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: KINEMATIC CHARACTERISTICS OF BAREFOOT SPRINTING IN HABITUALLY SHOD CHILDREN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article should include enough introduction and background to demonstrate how the work fits into the broader field of knowledge. The references are very old, you should include important references such as the following:

Latorre-Román, P. Á., Párraga-Montilla, J. A., Guardia-Monteagudo, I., & García-Pinillos, F. (2018). Foot strike pattern in preschool children during running: sex and shod–unshod differences. European journal of sport science, 1-8.

Latorre-Román, P. Á.L., Balboa, F. R., & García-Pinillos, F.  (2017). Foot strike pattern in children during shod-unshod running. Gait & posture, 58, 220-222.

Muñoz-Jimenez, M., Latorre-Román, P. A., Soto-Hermoso, V. M., & García-Pinillos, F. (2015). Influence of shod/unshod condition and running speed on foot-strike patterns, inversion/eversion, and vertical foot rotation in endurance runners. Journal of sports sciences, 33(19), 2035-2042.

Paragraph 78-86, how the mass of the shoe influences on the kinematic or FSP parameters?

The limitations and practical applications should be included, for example:
Limitaciones:

Shod/unshod condition must be randomized
The age, sex and antropometric influences should be analyzed
The rubber surface is another limitations

Discussion

The purpose showed in discussion section must be the same expressed in the introduction section. Be consistent with the terms.

Previous studies of Latorre et al., should be taken into account.

Practical aplications:

 Why the children should run barefoot at high speed?
Experimental design: Partcipants:

Other inclusion criteria should be included: barefoot experience, level of physical activity, physical and / or intellectual disabilities, etc.

Data collection and processing

How the FPS were analyzed ?, by observational method.

How do you know that the unshod condition could influence on the shod condition and not the other way around? Therefore, shod / unshod condition must be randomized,

Statistical analysis

To analyse the foot strike patterns (FSP) differences between the shod/unshod condition, McNemar’s test must be used
Validity of the findings: No coments
Additional comments: Thank you for the opportunity to review this manuscript. I have listed some specific comments below for your consideration. Please regard them as constructive recommendations. The paper is well written and is methodologically correct.


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: KINEMATIC CHARACTERISTICS OF BAREFOOT SPRINTING IN HABITUALLY SHOD CHILDREN
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1a) The use of English is appropriate and the writing style is easy to follow and understand
1b) The literature is scarce. Only 18 references are used, one of them is data of the Japanese Ministry and almost half of the references are from the 80's or 90's. Very relevant research, including very recent from Japanese colleagues who analyzed sprinting mechanics in Japanese children using a 50-m long force platform system is not reference, as well as the works by important authors on this topic such as Morin et al. Both the introduction and discussion should be significantly updated to include more recent and relevant literature.
1c) Article is well structured and the raw data is properly shared
1d) The purpose of the study is clear (i.e., to analyze the potential differences between running conditions in children), and the results are in line with the purpose of the study.
Experimental design: 2a) The purpose is relevant and original
2b) Research question is well defined, and it is justified how it adds to the current body of literature (i.e., there are known differences between running barefoot or with shoes in adults, but not in children)
2c) The study follows all ethical standards and the investigation have been performed in a rigorous way
2d) Methods are clear enough so the study could be replicated by another group of researchers
Validity of the findings: 3a) No comment
3b) Data is fully available in a spreadsheet. However, statistical analysis are quite weak as they are only based on the NHS and no effect sizes or CI are reported
3c) The authors fail to link the main result of the manuscript (i.e., sprint performance in barefoot condition is impaired) to their conclusion, as they don't critically discuss how this might affect training strategies or how coaches should use this information. They rather discuss how running barefoot could be used to develop proprioception and prevent injuries; variables that were not measured at all in the manuscript, nor was the purpose of the investigation
3d) Claims that running barefoot could potentiate proprioception and prevent injuries are not adequate and are not linked to the purpose of this investigation, since no single variable related to injuries was tested (authors even required participants to not be/have been injured, so potential links to injury prevention in a retrospective way is not possible)
Additional comments: Dear authors, thanks for your interesting manuscript. It is a well written study that covers an unstudied topic (i.e., comparing barefoot vs shod running in Japanese children), but it has some flaws that should be addressed/improved in order to get it accepted. Please follow these recommendations to improve your manuscript. Summarizing, your main problems, that requires major changes, are:

1. References are very scarce. You need much more relevant and RECENT studies, almost half of the studies have 15-20 years or more
2. Statistical analyses are also scarce. There are several limitations of the NHS, and only reporting p-values is not currently considered a good practice. You need to add to your current results, at least, the effect size and its 95% CI.
3. You need to improve your discussion to be better linked to your research question (i.e., the differences between running barefoot or with shoes), because you claim that several times that running barefoot could improve proprioception and prevent injuries, but the only thing that you really observed, and is not properly discussed, is the impairment of sprint performance in the barefoot condition. IMHO, this is the most important result, and the one which has more relevant practical applications for coaches.

BASIC REPORTING
1a) The use of English is appropriate and the writing style is easy to follow and understand
1b) The literature is scarce. Only 18 references are used, one of them is data of the Japanese Ministry and almost half of the references are from the 80's or 90's. Very relevant research, including very recent from Japanese colleagues who analyzed sprinting mechanics in Japanese children using a 50-m long force platform system is not reference, as well as the works by important authors on this topic such as Morin et al. Both the introduction and discussion should be significantly updated to include more recent and relevant literature.
1c) Article is well structured and the raw data is properly shared
1d) The purpose of the study is clear (i.e., to analyze the potential differences between running conditions in children), and the results are in line with the purpose of the study.

EXPERIMENTAL DESIGN
2a) The purpose is relevant and original
2b) Research question is well defined, and it is justified how it adds to the current body of literature (i.e., there are known differences between running barefoot or with shoes in adults, but not in children)
2c) The study follows all ethical standards and the investigation have been performed in a rigorous way
2d) Methods are clear enough so the study could be replicated by another group of researchers

VALIDITY OF THE FINDINGS
3a) No comment
3b) Data is fully available in a spreadsheet. However, statistical analysis are quite weak as they are only based on the NHS and no effect sizes or CI are reported
3c) The authors fail to link the main result of the manuscript (i.e., sprint performance in barefoot condition is impaired) to their conclusion, as they don't critically discuss how this might affect training strategies or how coaches should use this information. They rather discuss how running barefoot could be used to develop proprioception and prevent injuries; variables that were not measured at all in the manuscript, nor was the purpose of the investigation
3d) Claims that running barefoot could potentiate proprioception and prevent injuries are not adequate and are not linked to the purpose of this investigation, since no single variable related to injuries was tested (authors even required participants to not be/have been injured, so potential links to injury prevention in a retrospective way is not possible)


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: KINEMATIC CHARACTERISTICS OF BAREFOOT SPRINTING IN HABITUALLY SHOD CHILDREN
Review round: 2
Reviewer: 1

Output:
Basic reporting: Ok
Experimental design: Ok
Validity of the findings: Ok
Additional comments: Issues solved


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: SECAPR—A BIOINFORMATICS PIPELINE FOR THE RAPID AND USER-FRIENDLY PROCESSING OF TARGETED ENRICHED ILLUMINA SEQUENCES, FROM RAW READS TO ALIGNMENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors present a generally well written article that details a bioinformatic tool for the alignment/assembly and consensus calling of targeted sequence data.

The article is generally clear, unambiguous and well referenced.

I have some minor suggestions for improvement below:

 Title – suggest adding “targeted enriched” to the title to discriminate this pipeline from those designed to work on whole-genome data.

Line 51 –“ which are easiest to recover when specifically enriching these sequences across all samples prior to sequencing”
Suggest changing to “simple to recover”. It is easy to extract homologous sequences for phylogenies regardless of pre-sequencing enrichment.

Line 51: “archived” should be changed to “achieved”

Line 106: Is FASTQC referenced properly here?

Line 110 to 115: Is Trinity implemented as well? Would be good to include if so.

Line 135: Using SAMTools?

Line 148: “Recommendable” should be “recommended”

Line 204-205: Wouldn’t this result be due to polyploidy within the Geonoma genus? Could the authors comment on this?
Experimental design: The software tool was well designed (installation was very simple, thank-you!) and easy to use. Dependencies are handled well, which is important for a tool that relies on so much other software.

Although it doesn't affect the outcome of the study it would have been nice if the authors included more in the way of pipeline automation. Working my way through the tutorial was easy and everything was well explained but the major point of a pipeline is to automate the vast majority of steps and only require user input at critical stages. Surely not all stages of the pipeline would be critical for every data-set? Is there an easy way that someone without a good bioinformatic skill-set be able to automate the majority of the pipeline?

Some consideration with regard to using this pipeline on high performance computing infrastructure would be useful. For example running this pipeline on 1000 samples would be very difficult without writing additional resource management scripts to help submit jobs to a scheduler. Granted this is probably out of the real of most researchers but these resources are becoming increasingly common and SECAPR is designed to be largely automated and able to process large numbers of samples.

Some additional information about downstream approaches to phylogenetic analyses would help improve the paper (and online tutorial). After such a detailed and thorough guide through the workflow a novice user would be left with assembled contigs and alignment files but have difficulties with the next steps.
Validity of the findings: The data and data analysis are well presented in the article.
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: SECAPR—A BIOINFORMATICS PIPELINE FOR THE RAPID AND USER-FRIENDLY PROCESSING OF TARGETED ENRICHED ILLUMINA SEQUENCES, FROM RAW READS TO ALIGNMENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: Here the authors developed a pipeline for assembling and using targeted sequence capture in non-model organisms, which has been a clear deficit in the current  bioinformatic arena. The pipeline seems more or less sound; however, I wanted to use the pipeline on my own data to gauge success when paralogs are expected; when the distance between reference bait sequences and the recovered sequence varies; and where polyploidy is expected for some samples.

I encountered a minimum of two problems, which both delayed this review and caused me to stop testing.  The first error was in a section of the code for assemble_reads; i.e., the region in the python script which calls ABySS was commented out. This error actually took a little while to resolve since my first instinct was the the conda package was not playing well with our spack module environment. Assembly was successfully completed after removing these comment marks.

The second error may also be due to a conflict in the conda evironment versus our existing spack module enviroment; however, I cannot be certain that there are no other errors preventing the code from running without spending more time on this.

I would be happy to provide a bug report on the developer's github; however, it may be just as quick for the authors to bundle this for spack (https://spack.readthedocs.io/en/latest/index.html). I am not sure the relative prevalence of spack versus conda versus other module systems; however, porting this to spack should be relatively easy and make it more broadly accessible as spack gains in popularity.
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: DEMOGRAPHICS, PERCEPTIONS, AND SOCIOECONOMIC FACTORS AFFECTING INFLUENZA VACCINATION AMONG ADULTS IN THE UNITED STATES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Abstract: In the conclusion, I would avoid stating “improving vaccine effectiveness”. The authors are measuring a perception and these do not necessarily meet research results on vaccine effectiveness (another research on its own). I suggest only stating the already included conclusion about the need to “increase awareness about vaccine effectiveness”.
Results: Despite the clear, unambiguous, professional language used throughout, the paper, for some variables (e.g., social influence and herd immunity items), when the outcome used is “not getting the influenza vaccine” which makes sense in terms of the study question, it has led results to some tricky double-negatives in the reporting which impair the clarity of the argument.
I am not a statistician, but it strikes me a little bit odd the presentation of results of the Rao Scott results. I understand that when the authors refer to “annual vaccination being positively correlated with age”, they are referring to the fact that the proportion of individuals reporting to have an influenza vaccine shot every year is higher in the older age groups. However, I seems to me that the term could be more appropriated employed when testing the significance of bivariate correlation and not chi square test, which tests for contingency tables.
Consider rephrasing from highest value to the lowest in the following phrase: “Differences in ethnicity were also statistically significant; a higher proportion of White, non- 128 Hispanic adults (41.8%) get vaccinated every year, whereas relatively higher proportions of non- 129 Hispanic 2+ races’ adults (53.7%) and non-Hispanic Black adults (48.2%) never get vaccinated” (Lines 127-129)
Experimental design: Study objective: I suggest making the concepts clearer about the difference between barriers to vaccination, such as financial resources and perceived barriers, which correspond to a belief or attitude (e.g., fear of side effects).
Validity of the findings: No coment
Additional comments: The paper under review tried to clarify the impact of demographics, perceptions of vaccine effectiveness and socioeconomic factors on influenza vaccination status.
The paper deals with a worthwhile topic. The manuscript is well structured, has a good rationale and broadly appropriate methods. The results are important and in the line has to what has been found in other research on the topic. However, in few minor cases, the way in which the results are presented make the paper a little bit confusing to read.


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: DEMOGRAPHICS, PERCEPTIONS, AND SOCIOECONOMIC FACTORS AFFECTING INFLUENZA VACCINATION AMONG ADULTS IN THE UNITED STATES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is an interesting paper reporting the results of a national survey on factors affecting influenza vaccination.  The survey addresses many factors previously found to impact individuals’ decision to vaccinate or not, and includes some additional factors.  The figures/tables are relevant and present the results in a straightforward manner.  Relevant literature is cited.  There are multiple grammatical issues with the paper and in some cases the wording is confusing or misleading.  The text is essentially redundant with the tables.  The results are nothing more than a lengthy recitation of the data in the table.  Unfortunately this section is also written such that it presents the data in a confusion manner.

Overall, the manuscript is a good start but fails to distinguish itself from prior work, neglects to indicate if it replicates or supports prior work, does not identify which factors are likely barriers to influenza vaccination or discuss what might be done about these barriers.
Experimental design: The scope of the work is within the Aims and Scope of the journal. The research questions are well defined and would provide meaningful data that could be used to improve influenza vaccine uptake. The survey of questions asked is included in the manuscript. The statistical methodology is provided and is appropriate.  In the introduction, the authors have a paragraph outlining factors that have previously been studied in regards to influenza vaccination and so it is not clear how the research fills an identified knowledge gap or how the current study expands or builds on existing knowledge.  Another issue is that many of the factors in the survey are potentially linked and so the effect seen by “do you have to pay to get a vaccine” may be confounded with ‘income’, which might be confounded with ‘education level’.
Validity of the findings: The Discussion is mainly a review of the results with no real discussion about what the results mean and how the data could be used.  It contains essentially no discussion or conclusions, or speculation or data interpretation.  The findings are not placed in the context of existing knowledge or work.  Discrepancies or similarities to other studies are not presented.  Interesting findings are not followed-up on or discussed.  The one exception to this is the ‘Facilitators’ paragraph on line 271 where the authors attempt to dig into what drives the social effect.  Unfortunately, this is limited to a single possible explanation and the section neglects to mention other obvious drivers of the results (e.g., peer pressure)

Interesting results are not followed up on or discussed.  For example, those who are vaccinated every year seem more concerned about protecting themselves while those who are vaccinated in some years seem more interested in protecting others.  Why is this?
Additional comments: The authors should also address the following points to improve the manuscript.

The paragraph starting on line 60 mixes factors associated with increased and decreased vaccination. It is confusing to read and ends with a statement implying that the vaccine is detrimental.  The authors should organize the paragraph grouping factors positively associated with influenza vaccination and then listing those associated with decreased vaccination.

In the results section the authors bounce between associated with getting vaccinated and associated with not getting vaccinated.  A good example of this is lines 125-127.  At first glance the two percentages are very similar (47.7% vs 45.1%) but these numbers actually refer to different associations and the authors are trying to draw a distinction between the groups.  The continual jumping (between getting vaccinated and not getting vaccinated) makes the entire section hard to follow.

In the results section, remove the words ‘in comparison’.  It looks like you are comparing and contrasting age with unrelated factors.

Line 48 – insert the word ‘between’ after “Influenza has caused”.

Line 63 – awareness of what?

Line 80 – put a comma in 2,150.

Line 119 – remove the words ‘by the’ and place ‘influenza vaccine’ in parentheses.

Please define the following: metro status, region (what states are in each region), working (full-time? Part-time? Both?), internet (access at work? At home? Is access what matters or did you ask questions about usage?)

In the survey questionnaire section, the ‘health belief model’ is described but not the ‘socioecological model’.  Please explain why this second model was used.


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: DEMOGRAPHICS, PERCEPTIONS, AND SOCIOECONOMIC FACTORS AFFECTING INFLUENZA VACCINATION AMONG ADULTS IN THE UNITED STATES
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Relevant and required changes have been made to this re-submission, which now complies with the required guidelines for the journal publication.


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: DEMOGRAPHICS, PERCEPTIONS, AND SOCIOECONOMIC FACTORS AFFECTING INFLUENZA VACCINATION AMONG ADULTS IN THE UNITED STATES
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have addressed each of the reviewers concerns quite well.  Factors that are barriers and facilitators to vaccination have been grouped together for reporting and discussion.  Double-negatives and the back and forth between factors associated with vaccination and non-vaccination have been eliminated.  The revised manuscript is much easier to read.
Experimental design: As with the original manuscript, the scope of the work is within the Aims and Scope of the journal and the research questions are well defined and would provide meaningful data that could be used to improve influenza vaccine uptake.  The additional information on the analysis approach is also useful in clarifying the interpretation of the results.
Validity of the findings: In the revised manuscript, the findings are now placed in the context of existing knowledge or work.  Interesting findings are discussed.
Additional comments: The manuscript is much easier to follow and has grouped the findings into logical categories.


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: DIFFERENCES IN ELECTROMYOGRAPHIC ACTIVITY OF BICEPS BRACHII AND BRACHIORADIALIS WHILE PERFORMING THREE VARIANTS OF CURL
Review round: 1
Reviewer: 1

Output:
Basic reporting: Basic reporting is fine. I have no comments which could improve the quality of this section.
Experimental design: In my opinion the activity of the brachialis muscle, as the main and strongest flexor is very important. Furthermore, the activity of the antagonist muscles (triceps) should be recorded. This would add to the story.
Why are the EMG data not normalized?
The authors should show representative EMG data.
Surface EMG has a lot of limitations. This should be stated in the manuscript.
Validity of the findings: While the findings are robust, the significance and novelty is poor.
Additional comments: Minor comments: Replace "raw EMG" with "interference EMG".


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: DIFFERENCES IN ELECTROMYOGRAPHIC ACTIVITY OF BICEPS BRACHII AND BRACHIORADIALIS WHILE PERFORMING THREE VARIANTS OF CURL
Review round: 1
Reviewer: 2

Output:
Basic reporting: For comments on the English, please see the general comments section where this issue is addressed. In brief, there are many small grammatical errors throughout the manuscript and an English native speaker is needed to refine the manuscript. The literature references, background, and context provided seem to be adequate as is the professional article structure. The manuscript also appears to be self-contained with relevant results to the hypotheses.
Experimental design: The experimental design appears to be adequate if the main goal of the research is to provide practical information for bodybuilders or people training for general fitness. The research question and purpose are defined, fills a small gap in the literature, rather novel, and data seem to have been collected carefully. However, there are a few methodological details that are questionable and more detail needs to be provided on some of the methods.
Validity of the findings: Overall, I think the findings are valid if the main goal of the research is to provide practical information for bodybuilders or people training for general fitness. There are a few methodological issues that could be viewed as problematic (see general comments section). However, I do not think they are major enough to influence the main goal of providing information on muscle activation for practical training purposes. Finally, there are several issues regarding methodology and discussion of results that the authors need to address (see General Comments section).
Additional comments: The purpose of the present study was to determine if differences exist in the magnitude EMG activity between three variations of bicep curls (straight bar curl (BC), undulated bar curl (EZ), and alternate dumbbell curl (DC)) that are commonly used in bodybuilding and fitness training programs. Twelve healthy male participants (age: 25 ± 5 years, body mass: 77 ± 9 kg, height: 183 ± 6 cm) with at least three years resistance training experience (three lifting training sessions per week) participated in the study. The experimental design involved performance of a one repetition maximum (1-RM)  for each of the three types of bicep curls by means of a submaximal estimation method. A week later, subjects performed 1 set of 10 repetitions with 65% of maximum with each type of bicep curl in random order with 4 minutes of rest between each exercise/set. During these sets, EMG activity was measured from the biceps brachii (BB) and the brachioradialis (BR) muscles of the right arm. EMG activity was quantified for the total rep, the concentric phase, and the eccentric phase for 8 of the 10 repetitions (first and last repetition not quantified as mechanically these are different). Finally, the range of motion was quantified with a goniometer.

     The main findings were: 1) EMG activity was significantly higher for the BB and BR muscles for the EZ condition compared to the DC condition during the entire repetition; 2) For the concentric phase, BR activity was lower in the DC condition compared to the EZ and BC conditions; 3) For the eccentric phase, BB EMG activity was higher in the EZ and BC conditions compared to the DC conditions; and 4) Range of motion was greater in the BC condition compared to the DC condition.

    Overall, the manuscript seems to have been written by authors with English as a second language. The authors should have an English speaker edit the manuscript as there are small grammatical errors in many sentences. While the authors did a commendable job on the writing portion of the paper considering it is their second language and far better than I could ever do with a second language, there are numerous sentences that need to be rewritten due to the grammar. However, the authors did do a good job of not having typographical and other types of errors as I only say perhaps a few of these. In regards to the grammatical errors there are too many to point out individually but a native English speaking writer should be able to easily fix these errors as most are very minor. This topic addressed seems to be somewhat novel as to my previous studies have not investigated differences in muscle activation due to the EZ curl bar, despite the widespread use of this bar specifically for bicep curls for many decades. The focus of the research seems to be appropriate for PeerJ and of interest to many readers of the journal. At the present time, there appear to be no fatal flaws in the paper, however, I have a number of concerns, clarifications, and changes the authors should address before the manuscript can be considered for publication.

Major Points:

1. The comparison of 2 bilateral movements to a unilateral one could be viewed as problematic. The neuromuscular mechanisms underlying the control and activation of bilateral and unilateral movements can be quite different. Most importantly, the phenomenon of the bilateral deficit or bilateral facilitation (Henry and Smith 1961, Krol 1965, Ohtsuki 1984, Howard & Enoka 1991, Botton et al. 2013) was not mentioned and could potentially confound the results. Due to the bilateral deficit, one would think that the unilateral movement should have had higher EMG but this was not the case. Perhaps this could have been due to a bilateral facilitation if the subjects had mainly performed bilateral bicep exercises throughout their prior training careers. The authors definitely need to add these points to the discussion and if possible ask the subjects about their prior training history and report the results. In summary, this could be a methodological issue but it can be addressed by including it in the discussion and surveying the subjects if possible. Nonetheless, for practical training purposes the observations of the differences between the exercises are still valuable for practical applications so I do not see this problem as a fatal flaw.

2. The differences in range of motion between the DC and BC variants could be viewed as problematic also. Personally, I don’t believe that this statistically significant difference was great enough to have a major physiological effect or influence the overall results considering how the data was analyzed. Nonetheless, the authors probably should add to the discussion more information on why this one difference in range of motion likely did not have a big influence on the results.

3. The authors state that the right arm was used, but they should also report on how many of the subjects were right hand dominant. I assume most or all were. Although I really don’t think the exact number of right and left handed individuals would influence the overall results, this sort of information should be reported in papers involving the upper limbs.

4. I think the authors should have used a completely counterbalanced design instead of randomization. This likely doesn’t matter if there wasn’t a major bias due to the randomization in the order of exercises performed. However, with 6 possible order combinations due to there being 3 conditions and 12 subjects recruited, the authors could have completely counterbalanced the design. The use of a 4 minute rest interval probably mostly mitigated any fatigue effects, but it still would have been better to counterbalance.

5. More detail needs to be provided in the Methods section regarding the instructions to the subject and to how the sets of repetitions of the various curls were performed. Most importantly, what were the instructions with regard to movement intent in regards to velocity during the concentric and eccentric phases? This information is not provided. It would have been best to perform the eccentric over a set time span (i.e. 2 seconds) and the concentric as fast as possible. Since the weights were normalized to 65% of maximum for each exercise in this single joint movement, I doubt there were major velocity differences between the three movements as the subjects likely did the movements at nearly the same velocity subconsciously and due to the normalized load. However, if the authors have this velocity information perhaps they should provide it along with what the instructions were to performance. Finally, more detail should be provided on how posture or possible cheating (moving at the waist etc) was controlled for or monitored.


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: DIFFERENCES IN ELECTROMYOGRAPHIC ACTIVITY OF BICEPS BRACHII AND BRACHIORADIALIS WHILE PERFORMING THREE VARIANTS OF CURL
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have done a very good job of responding to all my previous concerns and have made the associated changes to the manuscript. One slight concern from before was the English, which has now been greatly improved. There are still a few spots where the English could be slightly improved. For instance, the part of the title that says "three variants of curl" would probably be improved if it read "three variants of bicep curls" or "three variations of the bicep curl". Overall, I think the article is ready for publication.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors have done a very good job of responding to all my previous concerns and have made the associated appropriate changes to the manuscript. One slight concern from before was the English and this has now been greatly improved. There are still a few spots where the English could be slightly improved. For instance, the part of the title that says "three variants of curl" would probably be improved if it read "three variants of bicep curls" or "three variations of the bicep curl". Overall, I think the article is ready for publication.


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: REPRODUCIBLE RESEARCH AND GISCIENCE: AN EVALUATION USING AGILE CONFERENCE PAPERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article describes an empirical evaluation of the reproducibility of research in geographic information science (GIS), based on a sample of papers that received a "best paper award" at an AGILE conference and on a survey sent to the authors of these papers. The article is well written, using a clear language and overall good illustrations. The references to the literature on reproducibility show that the authors are well aware of the state of the art of research in this field.

In the supplemental material, the authors provide raw data for their study except where this is prevented by copyright restrictions. These restrictions are particularly important in this case because the main subject of the study is a set of published articles. The authors also provide an R implementation of their computational analyses. The raw data that is supplied is understandable in the context of the article, and could be used as the basis for further studies.

I have two requests for improvement on basic reporting:

1. The authors should add a short README file to the supplemental material, containing a reference to the paper and a short summary for each file, much like the description available on the PeerJ Web site.

2. The authors should add a legend to Table 6, explaining what the color codes mean. It looks like the colors merely reflect the text in the fields, but it is difficult to be certain about this.
Experimental design: The work seems well within the scope of PeerJ Computer Science, although I think the editors are more competent to make such a judgement than a humble reviewer. Four relevant research questions are clearly identified at the start, and answered one by one in the manuscript. The authors have applied the high level of rigor one would expect in the context of reproducible research to their own work. I hope that this solid study will encourage others to apply the same methodology to other areas of science.

In spite of the very good overall quality of this study, there are two points which in my opinion deserve more attention:

1. The authors introduce "reproducibility levels" represented by the integers 0 to 3, with the understanding that a higher number indicates more or better reproducibility. These levels are assigned to different aspects of each paper by a panel of human judges. Their definition (Figure 2) seems overall reasonable, but some questions remain. Why does licensing enter into the criteria for data but not for code? Why does licensing matter for reproducibility at all? Why does a permanent ID (DOI) matter for data and results, but not for code? Why does openness enter at all, given that reuse is a concern distinct from reproducibility? The answers to these questions don't make much of a difference to the results of this study, since the observed reproducibility levels are rather low, but since the authors' criteria are likely to be reused by others in the future, improved clarity is highly desirable.

2. Starting at line 232, the reproducibility levels are elevated to a metric for use in quantitative statistical analyses (Figure 4, Tables 4 and 5). This step seems problematic and should be justified. For example, what is the interpretation of an average reproducibility level of 0.7? What would an increase of 0.3 in a reproducibility level mean in practice? In what sense is an increase from 0.7 to 0.3 "the same" as an increase from 2.7 to 3?
Validity of the findings: The conclusions provide answers to the initial research questions that are overall convincing. The analysis looks sound, the major weakness of a rather small sample size is ackowledged and discussed by the authors.

I have a single disagreement with the authors' conclusions. Starting from line 271, the authors self-evaluate the reproduciblity of their work and reach level 3 for methods and results. In case of acceptance of this paper, I would agree for the results. However, method reproducibility at level 3 would require the availability of the computational environment, e.g. in the form of a Docker image.

This is not just a theoretical concern because I have not been able to run the R code supplied with this study, meaning that I cannot reproduce its results. It uses the library "wordcloud" whose dependency "slam" cannot be automatically installed from CRAN. Manual installation using instructions found on the Web (https://stackoverflow.com/questions/39885408/dependency-slam-is-not-available-when-installing-tm-package) failed on my machine (macOS 10.12) because it seems to require the run-time library of the gfortran compiler.

I have also attempted to read the R source code in the context of the provided explanations, in order to check if it corresponds to the method description in the manuscript. Unfortunately I have failed in this step as well. My knowledge of the R language is limited and superficial. In particular, I am not familiar at all with the sometimes bizarre vocabulary of the "tidyverse" (What is a "tibble" or a "kable", for example?) This is clearly not the authors' fault. I would rather suggest to the PeerJ editors to mention expected programming language competences when inviting reviewers. I would most certainly decline any invitation to review R code.
Additional comments: I wonder if the authors have considered making their code available via Binder (see https://github.com/binder-examples/r for an RStudio-based example). The necessity to obtain a Springer API might be a problem for this kind of public execution environment, but perhaps it can be worked around.


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: REPRODUCIBLE RESEARCH AND GISCIENCE: AN EVALUATION USING AGILE CONFERENCE PAPERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The work presented takes a timely look at the state of reproducibility in the field of geographic information science. I am not from this field, but passionate enough about reproducibility in science to propose this review. This work is very commendable, and must have taken a fair amount of time and effort. I am broadly supportive of the paper, but cannot recommend publication as is. The aim of this review is thus to help improve the paper, not to criticise the general intrinsic value of the work.
Generally, I found the manuscript very difficult to follow; the structure, and the way the argument is constructed are at odds with what I would have expected.
It is good to provide research questions at the beginning, but let these questions drive and scaffold your narrative. Although your aim is clear, the confusion that arises due to the structure of the article dilutes any take-home message and likely to frighten your readership. Additionally, I can only recommend that the authors ask a native speaker to read and comment on their manuscript; at times, the authors use constructions that don’t really fit, e.g. line 59, one wouldn’t speak of “viewpoint” in this context; one would speak of “points of view” or “opinions".

* Sections 1, 2 and 3.1 seem to belong together; they are introducing the general context of the work, laying the foundations to the narrative. In particular, I don’t see Section 3.1 being part of “materials and methods”.
* Each research question should have its own section, and sections should be named appropriately, not assuming that the reader knows what you are talking about. The type of structure chosen for this paper, interweaving studies in between common sections, only work when studies are related, based on the same methods or assumptions. In this case, by virtue of the work, it adds confusion. Each study/research question could have its own set of sections (material and methods, analyses, etc).

The way this paper reads:
        1. Intro
        2. Material & Methods
            2.a Study 1
            2.b Study 2
        3. Results
            2.a Study 1
            2.b Study 2
        4. Analyses
            2.a Study 1
            2.b Study 2
        etc

The way I would think makes more sense:
        1. Intro
        2. Study 1 - RQ1
            2.a Material & methods
            2.b Analyses
            2.c Results
            2.d Conclusion
        3. Study 2 - RQ2 (or maybe combinations of RQs)
            2.a Material & methods
            2.b Analyses
            2.c Results
            2.d Conclusion
        4. Summary & Conclusion
        etc.

* Section 3.2 contains subsections that are either related to the “investigation”, e.g. Data, Methods, and “informative”, e.g. Summary, and not related to the investigation. These should be distinct.
* Taking the plunge into a whole corpus of papers is valuable, I think, but limiting the analysis to “exploratory text analysis” seems slightly wasteful. I am sure there would be ways for the authors of the papers in the corpus to reference reproducibility-related procedures, etc without using the keywords that the authors of this paper looked at. In other words, it feels that the keywords are rather limited, and not very informative. The more thorough evaluation of the papers that the authors report is, on the other hand, mightily more informative and should be given more space.
* Section 3.4 is a key part of the work, and the authors should spend more time detailing the procedure they followed to assess and rate the publications.
* Why is Table 2 presented before Table 3?


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: REPRODUCIBLE RESEARCH AND GISCIENCE: AN EVALUATION USING AGILE CONFERENCE PAPERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The revised manuscript addresses all of my concerns. I particularly appreciated the authors' efforts to make their computational environment available via Binder for easy re-use, and also provide instructions for re-building the Docker image locally. I have tested both methods and could produce the analysis PDF with either one. However, I was not able to generate the corpus-dependent results because I did not manage to get a Springer API key in a reasonable amount of time. The remaining results look visually identical to those provided by the authors. I am not aware of any tool that would let me compare two PDF files (including images) in a more precise way.


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: REPRODUCIBLE RESEARCH AND GISCIENCE: AN EVALUATION USING AGILE CONFERENCE PAPERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: n/a
Experimental design: n/a
Validity of the findings: n/a
Additional comments: I am really pleased with the revision of the article. I command the authors on the added description about the reproducibility of the article itself, and further suggestions to authors.

I have noted a couple of glitches:
* line 64, change “viewpoint” to “opinion"
* line 94, add “A Nature Editorial” or “In an editorial in the journal Nature, authors define…"


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: STOP SIGNALS DELAY SYNCHRONY MORE FOR FINGER TAPPING THAN VOCALIZATION: A DUAL MODALITY STUDY OF RHYTHMIC SYNCHRONIZATION IN THE STOP SIGNAL TASK
Review round: 1
Reviewer: 1

Output:
Basic reporting: Language could be considerably improved by checking spelling and grammar, and by making the sentence structure clearer. More linear definitions of terms and dependent variables would advance the article and increase readability.

A great deal of sensorimotor synchronization literature is missing, including shadowing tasks that use vocalisations. Moreover, the theories on multimodal integration are not discussed and, as such, results are not discussed through these theories. Theories on error correction would also be useful for interpreting results.

The stop signal task should be described in full before the method section. Discussing it in the method section means that the assumptions and meaning of this original test are ignored and the focus is on the task. This background is necessary to understand the rationale for using this task and interpreting the present results.

In many sections, APA formatting is not adhered to, often at the cost of scientific writing or information that would aid the reader in interpreting the results. Figures could be improved by including all of the results instead of the ones the authors believe are important.

Hypotheses are not supported by previous results or existing theory. Having a larger discussion about the theory will strengthen the manuscript.
Experimental design: The research question in interesting but it needs to be framed in theory and existing research. The investigation suffers some methodological and technical flaws.

The method and measurements are unclear and not well-defined. More detail is needed and the steps need to have a linear description. The task is somewhat clear but how the measures are derived from the responses (or what the measures represent) requires more description.

Presentation software has a delay when interpreting button presses and vocal responses, and these are different between the two. Details for how this was calibrated are necessary. You would likely need to adjust the timing for the two measures. Also, how were finger responses recorded? How can you be sure that the two are equivalent for measuring the NMA? What was the vocal threshold? This certainly could have affected the detection of onsets. Since the tapping task gave auditory feedback, the literature on delayed auditory feedback is relevant here. Benchmarking of these tools and systems are necessary to draw distinctions between the two response types.

The description of the procedure could be simplified by referring to the manual task as “finger tapping” and the vocal response as “vocalising”.

The rationale for using a vowel sound is unclear. A hard consonant would have made onsets easier to detect and reach threshold faster. This could be problematic for the interpretation and comparisons to the tapping task.

The tasks are currently very difficult to understand and interpret. The figures do not help in clarifying the task. Also, the stop signal delay might be affected by the period due to entrainment. How many periods (beat inter-onset intervals) were examined? Was it only 400ms? This is missing information (at least early on) and could have been included in a “stimuli” section.
Validity of the findings: The discussion focuses on the positive findings and does ignores inconclusive results. Results were not discussed through theory and previous research is not explored.

Why were the other significant results presented? Why was “go type factor” removed? The results need to be reported in full for transparency. APA also requires p values greater than .001 to be reported in full. If there are effects that are uninteresting or unwanted (e.g., phase), then a linear mixed-effects model could be used to remove these effects. As it stands, the three-way interaction with go type, block type, and response modality needs to be explored.

Analyses are not explained. Justification or rationale for each analysis is not provided and it is unclear which hypotheses are being tested and when. For example, why does it matter that the first go in phase 1 was significantly different to that of phase 2? Why was it then removed? Moreover, other differences not reported. The authors could test if one ANOVA is a better fit than the other by comparing the two models. The analysis is currently unsound and unjustified. The mean of all of the stop signals should be used. Also, there are tests for statistical equivalence that should be used when the null hypothesis is accepted (e.g., Bayes Factor).

Figure 3 needs to show all conditions next to each other. Too much is hidden with the current arrangement.
Additional comments: The manuscript reports a good idea but the technical flaws need to be overcome first. Benchmarking the setup will help to mitigate concerns regarding latencies and delayed feedback, or delayed recording of vocal onsets. Moreover, a second experiment with a hard consonant vocalisation would make the results more convincing. I think that, should these changes be implemented, the paper could make a good contribution. The authors may also want to reconsider using Presentation as there are several latency issues for recording responses and producing auditory feedback using this software.

Specific comments

 “Sensory motor synchronization” is usually called “sensorimotor synchronization”. In the present paper it is spelled both ways. Perhaps only use the latter.
Terms need to be defined “reafferent” and the notions of efference copies should be introduced and defined.
“I.e.” and “e.g.” should be followed by a comma throughout

Page numbers would be useful

Abstract
What is meant by “constraining the beat”?
Single and dual channel conditions need to be better defined. What does “manual” mean here?
Stop signals also need to be defined.
“Perturbed” NMA should be “reduced” NMA. Perturbed could mean increase or decrease depending on how it is viewed.

Check English and spelling, e.g., “… participant’s tap…” (line 56)

Missing definitions for some terms (e.g., “beat”)

Incorrect use of “which” (e.g., line 62). Replaced with “that” where necessary.

Line 64 “has to do with” sounds clumsy. Why not “is”?

Line 65. Should be “how regular taps are relative to the pacing stimulus”.

Line 74-75: Should be “differences… give rise”

Missing reference for “humans seem to perceive synchrony between the tap and the sound” (67-68). This would be an interesting paper. Same for “i.e. tapping to an auditory metronome is perceived to be 'in time', and not ahead of the beat.” (Lines 76-77) The perception of “in time” is not known, only the behaviour.

Lines 83-84: “cross sensory integration” should be “cross modal integration” to keep in line with the literature.

“Studies by Müller et al. (2008)” – only one reference, so should be singular, or should be more than one reference.

Lines 97-98: “Therefore, no central sensory multi-modal integration is required; hence, the possibility of delays being introduced by the integration process are minimised.”
Multimodal integration is required – proprioception, audition, and even touch (depending on the vocalisation type) are integrated. Unless you anaesthetise the mouth, you will still have multimodal integration.

Line 110: “cross modality interactions” should be “cross modal interactions”.

Line 111: “SR” used before it is defined.

Lines 112-114: “In the single channel SMS case, any shift away from the perception of synchrony is likely to be more apparent, and therefore more strongly resisted”
What is this based on? Why is it the “perception” of synchrony? This was not measured.

The stop signal task needs to be defined.

Line 130: +/- refers to a range, not the standard deviation.

Lines 132-133: Why was this range used? The rationale is not provided.

Line 137: Ethics number?

The “stop signal” is defined too late. The original stop signal task should be described in the introduction, including the rationale for why it is used and what it originally measured. The present method could then be reported more linearly.

By line 186 there are too many acronyms used and the acronyms are too similar. Perhaps shorten “Stop-signal” to “SS” then use the whole word following SS.

The purpose of the irrelevant stop blocks is unclear. Do they serve as a baseline?

Lines 203-204: “…measured as the increment in RT in the presence of intermittent stop signals”
Which increment? Is there a word missing? Do you mean the asynchrony for stopping/not stopping at approximately chance level?

Line 204: “In analogy with…” should be “analogous to”

Lines 208-211: “as the difference of synchronisation response from the mean of the relevant stop block against the mean of the irrelevant stop block”
The precise dependent variables should be defined. This could also be shown in the figure. “The amount of slowing” is difficult to link to a precise value or measure.

Lines 211-212: “synchronisation response data is statistically equivalent” – should be “was”. Check tense throughout (lines 214-215). Also, there are tests for statistical equivalence that should be used here.

Line 213: Incorrect use of semicolons (and this occurred earlier too). Check grammar and avoid usage if correct usage is unclear.

Lines 202 and 219: Proactive and reactive inhibition are not defined except by how they are measured. What do they represent?

Lines 231-236: The measure here is unclear. Why was the number chosen this way? What is the rationale and  advantage of this method?

Line 239: APA requires numbers less than 10 to be written out. Use of hyphens unnecessary here.

Lines 243-250: This sounds like conditions that were counterbalanced. Order effects should be examined to account for learning and/or fatigue.

Line 252: Figure 1 does not show the instruction screen

Figure text is generally too small. Also, APA format is not used (e.g., Figure in italics, period after figure number)

Lines 287-289: Why were these SR values chosen? What was the rationale? What is the a priori reason that the first and second go trials are different from the others?

What was important about phase 1 and 2 that required them to be analysed? Why wasn’t order include as well (i.e., the pseudo-randomisation)?

Why were the other significant results presented? Why was “go type factor” removed? The results need to be reported in full for transparency. APA also requires p values greater than .001 to be reported in full. If there are effects that are uninteresting or unwanted (e.g., phase), then a linear mixed-effects model could be used to remove these effects. As it stands, the three-way interaction with go type, block type, and response modality needs to be explored.

Analyses are not explained. Why are the analyses being performed? Which hypotheses are being tested? For example, why does it matter that the first go in phase 1 was significantly different to that of phase 2? Why was it then removed? Why are the other differences not reported? Why not test if one ANOVA is a better fit than the other by comparing the two models? The analysis is currently unsound and unjustified. The mean of all of the stop signals should be used.

Figure 3 needs to show all conditions next to each other. Too much is hidden with the current arrangement.

Lines 334-340: A 2x2 ANOVA of relevant/irrelevant and modality (manual/vocal) is necessary. Was there a significant difference between relevant and irrelevant conditions, or an interaction? This is on lines 345-347 but they reveal no interaction, so the analysis was not warranted.

Line 358: “…that the SSRTs were not statistically different” – should be “were not significantly different”.

Results are not interpreted in the discussion in light of the evidence and existing theory.

Lines 369-370: “In order that the central matching of these two sources of information occurs with overlap in the brain” – this is a vague statement. Where and how do you propose this happens? Missing reference.

Lines 375-376: “that the sensory integration that occurs between senses” – redundant “that occurs between senses”.

376-377: Unclear what is meant by “a broader range of tap timings”?

377: “assymetrical” – spelling

379-380: “However, the lack of any discernible difference in the measures of variance for tap vs. vocalisation times doesn’t support this” – scientific writing does not contain contractions.

405-406: “Furthermore, there is a significant overlap in the neural substrates that support inhibitory control and the production of rhythmic tapping tasks.” – Missing references. Which neural substrates and which tasks?

407: “show that top down influences onto motor cortex” – “from” the motor cortex?


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: STOP SIGNALS DELAY SYNCHRONY MORE FOR FINGER TAPPING THAN VOCALIZATION: A DUAL MODALITY STUDY OF RHYTHMIC SYNCHRONIZATION IN THE STOP SIGNAL TASK
Review round: 1
Reviewer: 2

Output:
Basic reporting: -The use of the term “channel” early on was somewhat confusing. My understanding from reading the full paper is that this refers to some aspect of a sensory modality, but it would help to include a clearer definition up front (i.e., in the initial Background section).

-There is mention of alternative theories to that of afferent conduction time in accounting for NMA/differences in NMA depending on the effector synchronizing with a stimulus. It would be nice to see a short overview of what these alternatives include.

-It would be nice to see some references for the point made in lines 112-115, about how single channel SMS is more robust than alternatives, or at least a qualification of this statement considering other factors. Findings demonstrating superior synchronization to auditory stimuli as compared to visual stimuli during SMS (across contexts in which visual feedback about finger taps is available) could be seen as counter to this idea. (e.g., Iversen, J. R., Patel, A. D., Nicodemus, B., & Emmorey, K. (2015). Synchronization to auditory and visual rhythms in hearing and deaf individuals. Cognition, 134, 232-244.)

Ease of readability:
-Typo on line 56: “participants”

-Having fewer acronyms defined within the paper (not including those commonly used across work in this field), can become challenging. Unless there are constraints on space I might prefer to have fewer acronyms.

-It seems as though number the figure sections in order based on how the content is addressed in the paper would make for smoother reading as well.

-In the caption for Figure 1, A there is redundant language in the second to last sentence.

-Line 351 includes an incomplete sentence, “A finding that meets the horse race model assumption.”

-Line 354 should include “on average”.

-Something weird happens with the parentheses used in lines 408-410.
Experimental design: -The authors claim that by employing a vocal synchronization task the “dominant feedback modality” is of the same sensory channel as the stimulus and that they are “eliminating transduction and conduction discrepancies”. Based on the current explanations provided I am not convinced that it was necessary to adopt this new task in order to achieve a feedback modality consistent with the stimulus. In other words, wouldn’t adding an auditory feedback signal associated with button presses also accomplish this? There are other factors worth considering here as well such as the fact that participants have visual information about their button press movements, but not their vocalizations. The interesting question here seems to be about the effect of congruency between the sensory modality associated with the stimulus and the outcome of synchronizing behavior. If this is the case, it seems as though some alternative designs may have provided for better control. Additionally, if auditory feedback was produced in both the manual and vocal response conditions and the same pattern of differences in NMA were observed this might support an alternative explanation of the observation of differences in NMA for different sensory-motor synchronization tasks, for example one based on the time required to execute the required motor response or the kind of timing process supporting SMS (see e.g., Studenka, B. E., Zelaznik, H. N., & Balasubramaniam, R. (2012). The distinction between tapping and circle drawing with and without tactile feedback: an examination of the sources of timing variance. The Quarterly Journal of Experimental Psychology, 65(6), 1086-1100. for discussion of some of these ideas.) (Iversen, J. R., & Balasubramaniam, R. (2016). Synchronization and temporal processing. Current Opinion in Behavioral Sciences, 8, 175-180. also provides discussion of the idea that timing processes during SMS reflect perceptual goals.)

-As clarification in the Apparatus section, what was the monitor being used for? (Last sentence.) Also, did the button press make sound at all?

-It would be helpful to have a rationale or some other examples from SMS studies relating to the selection of a stimulus onset asynchrony interval of 1250 ms. This seems to be on the longer side, as previous work has determined that beats are most strongly felt when the interval is ~700 ms, and above 1800 ms synchronization is no longer possible (see e.g., London, J. (2002). Cognitive constraints on metric systems: Some observations and hypotheses. Music Perception: An Interdisciplinary Journal, 19(4), 529-550.)

-The description of participant instructions would benefit from being more explicit, specifically with regard to what they were told about the relevant stop blocks.

-In the section on Estimating proactive inhibition, I think I understand correctly that only “go” trials are being analyzed. This could also be more explicit for ease of understanding. The later discussion of how stop blocks may be influencing behavioral control is good, but having this be clear when the idea of proactive inhibition is first introduced would be helpful.

-Similarly, in the section Effect of stop signals on the synchronization response it would be helpful to state that this measure uses just trials in which participants didn’t successfully stop.
Validity of the findings: -It seems important to address the fact that vocal responses are occurring after the pacing signal, on average. This is true in the irrelevant stop condition and then in the stop condition they come even later. It’s possible that this means the threshold participants are using as the onset of vocalization is just much lower than the experimental threshold being employed, but if that’s the likely explanation it should be included in the Discussion. As is, it does not follow that vocalization timing is based on achieving simultaneous arrival of self-feedback and the pacing signal. This is also an important consideration with respect to discussion of why there is more reduction in the manual response NMA than the vocal response NMA. Given that vocal responses are already occurring after the pacing signal in the irrelevant stop condition, it’s possible that they can not come the same amount later as seen for manual responses in the relevant stop condition without interfering with the processes involved in the subsequent synchronization response (i.e., is there a possibility of a ~ceiling effect for reduction of NMA).

-The implication of the lack of difference in SSRTs between the modalities is not obvious to me. It would be worth including a mention of this in the Discussion as well.
Additional comments: Overall this study appears to be well-executed, particularly in terms of the analyses selected and conducted. The majority of my comments relate to areas where additional explanation or clarifying language would be helpful for reader understanding. However, I do have some reservations about how the experimental design addresses the questions of interest as they are currently articulated. I think the study is interesting and significant as conducted, but that it would be even stronger with additional explanation addressing the questions I've included with respect to experimental design (also possibly including the conceptual rationale provided in the Introduction).


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

Input:
Title: STOP SIGNALS DELAY SYNCHRONY MORE FOR FINGER TAPPING THAN VOCALIZATION: A DUAL MODALITY STUDY OF RHYTHMIC SYNCHRONIZATION IN THE STOP SIGNAL TASK
Review round: 1
Reviewer: 3

Output:
Basic reporting: The study adresses the mechanisms underlying the phenomenon of negative mean asynchrony in (rhythmic) synchronization to a sound. To this end two tasks are studied and compared, tapping and vocal response (basically saying "i"). The hypothesis relates to the so called Paillard- Fraisse hypothesis, that the asycnrhony is caused by the phase shifting required to re-synchronize sound input and proprioceptive afferences. It is argued that in vocal response there is not such bi-modal integration mechanism, being a single sensory "channel": auditory. A stop paradigm, developed for the study of inhibition, is used to adress the robustness of the NMA (Logan et al.). The rationale is as follow: a single channel will be robust, a dual channel will be less robust to the "stop processing". In this case of rhythmic synchronization, the stop paradigm is adapted, basically a stop signal (cross turning to red) instructs the subject to stop synchronizing in the middle of a sequence. Irrelevant (don't stop) and relevant (stop) Stop signals are used.

I have two major comments: 1) the way the study is introduced focus on the NMA and the sensory uni vs bi modality distinction, while the Stop task is then presented as relevant to attentional and inhibitory processes. The prediction of a modulation of the NMA in each task is not presented initially as an attentional effect, the hypothesis tested being that the integration of two delays is the cause of NMA. Somewhat the MS changes topics on the way. 2) The assumption that vocal response is a single channel, auditory, is far stretched. The role of proprioceptive sensory mechanisms are known to be important in vocal function. Moreover as far as tapping is concerned, if a sound, a "clic", is added to the response, and the task is to sync the clic with the external stimuli, then vocal and tapping responses seem very similar. such tapping tasks have been studied in the NMA context. I would add also that there are data on the mean asynchrony for tapping in sync with a tactile stimuli, tapping in the aire without physical contact, and tapping at different rate which affects NMA.
The prediction of a more "tolerant" (from the authors) single channel process (vocal response) causing a greater resistance to the inhibitory stop mechanisms should be clearly delineated, compared to the assumed dual-channel tapping processes.
For an illustration, the role of the validity of the horse race model ine the Results section is not introduced earlier.

This said, it doesn't mean I don't appreciate the interest of the paradigm and data, but the MS should be thought differently to my opinion to make it informative and logic.

Finally, I would regreat that 30 years of research on synchronization to sound of tactile stimuli are completely ignored (Kelso et al., 1990). This has consequences in terms of theory first, but also in terms of observables founded on the theory. Of course the concepts are distincts, but there are also some basic emprirical results and methods that could be useful even if one doesn't adopt a self- organized, dynamical, account of cognitive and sensorimotor functions. In particular the stability of synchronization is a very robust observable (estimated by the variance (or std) of synchronization "errors").
Experimental design: Below some minor comments.

1) which device was used to record the vocal responses ? I guess the sound card.
2) the stop paradigm is described in great detail but could be introduced in a first simple and more transparent way, the reading is tenious to understand what the subjects were doing.
3) 161 : typo "go trials"
4) 211-221 : "The synchronization...equivalent to.." : I don't understand. It is the same variable or not? What means "statistically equivalent"?
5) 215-216: What means "we are presenting a synchronization response..."?
6) in Figure 3, one variable is "Proactive inhibition", this does not appear in the methods of the 1.3.3. stop signal sync task.
7) in the Results: 335 a typo: relevant
Validity of the findings: The data are sound, as the experimental paradigm. the discussion of "the idea that inhibitory control and rhythmic timing are linked" is interesting. The proof from the comparison of the two tasks is left to the reader, as no formal framework, non ambiguous and scientifically coherent to compare tasks does not exist to the best of my knowledge. Here is put forward the idea that one task is more single channel than the other, among other things.

But the logic of the MS, as stated above, is ackward.
Additional comments: I have nothing to add to my comments 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: STOP SIGNALS DELAY SYNCHRONY MORE FOR FINGER TAPPING THAN VOCALIZATION: A DUAL MODALITY STUDY OF RHYTHMIC SYNCHRONIZATION IN THE STOP SIGNAL TASK
Review round: 2
Reviewer: 1

Output:
Basic reporting: Improved but Figures need to be formatted appropriately and null results should not be discussed.
Experimental design: The main methodological flaw (i.e., differences between veridical and  measured responses were not obtained) is still problematic. See comments for a full description.
Validity of the findings: Difficult to assess until the correct calibration occurs. The null result is still interpreted as a "finding" and several interactions are not examined or controlled for using the correct statistical procedure (e.g., if "phase" is not important, then use a linear mixed-effect model to ensure it does not moderate the effects).
Additional comments: General comments
The authors have improved the manuscript considerably and several aspects are much clearer. However, the methodological concerns regarding differences between the data collection method of the voice controller and button response remain. I understand that the authors have attempted to address this issue so I describe what is necessary in full here. When a program (e.g., Presentation) records the timing of a stimulus, there is often some delay (I believe approximately 4ms after the time it reports for presentation). However, when presentation has to make auditory feedback relative to a response (e.g., keypress), this delay is much larger (I have measured approximately 40ms +/-5ms); some of this time is the error of recording the veridical response and the rest is error in producing the auditory feedback. To calibrate the system correctly, one needs to measure the veridical onset of the response (finger tap or vocalisation) relative to the stimulus. Currently, what is shown is the detected vocalisation onset relative to the start of audio recording by Presentation but this does not necessarily reflect when the stimulus occurred and this only lets one know what Presentation recorded as opposed to what actually occurred. One method for obtaining the veridical timing of the finger taps and vocalisations relative to the stimulus is to use any oscilloscope (or analog input box or audio sound card) that records the signals for all devices simultaneously using different channels (see Schultz & van Vugt, 2015 for a simple example). By the “signals” I mean both the inputs and the outputs; if there would be auditory feedback (although, in this case there is not), then one would need to record the veridical timing of the keypress through some kind of sensor (e.g., force sensitive resistor) and the auditory output (I mention this just in case the authors reasoned that using auditory feedback of keypresses is a viable measure of veridical onsets; they are not). What is missing for the present experiment is a calibration that measures the continuous signals of the stimulus, keypresses (through a sensor), and speech audio to obtain the veridical latencies of responses and to compare these to those recorded by Presentation to see if any correction needs to be applied. If the latencies are constant within a given range (e.g., any value with a range less than +/- 0.5ms), then you might be able to subtract these baseline values from each condition. If they are more variable, then the experiment might need to be replicated with the veridical latencies recorded in the manner described above. As it stands, the system has not been adequately calibrated to make any claims regarding differences between finger taps and vocalisations. Once this issue has been resolved, then the main claims would be justified. Until then, no claims can be made regarding negative mean asynchrony (i.e., hypothesis 1), although the claim regarding the change within response conditions (finger, vocalising) still stands (i.e., hypothesis 2) as each condition is relative to a baseline (i.e., tap irrelevant minus tap relevant, vocalisation irrelevant minus vocalisation relevant).

There are also references on delayed feedback and modality (e.g., Sugano et al., 2012, and others on tactile feedback) that are missing and should be included.

Last, differentiations between “in the brain” and “in the world” should be termed “perceptual” and “veridical” (or similar). “In the brain” would require EEG or fMRI.

Minor points
Title
Don’t use double negatives, suggest change to
“Stop signals increase synchrony more for finger tapping than synchronized vocalization: a dual modality study of rhythmic synchronization in the stop signal task”

Also, “synchronized vocalization” assumes it is “synchronized”. Suggest removing “synchronized”.

Abstract
“Paillard-Frassie hypothesis” should be “Paillard-Fraisse”

Vocalisations are still referred to as “single modality”. There is tactile feedback there too. What about bone conductance? Also, keypresses tend to produce auditory “clicks” that technically *could* be auditory feedback. These limitations won’t stop the paper from being published but should be acknowledged.
“Less asynchronous” would require the absolute value to be tested (i.e., the magnitude of asynchrony).

Bayes factor tests are necessary if you want to interpret the null result between finger tapping in the synchronization and stop-signal task. It is likely to give evidence for the null hypothesis given the means but the test should be performed.

Line 82
“e.g.” occurs without a comma. This was mentioned in the previous review and authors claimed to have fixed it. This also occurs for “i.e.” (e.g., line 113).

Lines 130-131
Specify that the t-tests showed “no [significant] differences”

Lines 143-146
This description is confusing as it makes it sound like there is auditory feedback for the tapping condition. Perhaps first state that the pacing signal involves the auditory modality, finger tapping adds the tactile modality, and vocalising adds the tactile and a second auditory modality.

Line 165
“On go trials” should be “”In go trials”

Line 177
“E.g.” should be inside parentheses

Line 202
No capital should occur after the semicolon.

Lines 209-212
Hypothesis should be statements (e.g., x is y), not possible future suggestions (e.g., x would be y).

Line 205 (and elsewhere)
Remove the “registered” logo after Presentation. I believe this is not necessary.

Lines 250-254
What was the hardware of the PC? Some PCs cannot produce 120 frames per second and the “syncmaster” does not work unless you have a compatible graphics processor unit.

Lines 288-291
I know it’s picky but with 120Hz, your visual timing resolution is 8.3ms. This means that, technically, your increments would only be approximately 30ms (to the nearest multiple of 8.3ms).

296-297
“Inter-tap interval” should be “inter-onset interval”. The former is the measure whereas the latter is a property of the stimulus.

324-326
The description and term used for “synchronized response” are still unclear. Why not “response time difference”? Also, shouldn’t this measure the difference between asynchronies instead? Why is the response time difference for continuous responses important? Why not call them “asynchrony with pacing signal” and “asynchrony between tasks/relevance”? I still don’t know why the latter is important, but it would make the terminology clearer.
How were missed responses dealt with? Wouldn’t this increase latency if a cycle was missed?

351
Separate Appendices should be used for each section and should be labelled as they appear in the manuscript. Also, the figures and tables in the appendices should use a difference nomenclature than those in the manuscript (e.g., Figure A1)

372
“…in time to…” should be “…in time with…”
Line 386 (and throughout)
Figures need to use APA formatting and should not have borders. “Figure n.” should be italicised and the caption should continue on the same line.

406-414
Why only these two? What about the other events? Wouldn’t that make a better baseline? From the table on lines 446-447 it appears that there is an interesting difference between “all other go” where finger tapping has an advantage.

413-414
“We were interested on…” should be “We were interested in…”

416-420 (and throughout results)
If p is less than .001 then one can report “p < .001”. Currently it says “p = .001”. Is this the case or was it less than .001?

430
Should it say (ps > .41)? Was it one p or multiple? If one, then report one p value (p = .41). If multiple, then say what value the ps were greater than.

440-441
If all other pairwise comparisons were significant then there was a significant difference between the relevant and irrelevant stimuli for the vocalisation condition: 5.92ms vs. 5.96ms. I don’t think this is the case, and the results need to be reported more precisely.

468-473
“…occurred significantly closer to the auditory pacing signal compared to the asynchronies…”
To say this (and the later statements), the absolute asynchronies need to be used. This becomes more confusing in lines 473 to 478 where the magnitude of the vocalisation (32.06ms) is reported as “similarly” closer to the pacing signal than the finger tapping (5.59ms).

489-490
“did not differ from the onset of the pacing signal” – See previous comments regarding “significant differences”.

Figure 3 is still not transparent. All of the factors and associated levels should be shown (see previous comments).

532
“Paillard-Frassie” – Misspelled “Fraisse” and missing “hypothesis”. The plural “hypotheses” at the end is awkward since these are the names of the hypotheses (e.g., “the Paillard-Fraisse hypothesis” is the name).

594-595
“made finger tapping very accurate” – should be “made finger tapping more synchronous”.

599-603
Where are the references for these studies? The reference you discuss is a review paper but I could not find the “hold back” quotation used here.

597-599
“did not find differences” – should be “did not yield a significant difference”. Check throughout the article for these mistakes.

632-633
“An incidental finding worth highlighting in this study is that SSRTs were not different across the vocalizations and finger tapping.”
A null result is not a finding and definitely not one worth highlighting. A null result is likely due to variability/noise in the experimental setup, or it indicates that you need more participants to find an effect. Bayes factor tests are used to measure whether one can accept the null hypothesis and the strength of the evidence. As this test was not used, the conclusions that are in the paragraph (632-647) are void.

828
The significant (and near-significant) interactions with phase require exploration. What do these interactions mean? Table 3 does not help to clarify the issue and requires the descriptive statistics of all factors used in the ANOVA.

References
Sugano, Y., Keetels, M., & Vroomen, J. (2012). The build-up and transfer of sensorimotor temporal recalibration measured via a synchronization task. Frontiers in psychology, 3.


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: STOP SIGNALS DELAY SYNCHRONY MORE FOR FINGER TAPPING THAN VOCALIZATION: A DUAL MODALITY STUDY OF RHYTHMIC SYNCHRONIZATION IN THE STOP SIGNAL TASK
Review round: 2
Reviewer: 2

Output:
Basic reporting: I initially commented “There is mention of alternative theories to that of afferent conduction time in accounting for NMA/differences in NMA depending on the effector synchronizing with a stimulus. It would be nice to see a short overview of what these alternatives include.” The authors responded with inclusion of additional theory relative to inhibitory control and SMS, but I feel the authors still need to explicitly acknowledge the many other alternative theories put forth to account for NMA as are outlined in Repp (2005) and Repp and Su (2013) (even if the mechanism is truly multi-factorial, as the authors suggest). This overview would be fitting within the discussion raised starting in line 91, before thorough discussion the Paillard-Fraisse hypothesis and its relation to the current study.

I suggested the inclusion of some additional references, which the authors do not see as particularly relevant to the scope of the current project. I maintain that the area of research that employs to the metric of performance variability for SMS (and that including studies that use other tasks for investigating sensorimotor performance) is important to the larger considerations of perception, timing and sensorimotor integration being addressed by the current project. As such I think some inclusion of key findings from these studies would help in situating the current study as relevant within this broader field.

Line 203 should contain “inter-modal”.
Experimental design: I initially commented ”The authors claim that by employing a vocal synchronization task the “dominant feedback modality” is of the same sensory channel as the stimulus and that they are “eliminating transduction and conduction discrepancies”. Based on the current explanations provided I am not convinced that it was necessary to adopt this new task in order to achieve a feedback modality consistent with the stimulus. In other words, wouldn’t adding an auditory feedback signal associated with button presses also accomplish this?” The authors have cited a study that does this, but do not include a description of the task in the paper and do not discuss the related findings. These seem critically important to understanding the background contributing to the current study.

I initially asked “Did the button press make sound at all?”. The authors responded with clarifying details that I think should also be included in the text of the paper, including the fact that participants were “encouraged to relax as much as they could and respond with ease, so this would not make a loud noise.” Furthermore, this leads to the question of what headphones were used, and were they noise-cancelling? These are all important details. In future uses of this paradigm it might also be good to survey participants afterward about whether they could hear their taps in order to be able to provide at least anecdotal information on this.

Relatedly, can the authors provide a rationale for selecting the vowel sound they did for vocal responses?
Validity of the findings: I initially commented “It’s possible that the threshold participants are using as the onset of vocalization is just much lower than the experimental threshold being employed, but if that’s the likely explanation it should be included in the Discussion.” This possibility is still not considered in the text, which seems problematic largely because a) the pre-set threshold for response detection is not specified in the manuscript (I think this should be included for replication purposes), b) there is no empirical or theoretical support provided for the selection of this threshold. This is the key remaining issue I see with the current manuscript as, based on my understanding, if the threshold was lower and caught vocalization onsets earlier, the difference in asynchrony magnitudes between synchronized vocalization and finger tapping may not actually be significantly different. If it were possible to reasonably demonstrate that the threshold selected corresponds to the point at which individuals perceive their vocal responses as coinciding with a periodic stimulus the findings would be much stronger.

The statement “asynchronies were reduced in the relevant stop blocks compared to the irrelevant stop blocks for the synchronized vocalization” (lines 575-576) is not consistent with the results as it is currently worded. While it may be accurate to say that negative synchronies were reduced, the synchronized vocalization asynchronies were not negative to begin with and actually became larger/appear to exhibit a shift to reduced accuracy in the context of the relevant stop blocks. This wording needs to be clarified throughout in order to avoid misstating the results, and there should be some discussion of why the stop signals appear to be making synchronized vocalizations less accurate (at least based on the chosen threshold for vocalization onset).
Additional comments: The resubmitted manuscript is much improved in all areas following revisions based on the initial review. It is now generally more coherent from start to finish and provides a much stronger rationale for the way in which the study was conducted, as well as a better background for appreciating the outcomes.


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: STOP SIGNALS DELAY SYNCHRONY MORE FOR FINGER TAPPING THAN VOCALIZATION: A DUAL MODALITY STUDY OF RHYTHMIC SYNCHRONIZATION IN THE STOP SIGNAL TASK
Review round: 2
Reviewer: 3

Output:
Basic reporting: The MS has been considerably revised and is aceptable for publication to my opinion in its current state.

I noted a typo in the abstract :
Typo ligne 38 The Paillard-Frassie hypothesis : Paillard Fraisse
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The MS has been considerably revised and is aceptable for publication to my opinion in its current state.

I noted a typo in the abstract :
Typo ligne 38 The Paillard-Frassie hypothesis : Paillard Fraisse