #5
References should be carefully revised.


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

Input:
Title: A SYSTEMATIC REVIEW OF THE APPLICATION OF MACHINE LEARNING IN THE DETECTION AND CLASSIFICATION OF TRANSPOSABLE ELEMENTS
Review round: 1
Reviewer: 2

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: A SYSTEMATIC REVIEW OF THE APPLICATION OF MACHINE LEARNING IN THE DETECTION AND CLASSIFICATION OF TRANSPOSABLE ELEMENTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors should clearly define what they mean with the TE tasks they are addressing. They mainly talk about TE detection and TE classification, but it would be good to properly define these tasks. Moreover, in the text they also talk about TE identification, TE prediction, TE analysis,... It is not clear whether these are considered as synonyms for detection or classification, or denote different tasks.

The formulation of the research questions should not involve methodological details (e.g. question Q2).

The structure could be improved. Some paragraphs in the response to the research questions (e.g. Q1: the paragraph starting with "In plants, TEs have been related") are more suited for the introduction.

It would be good to end each research question response with a small paragraph, summarising the answer to the research question.
Experimental design: In the Survey Methodology section, the text is well structured into the different steps, but it would be more clear for the reader if the exact same terminology as in Fig 2 is used (throughout the text and for the section titles).

I'm wondering whether there was a search criterion related to the publication date, since all included articles date from 2009 or later. Does it mean that there were no publications on this topic prior to 2009? (This would seem to contradict the fact that there is a review paper from 2010 on this topic.)

The response to research question Q2 also involves publications that apply ML to data similar to TEs. However, here the article seems to be less systematic in its review. In any case, it is not clear how the discussed publications are selected.
Validity of the findings: The results seem valid.

However, in the response to Q2, I'm not sure what an analysis of the programming language used to implement the machine learning algorithms adds to the contribution of this paper.

Also, for Q3, concepts of training/validation/test set, cross validation, and all the evaluation measures considered are not at all specific for TE detection or classification. These are concepts used in any machine learning study. Furthermore, I assume the evaluation measure will depend on the task, i.e. TE detection will require different evaluation measures than TE classification.
Additional comments: My main comments have been covered by the 3 areas above.

Some minor comments:
- The caption of Fig 6 seems to be incomplete.
- As far as I know, "neuronal networks" is not standard terminology. Please change to "neural networks".


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

Input:
Title: A SYSTEMATIC REVIEW OF THE APPLICATION OF MACHINE LEARNING IN THE DETECTION AND CLASSIFICATION OF TRANSPOSABLE ELEMENTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript was improved; however, I still have minor comments as follows:

On page 4: I do not know why the authors show only the first author as the research conductor in the line 155. Is it based on the guideline of systemic review of Moher et al., 2009? I think that “We” may be more suitable.

On page 5: “TEs or similar data” is ambiguous. What is similar data?

On page 7: The term “bioinformatics software” is also ambiguous. The authors may infer “bioinformatics software” as homology search-based software. The authors should carefully explain these words because it could be essential in this review.
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: A SYSTEMATIC REVIEW OF THE APPLICATION OF MACHINE LEARNING IN THE DETECTION AND CLASSIFICATION OF TRANSPOSABLE ELEMENTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Most of my comments have been addressed. However, I still have the following remarks, which all fall under basic reporting.

The authors removed 'deep learning' from the title, as suggested by a reviewer. This is fine, but then it should be consistently removed also from the abstract and from many places in the text where 'ML and DL' are always mentioned together.

The article contains many grammar mistakes, especially in the newly added text. To give a few examples:
- Each sub-class is then classify into orders regard to the structure features and life cycle as in the case of retrotransposons (...) and finally each order is then classify into superfamilies.
- In ML algorithms, it seems to be more common and get better results k-mers frequencies.

The second paragraph of the introduction has become unnecessarily lengthy by listing all lineages. I still believe it would be good to properly define the tasks of identificaton on the one hand and classification on the other hand. Also refer to Figure 3.

Q2, Q3 and Q4 now end with a paragraph summarizing the findings, as suggested. By starting these pragraphs with "To summarize,..." the text would be better structured and easier to follow for the reader. Also Q1 would benefit from such a paragraph.

In the section on Survey Methodology, in the sentence "We conducted an exhaustive literature review", the word "we" was replaced by the first author's name. This is not done. If the authors wish to make statements about author contributions, they should consult the journal editorial team on how to do so.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: COMPARISON OF DIVERSITY AND COMPOSITION OF MACROFUNGAL SPECIES BETWEEN INTENSIVE MUSHROOM HARVESTING AND NON-HARVESTING AREAS IN OAXACA, MEXICO
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are no page numbers in the manuscript.

There were a few typos and some information was lacking from the literature references. I would recommed to check there carefully.
Experimental design: One season study for mushroom fruitbody communities is not able to capture all or not always the majority of the species (see the non-saturating curves of rarefaction and accumulation is figure 1.). This may have an impact on the results and therefore it should be clearly stated both in methods and discussion why the results are presented based on 1 year sampling because most studies on this topic are based on 2-3 (or more) years inventories. It is also important to note the reader that the rarefaction curves do not saturate.

There was unintentional harvesting by the local people. This is an important point as it may have an impact on the results and it should be more clearly stated in the manuscript.

Aboveground mushroom community is not the same as the belowground community. More information of the community could be achieved by doing molecular analyses from the soil. I would like to see justification in the introduction/matmet why the authors decided to carry out this project based on mushrooms only.
Validity of the findings: The results indicated that harvesting did not have an impact on the fruitbody communities but that environmental variables were able to explain the findings to some extent. Although I consider the scientific value of this manuscript not be be very high, I still would like to see it published after revision. There are relatively few studies on mushroom fruitbody communities. Therefore I think it would be good to get publications on this topic.
Additional comments: The authors hypothesized that harvesting does have an impact on the mushroom yields.  However the results indicate that harvesting did not have an impact but that the weather and environmental conditions play more important role. This is what can be expected: mushroom fruitbody yields are very dependent on environmental conditions. Especially the different weather conditions may  cause notable differences between years. In addition, I am especially concerned if the results were affected by unintentional harvesting of “the non-harvesting treatment plots” which was suggested in the discussion. I think this is an important point and should be mentioned already in the Materials and methods.


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: COMPARISON OF DIVERSITY AND COMPOSITION OF MACROFUNGAL SPECIES BETWEEN INTENSIVE MUSHROOM HARVESTING AND NON-HARVESTING AREAS IN OAXACA, MEXICO
Review round: 1
Reviewer: 2

Output:
Basic reporting: Sentences could be improved in English. References cited in the Introduction are relatively old. Raw data are available but not very well annotated.
Experimental design: The content of the paper is within the scope of the journal, but does not very well correspond to the title of the paper. The design for the field investigation is ok, but the data obtained are not dependable. Pl. see the problem with methods in the comments.
Validity of the findings: Pl. see above.
Additional comments: 1.	Lines 44-51: Since the article mainly focuses on mushroom harvesting and its effects on macromycetes, it is suggested to add some information on the relationship between mushroom and macromycetes but not mycorrhizal fungi and pathogenic fungi.
2.	L62-63: it is suggested to delete the sentence since it is about eating culture and habit, which may influence on mushroom harvesting, but not directly be related with the topic of the article.
3.	L86-99: it is suggested to simplify this paragraph. For example, using one sentence to outline the paragraph and having it integrated into the previous paragraph.
4.	It is suggested to restructure the paragraph of L100-110. Purposes of composing this paper should be stated clearly, but not the predictions.
5.	The references cited in the Introduction are restively old. It is suggested to use as many latest references as possible.
6.	L114-121：since no specific village name is mentioned in the paper, it is suggested to change village to four sites. “surrounding Independencia” means not in or inside the Independencia.
7.	L133-134: Since mushrooms are ephemeral, sampling conducted every week seems to have a too long interval. Was sampling not done on a daily basis? Or only the calculation of sample quantity was conducted on a weekly basis?
8.	L123-127: it is stated that the characteristics of the selected sites were as similar as possible in terms of altitude, tree composition, vegetation structure, topography of the terrain, and understory coverage. It is suggested to have a more detailed description of these aspects.
9.	L147-149: please specify the bulk density of the four sites, not the criteria for the division of the bulk density.
10.	Since a paper is composed of written sentences, but not oral sentences, it is suggested to use as many written sentences as possible. For example L151-153.
11.	For explanatory variables, no specific description is available in the paper and readers have to read raw data / supplementary files. It is suggested to have a summary description for each variable. No title is available for supplementary files 2 and 3 and no unit for each variable in the file 3 although they are supplementary files.
12.	It is suggested to describe explanatory variables first, followed by macromycete sampling.
13.	Appendices A and B could be combined into one, with edible species marked with asterisks in Appendix A. Latin names of some species in the appendices have no space between two words. Pl. add notes to the appendices to explain sp. 1, sp. 2, etc. Do they mean species unidentified?
14.	L179-180: are Basidiomycota and Ascomycota two extremes of species richness? Description is not very clear.
15.	In L155-166, it is stated that both effectiveness of the sampling effort and the completeness of the macromycete inventories were estimated. So other data analyses should be based on the estimation of effectiveness of sampling and completeness of inventories. As stated by authors, the effectiveness of sampling efforts and completeness of inventories were not as good as expected, validity of the data is questionable.
16.	Since the topic of this paper is to study the effect of intensive mushroom harvesting, harvesting intensity (for example, weekly harvesting quantity) should be mentioned in the paper, but nothing is read. According to the paper, only are harvesting and non-harvesting described. In addition, according to the design, analysis of variance could be performed to see whether there is significant difference between harvesting and non-harvesting, based on which further detailed analysis of reasons behind the phenomenon could be continued. A richness-based result and clustering of species composition indicating no influence of harvesting are not dependable.


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: EXPLORING SNAKE OCCURRENCE RECORDS: SPATIAL BIASES AND MARGINAL GAINS FROM ACCESSIBLE SOCIAL MEDIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written, clear and structured.  The authors give a succinct summary of the relevant background information.  I would be interested in a little more elaboration on which taxa social media records have been most successful in providing information on but this is a minor point - all the relevant citations are given in the text.
Experimental design: The methods are generally well described and code is provided.

Lines 173-181.  I got a little confused here.  It sounds like you randomly selected 9 species and then randomly selected a further 9.  But I don’t think you did?  Could you rewrite this paragraph to make it clear please?  Thanks.
Validity of the findings: The results are given clearly and concisely.
Additional comments: Might there be other factors which explain the number of occurrence records?  Rarity, threat status, body size, habitat use or other ecological traits?  I appreciate you do say in the discussion that species that are brightly coloured/large have more Flikr records.
Line 61: You are missing a fullstop.
Line 83: Typo, ggplot2

Line 348: ‘data deficiency’ not ‘deficient data’


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: EXPLORING SNAKE OCCURRENCE RECORDS: SPATIAL BIASES AND MARGINAL GAINS FROM ACCESSIBLE SOCIAL MEDIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general, I think the paper is well written, clear and unambiguous. The hypotheses are well presented. The list of references cited could be a bit more complete. I detected two English mistakes in line 95 “all recorded (records)” and line 355 “However, while improvements in occurrence data my (may) help identify current distributions…”
The last sentence of the abstract is not consistent with the results obtained “We suggest that researchers studying species with low detectability or limited data consider integrating social media records into occurrence datasets (if available), so long as photographic identification is viable.”
Experimental design: The research presented suits well the aims and scope of the journal. The research question is well defined, relevant and meaningful. This paper is anchored in an area of research in wide expansion and that relies on information collected by citizens in social media. However, I missed the inclusion of data from global citizen science projects such as iNaturalist, iSpot, Atlas of Living Australia, Observado among others. I believe that the results obtained could have been different if this information were also used. Opportunistic citizen science databases of species observations can represent a viable alternative to scientific records when these are not available, and the challenge might be to combine different data sources to achieve better results. Materials and Methods were described with sufficient detail allowing the results to be replicate. The way they were presented shows rigorous investigation.
Validity of the findings: With the experimental design presented I felt a bit disappointed with the results obtained. The paper “highlighted that there is significant spatial bias in the GBIF records for non-marine snakes, with gaps in tropical regions”. The authors encourage the investigation of supplementary data sources to help fill gaps in biodiversity databases, currently accessible social media occurrence records only improve species distribution models marginally.” I would like to see a bit more of this supplementary data sources studied like, for instance citizen science data or other social networks.
Additional comments: I like the paper, the question raised, and approach followed by the authors however, since the results do not seem very strong, I would like to see some more analysis performed with other data sources.


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: EXPLORING SNAKE OCCURRENCE RECORDS: SPATIAL BIASES AND MARGINAL GAINS FROM ACCESSIBLE SOCIAL MEDIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: Currently, I don’t feel the introduction flows particularly well. To address this I suggest a broader opening paragraph in the introduction discussing the value that SDMs have in the ecological literature. Add some examples of the types of research they have been used for, this could include the current introduction section on threat assessments. The next section could be focussed on the data sources and issues surrounding them for SDMs. Next you could add the introduction of snakes as a model system here. Finally, end with a clear set of aims for the study.
Experimental design: Generally, the methods are clear and easy to follow. However, there are a couple of points that need additional detail to ensure readers can replicate the study.

Line 129: In the interest of reproducibility, how was “geographic proximity to zoos” assessed? For example, were photos within 1km of a zoo excluded?

Line 145: Please describe how these variables were downscaled.
Validity of the findings: The addition of the social media data resulted in only marginally different niche estimations and negligible difference in Maxent model performance, however the authors still recommend readers acquire the extra data sources. I feel an obvious question is why bother going through the effort to extract extra data sources when they appear to have little impact on the result? Particularly given the difficulty in accessing these data and ensuring their reliability (presumably this was not a quick job – Line 126: suggests manual verification of at least 45000 snake photos!). I feel a discussion around this question is important, and perhaps a line in the abstract summarising why we should seek additional data would be useful.
Additional comments: The authors present an interesting study where they assess the added value of including distribution data scrapped off social media (geo-tagged species images from Flickr in this case), to species distribution model performance. The key result was that SDMs which included data derived from social media had only a very minor improvement in model performance compared to those based purely on GBIF data. The authors rightly highlight the need for macroecological studies to utilise as many data sources as possible, particularly when studying species with low detectability. Please see my additional comments on the study below:

Firstly, the code to extract and clean data from GBIF is useful, however the code for extracting images from Flickr is exceptionally useful, particularly given the main message of this paper (i.e. use these other data sources!). I feel the authors could make more of this in the paper, for example add a sentence to the abstract saying “we provide code for extracting geo-tagged images of species from Flickr”. This code is not only relevant for the types of study we see here, but also to those interested in putting together photo libraries for training image recognition algorithms, a growing area in ecological research. I feel this simple change would add value to this study, increasing citations of the paper and the associated code.

Minor comments:
Lines 41-49: Do the IUCN actually accept SDM outputs as part of the species assessments?

Line 66-68: The two questions seem oddly placed here. Suggest rephrasing this from a question to a point, i.e. it is not known how…

Line 131: missing “(“ before Fick.

Line 262: Please add the direction to this association, i.e. weakly positively associated.

Line 355: typo- “may” not “my”

Figure 3: Could this be ordered by number of GBIF records. I feel this would emphasise the variation in ranking (based on n records) when compared to Flickr.


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: EXPLORING SNAKE OCCURRENCE RECORDS: SPATIAL BIASES AND MARGINAL GAINS FROM ACCESSIBLE SOCIAL MEDIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am happy with the changes the authors made in response to my comments.
Experimental design: I am happy with the changes the authors made in response to my comments.
Validity of the findings: I am happy with the changes the authors made in response to my comments.
Additional comments: I am happy with the changes the authors made in response to my 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: EXPLORING SNAKE OCCURRENCE RECORDS: SPATIAL BIASES AND MARGINAL GAINS FROM ACCESSIBLE SOCIAL MEDIA
Review round: 2
Reviewer: 2

Output:
Basic reporting: I think the new version of the paper answers the questions raised and clarifies the results obtained. I think the publication is appropriate and interesting for the scope of the journal. The new literature cited is adequate and responds to the requests of the reviewers
Experimental design: The reviewers' suggestions were taken into consideration and the answers given were enlightening.
Validity of the findings: The major problems identified have been resolved.
Additional comments: I like the paper, the question raised, and approach followed by the authors. The authors resolved the questions raised by the reviewers


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

Input:
Title: THE INTERPLAY BETWEEN MOVEMENT, MORPHOLOGY AND DISPERSAL IN TETRAHYMENA CILIATES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Mostly the text is very clear. The Figure and Table legends require more information. For instance, describing what the different symbols refer to.
Experimental design: The experimental design is sound and clearly described. I found the description of the statistical analysis and results for the second question very difficult to follow. Please see my comments to the author.
Validity of the findings: no comment
Additional comments: This study investigates the genetic and environmental link between movement, morphology and dispersal across 44 Tetrahymena genotypes. First they describe how movement behaviour, morphology and dispersal is linked within and across the 44 different genotypes, before quantifying how much variation in dispersal can be attributed to these differences in morphology and movement. They show that relationships between these traits have both a genetic and environmental component. Some genotypes had a greater tendency to disperse, however, across all genotypes there was a difference in morphology between dispersers and residents.

Overall I enjoyed reading this manuscript and recommend it for publication in PeerJ. My major concern is that I found the description of the analyses and results for question 2 (link between movement and morphology) very difficult to follow. Some things became clear from simultaneously looking at the figures and supplemental Tables, but this information should be clear from the main text. Please see my more detailed comments below.

Lines 54 – 56: maybe add that dispersal movements are necessarily in sub-divided populations.

Line 73: Add reference for ‘environmental causes’.

Line 84: is there a general effect of body condition on dispersal across species, or is it species and context specific?

Lines 91 – 104: this paragraph logically follows on from line 80. Also, on first reading I thought this contradicted the information presented in lines 76 – 80. Before you state there is new technology to investigate dispersal, then here you state difficult to track long-distance dispersal. But on a second reading I see that lines 91 – 94 are talking about genetic effects and before (lines 76 – 80) the genetic component could not be disentangled. This could be stated more explicitly.

Line 104: you could state here what the next step needs to be. A study across lots of genotypes which is easily done with microcosm experiments.

Lines 112 – 121: Changing the order of these sentences might provide a better context for your study. I’d put the last sentence first and change it to say ‘There is compelling evidence that dispersal in this organism………’, then the second sentence describing all these studies and finally say ‘There is extensive variation among genotypes……’. Then you could say how the present study advances on Fjerdingstad et al. 2007 and Pennekamp et al. 2014.

Lines 122 – 131: Describe Fjerdingstad et al. 2007 and Pennekamp et al. 2014 in more detail. Were the same genotypes used? And then frame the questions so that it is clear how this study is different.

Line 152: add the length of the tube.

Line 161: add that there were 5 photos taken, 1 for each chamber. You could add the text from lines 60 – 64 of the supplemental material.

Line 177: ….all the….

Lines 192 – 197: It is not clear how this measure also integrates step length and turning angle?

Line 201: The term ‘dispersal system’ is introduced out of the blue. State earlier on that your 2 patch population (or maze) is referred to as a ‘dispersal system’.

Lines 231 – 237: This is quite confusing. Change ‘condition-dependence of movement’ to ‘to see if there were differences between residents and dispersers’. It is unclear how the models were constructed. Was movement speed and tortuosity measured separately in 2 models each with size and shape as fixed factors? From the supplemental material it looks like there was one model for size and another for shape on each explanatory variable.  This should be stated. Why not do one model with both size and shape? How did you account for differences in dispersal status in these models (lines 233 – 234)? From the supplemental material it looks like ‘start’ or ‘target’ tube was included in models. This should also be stated. And then were models repeated with the mean value for each genotype (lines 235 – 236)? If this is the case were means for genotype calculated as the mean for each replicate and then the mean of these two replicates?

Line 253: This contradicts the previous sentence. Maybe say in the previous sentence that for this was the result for majority of genotypes.

Lines 264 – 266: this sentence doesn’t make sense. Table S4 shows this to be the most parsimonious model ‘log(FractalD - 1) ~ size + tube + size:tube + 1’, which to me means that there is a significant interaction between size and disperser/resident for tortuosity.

Lines 270 – 276: this is really confusing.

Lines 293 – 295: The end of this sentence is unclear.

Lines 317 – 321: I don’t completely follow the logic here. Is there any evidence that your movement behaviours are linked to foraging? And why only in non-territorial animals?

Line 322: change ‘currently receives more attention’ to ‘has recently received more attention’ and you could describe this study in more detail.

Lines 360 – 364: this sentence is confusing.

The tables in the supplementary material (Table S2 – S13) are confusing. What is tube in these models? Each Table should have a legend at least stating what the response variable was? Is the model in bold the one which was retained?

Legends should be included for the figures in the supplementary materials?

Figure 2: are the circles and triangles dispersers and residents? This information should be in the figure legend.

Figure 3 looks like it shows the means for replicates and dispersers for each tube. Was this the response variable in the analyses described in lines 231 – 237?

Table 1: add the denominator degrees of freedom.