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: MEASURING CLIENTS’ EXPERIENCES WITH ANTENATAL CARE BEFORE OR AFTER CHILDBIRTH: IT MATTERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: > Clear, unambiguous, professional English language used throughout.
The standard of English is generally good and with the exception of some minor editing will be appropriate for publication.
> Intro & background to show context.
The context and background to the key research question are well described and the need for this study justified. Please state in which countries the ReproQ is the national survey of childbirth care (Line 78).
> Literature well referenced & relevant.
Appropriate literature has been referenced.
> Structure conforms to PeerJ standards, discipline norm, or improved for clarity.
The article follows a Methods/Results/Discussion structure, including limitations and conclusions, which is appropriate for this type of report.
> Figures are relevant, high quality, well labelled & described.
The Figures are basic but generally clear.
> Raw data supplied (see PeerJ policy).
A labelled SPSS data set is provided.
Experimental design: > Original primary research within Scope of the journal.
The research topic is relevant to health service quality improvement, and can therefore be considered an aspect of health science, so although based in social science methodology it is my view that it is within the journal’s scope.
> Research question well defined, relevant & meaningful. It is stated how the research fills an identified knowledge gap.
The research addresses a clear issue in the measurement of maternal care experience, and this is important because it affects the interpretation of results from surveys of antenatal care and the future development of measurement in this area. These in turn impact on the delivery of high quality healthcare. The research question is clearly stated and defined.
> Rigorous investigation performed to a high technical & ethical standard.
The question has been carefully investigated using appropriate statistical methods, and on the whole the results are clearly reported. However, where statistical significance tests are reported (Table 4), this is done using asterisks to indicated p<0.05, whereas actual p-values should be reported. This is not only good statistical practice (see American Psychological Association style), it is also a requirement of this journal.
> Methods described with sufficient detail & information to replicate.
The methods are generally well-described and SPSS analysis syntax is provided which makes clear how analyses were conducted and will aid in replication. The ‘median’ scoring approach is a little hard to follow in the text, and could usefully be clarified by stating in the initial description that the median referred to (Line 132) is the median of all cases in the data – or if not, then to specify which reference is used. The decision to exclude women who filled out the questionnaires in paper form (Line 164) is puzzling and would benefit from some explanation.
Validity of the findings: > Negative/inconclusive results accepted.
The commentary covers positive and negative results without prejudice.
> Meaningful replication encouraged where rationale & benefit to literature is clearly stated.
There is no invitation to undertake replication of the results.
> Data is robust, statistically sound, & controlled.
The ‘funnel’ down from 3,313 women invited to take part to 462 actually participating is considerable, and presents a risk of bias. This in itself is not mentioned as a limitation of the study, although there is some comment on differences between the sample characteristics and the women originally eligible. It would be advisable to include a note about these numbers, and if possible also to provide some reassurance that other characteristics were broadly comparable.
> Speculation is welcome, but should be identified as such.
The discussion includes informed speculation, and this is clearly indicated by the wording.
> Conclusions are well stated, linked to original research question & limited to supporting results.
The conclusions are generally sound and reflect the results obtained. However, that ‘agreement between the antenatal experiences measured before and after childbirth is overall poor to moderate’ (Line 388) applies to summary scores, not necessarily to the domain scores or items (notably in relation to negative scores, when the agreement is often ‘excellent’). This should be clarified.
Additional comments: This study addresses an important aspect of the validity of survey results for antenatal care and demonstrates the impact of delaying evaluation until after delivery, as well as indicating some of the factors that may affect delayed evaluation. It has been well-conducted and the results show these findings clearly. As well as being immediately relevant to maternity care, the findings should also encourage reflection more generally on how events between a care episode and a service-user survey can impact on the ratings obtained.


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: MEASURING CLIENTS’ EXPERIENCES WITH ANTENATAL CARE BEFORE OR AFTER CHILDBIRTH: IT MATTERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors need to check that they are using the correct term in the following places:
Line 279: “Secondly, we did not administer whether the clients’ situation changed during the interval between test and retrospective test other than the events, experiences and perceptions during childbirth and postnatal care. It is possible that omitted variables could further modify the gap between test and retrospective test.”
Perhaps the word administer should be replaced with “test”.
Minor editing issues need to be addressed as shown below:
Line 66 – clarify: “events that happened since, particularly regarding the antenatal care experiences.” Since the antenatal experiences.
Line 210 – “The following sets of determinants were included (forced entry)” – meaning of “forced entry”?
Table 2 key – “(never in an domain and/or ‘sometimes’ in the individually chosen two most important domains).” ‘Never’ should also have apostrophes.
Table 2 -  the “vs” –is slightly distracting and not necessary I think. Perhaps a single vertical line between the 3 types of scores could be applied instead.
Table 4- the header seems to be very long and incomplete – authors to check.

Reporting of statistics
As required by the journal, authors should report the exact p-values and not ranges.
Experimental design: To help the reader to understand the three different scoring models, given their centrality to the analysis, it may be useful to insert a small table on this could be helpful, showing the definition and descriptive statistics.
Validity of the findings: Through multiple revisions in preparation for submission of the manuscript, as inevitably happens, some discrepancies may have crept in.

In the abstract, the authors highlight two broad factors accounting for the gap between the gold standard and the retrospective assessment as follows:
“Adverse experiences during childbirth and postnatal care and lack of professional continuity during childbirth negatively influenced postnatal measurement of antenatal experiences.”

However, in searching for the phrase “adverse experiences in childbirth”, this phrase does not occur in the results, nor in the discussion. It would make it easier for the reader if there was a one-to-one alignment.
Currently the results read: “Additionally, gap between antenatal and postnatal measurement is (partly) associated with clients’ experiences during childbirth and postnatal care and by professional discontinuity during childbirth”.
In the discussion, the same observation reads: “Surprisingly, the perceived health outcome of mother and child had no impact on the antenatal experiences measured after childbirth.”  - this latter description seems to contradict the statement in the abstract. Yes the effect of professional continuity is accounted for: “One exception to this is professional continuity during childbirth that was of significant impact on the antenatal experiences measured after childbirth.
In the conclusion, the related observation reads: “Measurement of antenatal
experiences postnatally is probably subject to postnatal effects.”
When reviewing Table 4 one observes that the overall rating of the experience of birth is significant in explaining the antenatal total experience score as measured after birth (dependent variable: 1.05 - 2.87 *).  However, the “health outcomes” related to birth do not seem to hold explanatory power according to the regression analyses. The authors may wish to consider aligning all these statements more clearly.

Another issue is to improve the clariy of the findings in the first paragraph of the discussion. In the opening part of the discussion, state clearly what the final pattern is before indicating, as done in Line 286/7 – that “patterns were quite consistent” for the scoring model used. Then, the use and performance of different sum scores to test agreement could be compared in separate paragraphs afterwards, but only with reference to any significance of the difference in performance of the agreement statistics. In some ways I wonder whether the difference in performance of the agreement statistics distracts from the key messages. Perhaps keeping this section shorter, as long as it doesn't undermine validity, will make for a cleaner exposition.
Additional comments: I commend the authors for raising this important measurement question and resolving it with an in-depth analysis. The measurement of maternal experiences related to antenatal care is important. The manuscript supports the measurement of antenatal experience during the late stages of pregnancy as the gold standard, rather than after the birth event. Aside from being more accurate, the timing of the measurement may also assist in improving the quality cycle. Overall, the manuscript is accurate and clear, providing sufficient information on the data, methods and results. There are just minor suggestions to address the presentation of the work undertaken.


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: BRAINCASE AND ENDOCRANIAL ANATOMY OF TWO THALATTOSUCHIAN CROCODYLOMORPHS AND THEIR RELEVANCE IN UNDERSTANDING THEIR ADAPTATIONS TO THE MARINE ENVIRONMENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English is very good on the whole - I have highlighted minor issues in my annotated version of the MS PDF.

Ideally, the original tomograph image stack should be made publicly available for independent verification of the authors' results, but mesh models of the segmentations should be included as electronic supplementary data in STL, PLY or 3D PDF format.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Review: Herrera, Leardi and Fernández.

This manuscript is on the whole well written and easy to follow, with good descriptive sections on both the osteology and neuroanatomy.  There are a few issues with language (agreement for plurals and verbs etc.), but these are very minor and I have annotated the PDF version of the MS to indicate where changes can or should be made.  The descriptive detail alone makes this MS a valuable contribution to the field, and I have no real reservations recommending it for publication with minor corrections

I have a few comments about the content that would need to be dealt with, mostly by adding a little extra discussion or comment.

1.	MLP 72-IV-7-1 was scanned at low resolution on a medical scanner.  The authors rightly mention possible limitations in analysis and interpretation that this may have caused at various points in the text.  I think the resolution is probably sufficient given the size of the specimen, but this issue should probably be discussed in the text more thoroughly.  The voxel dimensions must be given (lns 124-5) for consistency with scan parameters given for BSPG 1984 1258.

2.	A statement about likely ontogenetic stage is needed for both specimens, as this affects the fidelity of the brain cavity endocast for the brain itself (lns 298-318).

3.	Endocast figures – is there any point in including ‘en’ as an annotation?  If it is used it would need to be ‘brain cavity endocast’ because the rest of the segmentations are endocasts too.

4.	The shape of the pituitary fossa should not be assumed to be the shape of the pituitary itself – the shape of the fossa in BSPG 1984 1258 is clearly affected by the anastomosis of the carotid rami, and the rostral projection of the arterial pathway.

5.	The relative length of the endosseous cochlear canal appears to be markedly different in each taxon, but there is no real discussion of what this might mean with respect to hearing sensitivity thresholds (e.g., Walsh et al. 2009; doi:10.1098/rspb.2008.1390).  Could the shorter length in MLP 72-IV-7-1 be an artefact of the lower resolution scan?  This could be discussed.  There seems to be surprisingly little discussion of the labyrinth in either specimen despite the emphasis that previous research has placed on the structure with respect to adaptation during evolutionary transitions out of and into water.  This really could be expanded on.  See Benson et al. (2017; doi: 10.1111/joa.12726) for discussion of SSC canal shape and size in birds for some discussion of limitations.

6.	The olfactory tract projects from the olfactory bulbs to centres in the rest of the telencephalon – in most sauropsids there is probably no trace of the tract on endocasts because the connection is internal, and all that can be seen is the olfactory bulb and cerebral hemispheres.  There may be no obvious demarcation on the endocast between the two even in birds, and the endocasts of these particular crocodylomorphs are especially difficult to interpret.  I have to admit that I am uncomfortable with the idea of the telencephalon being stretched in such a way that the olfactory bulbs end up separated so far away from the cerebral hemispheres because the rostrum lengthens – all of the brain should be enclosed by the skull roof.  In fact, evolutionary expansion of brain regions tends to create a problem because the interconnecting ‘wiring’ has to become longer.  Lengthening CNI as the olfactory epithelium moves rostrally during snout lengthens makes more sense. Are you sure this is the olfactory tract on both endocasts?

In Steneosaurus (Figure 3 A and C), there appears to be a slight bulge rostral of the taper of the telencephalon.  If this is the case, the structure labelled as the olfactory tract would have to be a joined ramus for CNI.  However, CNI would be rather thick if this is the case.  Likewise, if the widening marked ‘olt’ in Cricosaurus (Figure 7 A and B) is actually the olfactory region of the nasal cavity, the ‘olt’ has to be CNI.  This then begs the question of what projects rostrally from the nasal cavity?  Either way, the labelling for the figures would need either a slight tweak or a complete review.

7.	Discussion: As the discussion stands, it is ordered in a logical way, dealing with what each structure of interest can say about (mostly) secondary adaptation to life in water.  However, it seems as though there are two main reasons for increased blood flow in metriorhynchids under discussion here – extra blood for salt excretion, or for some sort of thermoregulation.  I can’t help thinking that the discussion could be made shorter by dealing with these (and other adaptations) and bringing in evidence from the osteology to support or refute them.  However, I am not suggesting restructuring the section, just that the story suggested by the title could have been made clearer and stronger this way.

There should, however, be some mention of other possibilities for increased blood volume in the skull in the pelagic taxa.  One obvious one would be as a cushion for delicate neural tissue for rapid barometric gradients experienced during diving (if, indeed, these animals were diving in any significant way).  This would also account for the poorer fidelity of the brain cavity endocast – a larger ‘jacket’ of sinusoidal tissue.  Another relates to brain size (large brains need more blood), but this can easily be discounted as a variable.
There is a mix of anatomical directional terms in the text (e.g., anterior/rostral; posterior/caudal).  This needs to be standardised.


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: BRAINCASE AND ENDOCRANIAL ANATOMY OF TWO THALATTOSUCHIAN CROCODYLOMORPHS AND THEIR RELEVANCE IN UNDERSTANDING THEIR ADAPTATIONS TO THE MARINE ENVIRONMENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript describes the braincase anatomy of two thalattosuchian taxa based on CT scans. The descriptions are much-needed additions to the body of literature on the neural anatomy of the group. The authors demonstrate a robust knowledge of the topic and the results will improve our understanding of the evolution of the group. This manuscript will certainly contribute a lot to future analyses of the group and of the general crocodyliform evolution.

The manuscript is well-structured, although there is room for improvement.

1) The english used is sometimes difficult to understand. I did some language corrections and I tried my best to suggest changes without significantly altering the text, but I would still recommend the authors send the manuscript for a language review.

2) The description part of the manuscript bears comparisons that sometimes make the text a bit confusing. The authors should consider moving the comparisons to another section, to avoid repetition and to make the descriptions more objective. This include the endocast as well as the osteological comparisons.

3) The figures are small. Maybe this is an issue of the PeerJ platform, but I fear that even taking into account the proportion of the abbreviations and the figures themselves, that the space could be better used.

4) Figure callings and figure abbreviations are sometimes not compatible. For instance, when the text refers to the structure X, many times structure X is not pointed at in the figure. There are many instances where the same structure is pointed at in different views. This number could be reduced in order to make room for other relevant structures. The same features need not be marked all the time.

5) In some cases, instead of marking structures on the photos, I suggest a line drawing is provided together with the specimen photo, and that these markings be left to the line drawings only.
Experimental design: CT scanning was the most appropriate approach for this manuscript. The scanning of fossil braincase has yielded a lot of information on the internal braincase anatomy of several fossil taxa, but many groups are still undersampled. This is the case of thalattosuchians. Several aspects of their anatomy remain dubious and this manuscript adds to the body of literature coving this topic.

There are two simple analyses, however, that could enrich the manuscript.

1) Ancestral State Reconstruction. With this simple analysis of the software Mesquite, it is possible to reconstruct character states for internal branches based on the scorings of the terminal taxa. It will make the statements of the manuscript more robust.

2) Time Calibration. This analysis may slightly run out of the scope of this work, but the authors express their wish of it at the end of the manuscript and it's not too time-consuming. It would put the results in a nice geochronological perspective.
Validity of the findings: The anatomical analyses, although not too extensive, expands our anatomical knowledge to several thalattosuchian groups. The paleobiological implications are tackled for the whole group in a much broader sense.

This covers most of the fidings reported in the manuscript. However, the section "Braincase and endocranial anatomy evolution of thalattosuchians" cannot the sustained without a more robust analysis, as suggested in the previous topic (the Ancestral State Reconstruction).

Depending on the number of taxa, the character states of the internal branches are not too difficult to be determined by hand, but being such a simple computational analysis, I would strongly recommend adding the ASR to the manuscript in order to better support the hypotheses erected here.
Additional comments: I congratulate the authors for this manuscript. The descriptions are much-needed additions to the body of knowledge on the thalattosuchian braincase anatomy. CT scanning is much needed in thalattosuchian literature. The group is overall undersampled and such information can contribute a lot to future analyses of the group and of the general crocodyliform evolution.

I have made only a few suggestions regarding manuscript structure and form. However, I highly recommend adding an Ancestral State Reconstruction analysis to the study in order to better support the hypotheses on thalattosuchian braincase anatomy. It is not time-consuming and will add robustness to the results.

The suggestions made here are only general ones. Please check the annotated PDF to address more particular issues.


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: BRAINCASE AND ENDOCRANIAL ANATOMY OF TWO THALATTOSUCHIAN CROCODYLOMORPHS AND THEIR RELEVANCE IN UNDERSTANDING THEIR ADAPTATIONS TO THE MARINE ENVIRONMENT
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Herrera et al. describe the braincases, endocasts, and semicircular canals of two distantly related thalattosuchian specimens. They provide important new data on the neuroanatomical features of this clade and discuss how it may relate to their adaptation to the marine realm. This is a well-done study and well-written paper. I think it only needs some minor changes to be ready for publication. I very much enjoyed reading this (especially in comparison to other descriptive papers I’ve reviewed recently) and feel it will make a valuable contribution to the growing literature on crocodylomorph neuroanatomical evolution.

Comments:

I received a word document rather than a pdf for review, so I made most of my comments as “track changes” annotations in Word. I also made a number of minor English language spelling/grammar corrections, but as I said above, it was well written, so these aren’t voluminous.

In general, I think the presence of a single XII foramen as characteristic of thalattosuchians is a bit overstated in this manuscript. While most may have only a single opening, some have multiple. More importantly, a single XII opening is fairly common among crocodyliforms, and where we have good sampling, seems fairly variable within species. The authors are welcome to keep this in the manuscript as most thalattosuchians do only have a single opening, however, they may wish to emphasize that this is not unique to thalattosuchians.

Comments on figures:
I did not receive any figure captions with my review materials, so I could not evaluate these.

Could the authors add a white shadow behind the label lines on the endocast figures (Figs. 3, 4, 7, &8) as they did for figures 1, 5, &6? The lines are hard to follow across the darker colors.

Fig 6C – could the authors add a dashed line for the groove for V2 (as they did for V1)?


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: BRAINCASE AND ENDOCRANIAL ANATOMY OF TWO THALATTOSUCHIAN CROCODYLOMORPHS AND THEIR RELEVANCE IN UNDERSTANDING THEIR ADAPTATIONS TO THE MARINE ENVIRONMENT
Review round: 2
Reviewer: 1

Output:
Basic reporting: This submission is about the reviewed manuscript on the braincase anatomy of two thalattosuchian taxa based on CT scans. It is a very welcome addition to the literature on the neural anatomy of the group.

The authors have addressed all the reviews accordingly. They accepted most of modifications and while they refused others, these were all well justified. I accept them and have no further issues with the manuscript.

Among the accepted modifications are new figures, including line drawings and a cladogram with character states plotted on it. These are very well done and they have certianly improved the quality of the manuscript, helping clarify some points and guiding the reader more easily through the text.

This manuscript will contribute to expanding our knowledge in crocodyliform evolution and therefore I recommend the manuscript for publication.
Experimental design: Nothing to add.
Validity of the findings: Nothing to add.
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: BRAINCASE AND ENDOCRANIAL ANATOMY OF TWO THALATTOSUCHIAN CROCODYLOMORPHS AND THEIR RELEVANCE IN UNDERSTANDING THEIR ADAPTATIONS TO THE MARINE ENVIRONMENT
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I am well satisfied with the revisions that the authors have made to the manuscript and the manuscript and figures are much improved. I think they did a good job of addressing the issues raised by the reviewers and I feel the paper is basically ready for publication. There are still a few lingering grammatical issues, but they are much fewer and can be cleaned up during the editing/proofing stage. Congrats to the authors.


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: SERUM LIPID LEVEL IS NOT ASSOCIATED WITH SYMPTOMATIC INTRACEREBRAL HEMORRHAGE AFTER INTRAVENOUS THROMBOLYSIS FOR ACUTE ISCHEMIC STROKE
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is overall well organized and professionally written. It can be clearly understood. The statistical data in tables are well described.  However, the introduction part could include more related information. There are some issues regarding formatting, but which are minor. Here are some concerns:
1.	Even though this study focused on serum lipids, the introduction should include broader background of associated factors to acute ischemic stroke, its treatment options, and how sICH associated with each treatment. When other studies are cited, it is better to specify the sample size of each study, as well as the conclusion.  The general words like “some…and others…” should be avoided.
2.	Font size in Line 93.
3.	“analyses” in Line 121 should be “analysis”.
4.	The number of reference in text should be before the period, so the readers know which sentences are cited from references.
Experimental design: The experiments were designed properly to serve the aim of investigating the association between sICH and functional outcome in patients with acute ischemic stroke treated with intravenous. The only issue I found with the description of methods is lacking of information on when the fasting blood was drawn, and the non-fasting blood drawn as well.
Validity of the findings: The study focuses on association between serum lipid profile and sICH after intravenous thrombolysis for acute ischemic stroke. The conclusion is no association. It is a negative result, but it also provides hard evidence to a controversial debate. Here are some thoughts on the discussion of results:
1.	How did serum lipids tended to an association for lower sICH rate which authors claimed in Line 133-135? How do they compared to other factors to make the conclusion of tendency?
2.	Table 1: To my understanding, the serum lipids were measured in fasting state, while the serum glucose was measured in non-fasting state. Why was serum glucose not recorded in fasting? Please clearly clarify each parameter in fasting or non-fasting state in Table 1.
Additional comments: Overall, it is a study well organized and thoroughly discussed. It provides negative but yet informative results for clinical practice. However, to improve the reading experience of broader readers, the introduction can be expanded to provide more information on the background. There are also some experimental details needs to be specified.


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: SERUM LIPID LEVEL IS NOT ASSOCIATED WITH SYMPTOMATIC INTRACEREBRAL HEMORRHAGE AFTER INTRAVENOUS THROMBOLYSIS FOR ACUTE ISCHEMIC STROKE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Some grammar mistake should be corrected:
In line 152: “independenlty” should be “independently”.
In line 93, the font size is not consistent.
Experimental design: The experiments are rational designed and the conclusions are well supported by the data.
Validity of the findings: The authors showed that that history of diabetes mellitus is significantly associated with sICH. Moreover, based on univariate regression analysis regarding the occurrence of sICH, the serum glucose level, a critical factor of diabetes, was also significant associated with sICH. This co-relationship was also found by other reports (Mishra, Ahmed et al. 2011, Messe, Pervez et al. 2013, Reiter, Teuschl et al. 2014), however, the authors failed to mention this in the introduction or discuss it in the discussion, which make readers who are not experts in this area hard to comprehend the whole paper. It’s better to add some sentences about the relationship of diabetes and sICH in the discussion.
Additional comments: This finding should be interested by the reader of Peer J while some minor modifications are required before publishing.


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: SERUM LIPID LEVEL IS NOT ASSOCIATED WITH SYMPTOMATIC INTRACEREBRAL HEMORRHAGE AFTER INTRAVENOUS THROMBOLYSIS FOR ACUTE ISCHEMIC STROKE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The writing of this manuscript is subject to multiple errors in grammar. Seeking help from a professional English writer is strongly recommended.
Experimental design: The definition of "serum lipid level" and "serum lipid profile" are poorly defined---are they looking at associations of individual serum lipids with sICH, or are they looking at it as a whole? From their results, it seems that they are looking at the individuals, while I am not sure whether the results tell anything. I would suggest authors creating an overall score for the lipids level and looking at the real "lipid profile" and sICH, which could be more helpful and the analysis could make more sense.

The authors may need to have more explanations of the variables, including the exposure variables and potential confounding factors included in the analysis.

The authors did not state the current gap on knowledge in the area, which may not prove its meaningfulness.
Validity of the findings: I would not say that the data is well controlled, since there are some important factors not included---such as education, body mass index, drug (e.g., statin) use. If not assessed, it may be included in the limitation.

Also, again, I am not totally convinced by the results of the regression models. Are there potential over-adjustment (e.g., SBP and DBP, different lipids)? How about collinearity?
Additional comments: The manuscript needs some changes before getting published.


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: SERUM LIPID LEVEL IS NOT ASSOCIATED WITH SYMPTOMATIC INTRACEREBRAL HEMORRHAGE AFTER INTRAVENOUS THROMBOLYSIS FOR ACUTE ISCHEMIC STROKE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised manuscript has added more current study on acute ischemic stroke and its treatments, which helps to understand the purpose of research carried out in this study. It is well organized and is easy to understand. Literatures were properly cited. Overall, it is an interesting and informative study.
Experimental design: The experiments were designed properly to serve the aim of investigating the association between sICH and functional outcome in patients with acute ischemic stroke treated with intravenous.
Validity of the findings: The study provided a negative result, but it also provided hard evidence to a controversial debate. The authors has changes some wordings to avoid over-stating, which is praiseworthy.
Additional comments: Overall, it is a study well organized and thoroughly discussed. It provides a negative but yet informative results for clinical practice.


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: SERUM LIPID LEVEL IS NOT ASSOCIATED WITH SYMPTOMATIC INTRACEREBRAL HEMORRHAGE AFTER INTRAVENOUS THROMBOLYSIS FOR ACUTE ISCHEMIC STROKE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The writing of this manuscript is professional.
Experimental design: The author collected the information of 229 patients and methodically analyzed.
Validity of the findings: The finding that "Serum lipid profile is not associated with symptomatic intracerebral hemorrhage after intravenous thrombolysis for acute ischemic stroke" will interesting to both biological and clinical readers.
Additional comments: All my concerns were properly addressed. I think it suits for publishing now.


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: SERUM LIPID LEVEL IS NOT ASSOCIATED WITH SYMPTOMATIC INTRACEREBRAL HEMORRHAGE AFTER INTRAVENOUS THROMBOLYSIS FOR ACUTE ISCHEMIC STROKE
Review round: 2
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have well addressed my previous comments, and it has been largely improved. I think it looks good now.


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: NOT ALL BRAWN, BUT SOME BRAIN. STRENGTH GAINS AFTER TRAINING ALTERS KINEMATIC MOTOR ABUNDANCE IN HOPPING
Review round: 1
Reviewer: 1

Output:
Basic reporting: I commend the authors on a manuscript which is very interesting, well written and novel. The raw data supplied with the manuscript allows readers to use or view the authors code to further understand the methods used in this study. This, together with the clear language used throughout the manuscript aids the reader to understand the complex uncontrolled manifold method. For this reason, I believe the study is appropriate for PeerJ and will be of interest its readers.

The abstract for this manuscript was clear and summarised the study well. The abstract also conforms to the journal standards. Enough background was given in the manuscript to allow the reader to understand why the research was undertaken, and what importance this research could have on the field. The literature referenced was relevant and recent and the formatting and language used throughout the manuscript was appropriate.

In general the figures were relevant to the work and well described. However, in Figures 2-4 I could not see any of the mean data points on the graphs, as the shaded ±SD of the data seemed to overlay this data. This must be amended in the revised version. I would also suggest the axes be amended in Figure 3, as explained in the general comments.
Experimental design: This study was well designed and appropriate methods were used to address the aims and objectives stated. The study is also original and provides new information to the field of motor control. Although the materials and methods were well written, I would suggest the clarification of a couple of points (as outlined in the general comments) to ensure that the methods are fully repeatable.

The study was approved by a local REC and informed consent was obtained from all participants.
Validity of the findings: The data reported in this study appears to be robust and statistically sound. My main concern is that the inclusion and exclusion criteria were not adequately described in this study, and should be clarified in the revised manuscript. In general however, the data was discussed well and the conclusions drawn were fair. Readers may benefit from a description on the potential implications this study may have in the discussion.
Additional comments: Main Points:
1.	Clarification of the protocols used in recruitment and during data collection recommended.
2.	It is not clear whether the excluded data led to statistical differences in the results as the authors have only described the differences as ‘small’.
3.	It is not clear why the authors have used increases of 1Nm/kg as the benchmark for comparing to changes in IMA.
4.	The authors have not argued their reason for analysing variable numbers of hop cycles between individuals (cited as ranging between 20 and 57 cycles).

Abstract
Line 18:   I would suggest changing the word ‘manuscript’ in this sentence to ‘study’.

Introduction
Lines 64-68: Please ensure this sentence is all in the same tense (preferably past tense).
Line 73: Remove semicolon after reference
Line 75: Remove semicolon after reference
Line 79: Remove comma before ‘…may’
Lines 82-83: Please elaborate on the differences between these two papers. Some of the readers may not have access to these papers but may wish to understand the differences in order to understand the reasoning behind the methods used in your study.

Materials and Methods
Line 110: This section could be titled ‘Participants’.
Line 113: What are your definition of ‘healthy’ and ‘active’ here? How how can you be confident that all involved were active to similar extents? Was a thorough check of the individuals’ medical history taken to ensure that none have had any lower limb injuries which may affect their hopping biomechanics? Different levels of health/activity and baseline muscle strengths within the group could affect the interpretation of the mean results.
Line 113: Please clarify what the inclusion and exclusion criteria for the study were. This will aid in clarifying my comment above too.
Line 132: Please clarify here that your analysis was based on the combined group, and that you did not analyse both groups separately or chose to assess the data from one group only.
Line 144: Here, you have referenced another paper in which the biomechanical model is described. To ensure that the readers could replicate your methods from this paper alone, please mention the model used and describe whether this model adheres to the International Society of Biomechanics standards.
Furthermore, on inspection of the referenced paper, I find that it does not contain the marker placement protocol, as stated in this manuscript. Please insert the appropriate reference (Liew et al., 2015).
FYI:
Wu, G. & Cavanagh, P.R (1995). “ISB Recommendations in the Reporting for Standardization of Kinematic Data.” J Biomechanics 28(10) 1257–1261.
Grood, E.S., Suntay, W (1983). “A Joint Coordinate System for the Clinical Description of Three-Dimensional Motions. Application to the Knee” Transactions of the American Society of Mechanical Engineers 105:136–144.

Line 160: Please clarify what you mean by the ‘proximal end of the pelvic segment’. Is this calculated from the positions of both anterior superior iliac spines?
 Line 170: The start of this reads as if a part of the sentence is missing. Although I understand that you are referring to the variables in the equations above, please refer to these equations in the text and consider capitalising the start of the sentence, or rephrasing slightly.
For example: ‘In the above equation (1), non-goal equivalent variance (NGEV) represents…’
Lines 189-191: Please insert appropriate reference here.

Results:
Line 199: Remove one of the words ‘baseline’ in this sentence.
Lines 200-204: Here, it is stated that the differences between the demographics and ankle/knee beta coefficients in the full group (n = 30) and the analysed group (n = 25) were ‘small’. Small differences can present statistical or clinical differences, which would influence the interpretation of the results. Please consider statistically comparing these variables to confirm that analyses carried out was valid.
Line 204: I recommend starting a new paragraph at ‘Baseline hopping kinematics…’ as these results refer only to the group analysed, unlike the previous sentences.
Lines 209-217: It is not clear why the authors have used increases of 1Nm/kg as the benchmark for comparing to changes in IMA. Was this arbitrarily chosen, or is this deemed to be the minimal clinically important change in strength?

Discussion:
Line 261: Missing word ‘gain’ after ‘…knee extensor strength…’
Line 289: This is the first place it is stated that the number of hop cycles analysed per participant varied between 20 and 57 cycles. Please also declare this in the results section.
More importantly, it would benefit the reader to understand why you chose this method of assessing the groups, rather than choosing x number of hop cycles (e.g. 20) to assess per individual.  Could the method used not influence the data analysed and thus the interpretations made?

Figure 2:
Please add ± to legend in front of ‘standard deviation’ and add n number.
Please amend the figures so that the mean data points can be visualised.

Figure 3:
Please add ± to legend in front of ‘standard deviation’ and add n number.
Please amend the figures so that the mean data points can be visualised.
Please annotate the y axes of the individual graphs independently, so that it is perfectly clear which graph shows the ratio and which show the variances.

Figure 4:
Please amend the figures so that the mean data points can be visualised.

Other:
1.	Consider moving Figure S1 into the main manuscript, as this is a good and informative figure.
2.	Please add in a sentence or two in the discussion on the potential implications this study may have.
3.	Often in this manuscript, a reference is cited in the middle of a sentence, where it could be placed at the end. Consider moving some of these references to the end of sentences so that they are easier to read. I realise this is an extremely minor comment (nit-picking) and is most definitely personal preference.


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: NOT ALL BRAWN, BUT SOME BRAIN. STRENGTH GAINS AFTER TRAINING ALTERS KINEMATIC MOTOR ABUNDANCE IN HOPPING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors analyzed motor abundance using segmental angles, not joint angles. Using segmental angles (rather than joint angles) is potentially a serious drawback because segmental angles cannot be changed independently: Changing one of the angles forces changes in other angles to preserve body integrity. This means that, even if there is no specific neural control strategy, co-variation among joint angles may be expected. By pure chance, this co-variation could affect the UCM-based analysis. In actual, the authors wrote as follows in the Introduction (page4 line50) “-, along which flexion-extension occurs.”
Experimental design: Page4 line47
In hopping, I think that perturbation to the COM trajectory is more affected by the trunk, head, and upper arm, but was not it necessary to add these segments?

Page8 line134
In hopping, it was written that the authors instructed only “comfortable pace”, but did not the position of the upper limbs or trunk instruct anything? Then it seems that the perturbation to the COM trajectory will change by the effect of trunk and upper limbs.
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: NOT ALL BRAWN, BUT SOME BRAIN. STRENGTH GAINS AFTER TRAINING ALTERS KINEMATIC MOTOR ABUNDANCE IN HOPPING
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I would like to thank the authors for all the amendments made to their manuscript. The manuscript is now much clearer and informative. Having read through the paper a few times, I only have two very minor comments.

1. Line 164: When describing the coordinate system used in this study, the authors state that the mediolateral (X) axis was pointing 'laterally'. When describing the left limb, this would mean the axis is positive to the left, but when describing the right limb it would mean the axis is positive to the right. I assume this is a mistake, and I am guessing it should read that the axis was positive to the left. Please amend/clarify this in the paper.
2. Line 201: The word 'That' can be uncapitalized here as it is in the middle of a sentence.

Please note that the line numbers refer to those in the PDF document and not the Word document with tracked changes. They are slightly different for some reason.


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: NOT ALL BRAWN, BUT SOME BRAIN. STRENGTH GAINS AFTER TRAINING ALTERS KINEMATIC MOTOR ABUNDANCE IN HOPPING
Review round: 2
Reviewer: 2

Output:
Basic reporting: Thank you for your polite answer. I could understand why you chose a segment angle as an element variable, not a joint angle.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: EFFECTS OF BLOOD PARASITE INFECTION AND INNATE IMMUNE GENETIC DIVERSITY ON MATING PATTERNS IN A PASSERINE BIRD BREEDING IN CONTRASTED HABITATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is coherent and well written, although see my specific comments below regarding the working hypothesis and predictions, which are not clearly stated in the introduction. The chosen figures are not appropriately labeled, and I made some suggestions to the authors on how to improve their accessibility to readers with minor changes.
Experimental design: The research question was well defined, and the authors did an excellent work in laying out their goal for this study. The experimental design and methods used in this study were chosen well to answer the questions of interest and the materials and methods section is sufficiently detailed to allow its replication.
Validity of the findings: Most of my comments to the authors relate to their findings and the interpretation of their results. I hope the authors will find my comments useful and will use my suggestions to improve the integrity of their manuscript.
Additional comments: This manuscript details an experiment aimed at understanding mating choice in Tree swallows based on three measures of heterogeneity: (1) infection by parasites, (2) β-defensin genetic diversity, and (3) habitat type. The authors differentiated between social and extra-pair male partners and monitored couples during a period of four years.

Specific comments

Social versus extra-pair male partners:
First, the authors need to state their hypothesis and the predictions stemming from it more clearly. Their goal was to assess whether there is evidence for assortative/disassortative mating in Tree swallows based on three different heterogeneity features. The authors explained very clearly how each of these three features may play a role in mate choice, but they have not adequately addressed the distinction between social and extra-pair male partners. The authors should detail their hypothesis on the different selection pressure imposed on the females when choosing a social male partner versus an extra-pair male partner; and provide predictions on how females should choose each of the partner types.

I think that if the authors were to state their hypothesis and predictions more clearly, it would have reflected also on their statistical analysis and interpretation of their results. More specifically, if one assumes that the selection pressure imposed on a female is different when choosing a social partner versus an extra-pair one, then one should distinguish between social partners who are also the genetic partners of the females and between social partners who are not the genetic partners of a specific female. I briefly scanned the raw data the authors provided with the manuscript and noticed that the authors have a significant sample size to test this hypothesis. This distinction may alter the results of this study and should be addressed.

Weak effect:
The authors found no significant mating choice based on individual levels of parasite infection, rather they found an indication of such a trend (p < 0.1). To address this finding as a “weak effect” the authors should provide a power analysis to investigate whether the lack of statistically significant differences is due to small effect size/sample size, and they should report their type II error in this context.

Habitat quality:
The authors need to explain better their terminology in this context. How did they arrive at the conclusion that intense farmland is a low-quality habitat and non-intensive farmland habitat is a high-quality one? They should detail the measures by which they arrived at this conclusion. This is especially important considering that they report the counterintuitive observation of infected individuals preferably inhabiting the habitat they define as high-quality.

Figures:
Two comments about the figures: (1) It would make the figures much more accessible if the authors were to add titles to each panel to indicate what feature of focus is presented there (AVBD2/7, level of parasite infection, etc.); and (2) The authors should consider showing the difference between observed and expected instead of a column for each measure, and then highlight the 0 level. This will make it easier to detect whether groups are statistically different from 0 or not.


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: EFFECTS OF BLOOD PARASITE INFECTION AND INNATE IMMUNE GENETIC DIVERSITY ON MATING PATTERNS IN A PASSERINE BIRD BREEDING IN CONTRASTED HABITATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This paper describes the results of a four-year field experiment examining patterns of assortative mating with respect to both parasite infection and heterozygosity at two immune genes. In addition to looking at overall patterns, the authors also explore the possibility that mate choice patterns might differ for within vs. extra-pair partners and across habitats that differ in quality. There is a lot of interest in context dependent mate choice and the mechanisms that might maintain variation in mate choice across environments, so this paper is a timely contribution. Moreover, the paper includes a remarkable amount of field data and this robust sample size (especially for the parasite related questions) clearly represents a huge amount of field and lab work. That being said, I do that that as currently written and analyzed there are some issues that make it hard to determine exactly what, if any, differences exist between habitats and hard to interpret exactly what the patterns, or lack of patterns, that the authors describe here mean in a larger context. One of the main conclusions, that there is a ‘difference between habitats in mating patterns related to infection status’ is not at all clear to me. I’ve made several comments below on this point. I found the assortative mating with respect to AvBD result more convincing, though I still had a few questions about its interpretation. Finally, I think there are a number of places where the results, methods, and analyses are somewhat confusing or not fully explained. I’ve detailed these and some more minor comments below.

Specific Comments
•	One of the main claims of the paper is that there is a ‘difference between habitats in mating patterns related to infection status’. The authors rightly point out that this is due to a higher number of infected birds in non-intensive habitats. If I’m understanding correctly, the claim that mating patterns differ is based on the fact that the proportion of pairs that are 0-0, 0-1, 1-0, and 1-1 (1 infected, 0 not) is different between the habitats. While the percentage in each category clearly does differ between the two habitats, this seems to be an inescapable product of baseline infection rates and not any clear evidence for different patterns of assortative/dis-assortative mating (which is how it seems to be interpreted). The same pattern would presumably be found for any 1/0 trait that differed in base frequency by habitat whether or not it played any role at all in mate choice. That isn’t to say that infection—and the differences in infection by habitat—aren’t interesting, but I don’t think that the statistical tests currently run are really testing for habitat differences in mating patterns. It would seem that a more fair comparison would be to test for assortative mating within each habitat type (compared to random expectations within that habitat) and ask whether those patterns differ rather than to compare the raw ratios of pair types across the habitats.
•	I realize that this study builds on a lot of previous work, but I think that the methods are really not sufficient in several places. Citations to the previous papers are fine, but at least a brief summary of the relevant info would be useful to include here so that the reader does not have to look up a variety of separate references to understand what was done. I’ve noted a few places in particular in the comments where I thought more detail was needed.
•	Line 131: What is assignment rate? What is % EPP and does that vary by site/habitat?
•	Lines 136-138: What does this mean in terms of the number of farms that were included? Do some farms end up including only the 40 boxes at that farm while others include multiple neighboring farms? Given that infection status is habitat specific, these choices seem very important because it could really alter the ‘random’ expectation for mating patterns. Are the results the same if you randomize only within a farm? How do the number of possible mating choices differ between the farms and what effect might that have on these tests?
•	Throughout the text, the authors argue that mating choices might differ with respect to infection status. However, there is no discussion of the fact that the mate choice patterns (putative response) occurred temporally prior to the sampling for infection (putative causal driver of response). Of course if these are chronic infections then measuring them after mate choice has occurred might still give a good picture of what infection status was at the time choices were made, but this isn’t necessarily true if infection is picked up on the breeding grounds (and perhaps this is the case given the habitat dependent associations). This isn’t a problem for the heterozygosity comparisons since those are stable, but the limitation and potential for different interpretations should be discussed.
•	Lines 185-190: It isn’t clear to me why the preference would only be exhibited in heterozygous females when presumably (under this model) all females would benefit from a heterozygous mate. Later in the paragraph male preference is mentioned briefly and I suppose this is one mechanism (mutual mate choice) that could produce the pattern here, but the idea is not really fleshed out.
•	Figure 1: I found these figures very difficult to interpret and I wonder if there is a better way to visualize these results (even a table might be clearer). It wasn’t clear from the caption why the bars were different heights and that you need to add panels a+b and c+d to get the full sample of pairings. Visualizing the spread of the randomized distribution with respect to the observed point would possibly be more helpful (something similar to figure S1).

Minor Comments
•	Line 61: ‘results’ instead of ‘result’ (or change to infections)
•	Lines 94: It would be helpful to have a short description of what makes these ‘high’ vs. ‘low’ quality here without having to refer to previous work.
•	Table 1: I’m not sure this table adds much. I’m also a bit confused about the ‘total’ column since it doesn’t seem to match the numbers in the methods/results section. Perhaps this one is adding multiple records of individuals across years and the methods reports unique individuals?


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: EFFECTS OF BLOOD PARASITE INFECTION AND INNATE IMMUNE GENETIC DIVERSITY ON MATING PATTERNS IN A PASSERINE BIRD BREEDING IN CONTRASTED HABITATS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I am happy with the changes that the author's have made in response to my earlier 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: OPTIMAL AND NEAR-OPTIMAL EXPONENT-PAIRS FOR THE BERTALANFFY-PÜTTER GROWTH MODEL
Review round: 1
Reviewer: 1

Output:
Basic reporting: English language and style are fine/minor spell check required:
1) Review the use of colons, commas, periods, semi-colons  for the equations  in the lines 44,61,106,169,179,291 and 292.
2) line 169: improve writing, specifically remove the text ", eq. (1)".

Review the line 62,  the definition of hypergeometric function according to Seaborn (Hypergeometric functions and their applications, V8, pp 50) it is a solution of a second-order linear ordinary differential equation (ODE).  Thus, the proposed model of first order ODE does not fit. However, at work (Ohnishi, Yamakawa & Akamine, 2014) finds a relationship with incomplete beta function which is a special type of hypergeometric function. In this relation the solution x obeys the form B (x; a, 0) -B (x0; a, 0) = kt. Note that x is not a function of incomplete beta function.

Seaborn, J. B. (2013). Hypergeometric functions and their applications (Vol. 8). Springer Science & Business Media.
Experimental design: I commend the authors for their extensive data set. In addition, the manuscript is clearly written in professional, unambiguous language. The statistical analysis is very good and well summarized. However, the authors suggest in the title, abstract, introduction and conclusion that only SSE and AIC are sufficient to optimize the parameters of the Pütter-Bertalanffy equation. However,  they use very advanced tools when compared to SSE and AIC such as  Nelder-Mead amoeba and  Simulated Annealing methods. This mathematics appears extensively in the sections Preparatory screening, Semi-automated optimization and Custom-made simulated annealing. I recommend reviewing the abstract and  conclusion which should be improved upon before Acceptance. Summarizing, it is not possible only with SSE and AIC to get article completion.
Validity of the findings: The paper is well-written and correct. Many new results are derived,  which are original and worth for publication. The masses collected (20167 fish) follow a normal distribution but it is not indicated if this choice was intentional.
Additional comments: The paper has many interesting results and can be published if the authors address after minor revision.


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: OPTIMAL AND NEAR-OPTIMAL EXPONENT-PAIRS FOR THE BERTALANFFY-PÜTTER GROWTH MODEL
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is structured well. The literature referenced is appropriate, the results are relevant and test some hypotheses, but these hypotheses could be clearer (see below). The figures and table are clear and useful.

I do think the paper suffers from a few key problems that make things unclear and there are some English language problems. One of the issues I found with the paper was flow: the authors use a lot or 'passive tense' rather than 'active tense'. Hence, I do recommend some major re-writes to increase clarity (but I don't recommend any changes to the study design).

Examples here include:

Line 27: 'it was conjectured' rather than 'We hypothesized'. It is okay to use the first person, this will make things more clear and direct with less chance to confuse readers. It will also reduce word usage and avoid wanting to invert sentence clauses.

Line 100: 'As Shi et al. (2014) observed, already for the generalized Bertalanffy model (i.e. b = 1, a, p, q, m0 are optimized) data fitting was impeded by numerical instability.' I suggest re-writing this sentence to say: Numerical instability tends to imped fitting the generalized Bertalanffy model (i.e. optimization a, p, q, m0 when b = 1) to noisy data (Shi et al. 2014).

Line 104: change 'the paper' to either first or third person throughout the whole paper. I recommend first person and just say something like: "we used a grid search to estimate growth model exponents.'

Furthermore, the paper has some odd sentences that appear incomplete. For example, line 26 in the abstract:

"Thereby, data fitting used the method of least squares, minimizing the sum of squared
27 errors (SSE)." This sentence has some uncertainty what point the "thereby" is following up. A second problem is that the objective of the sentence "data fitting used the method of least squares" is unknown because the key points or knowledge gaps being tested in the paper have yet to be introduced. I would re-write these portions of the abstract to introduce the topic, then the knowledge gaps, then the objectives in the paper. And its okay (and clearer) to be direct.

Another challenge with passive tense is that the major conclusions appear soft and vague rather than clear and direct.

Line 33: " SSE is used, when predictive power is needed alone, and AIC is used, when simplicity of the model and explanatory power are needed." This sentence needs a re-write to be direct and active. Tell the reader your conclusions/recommendations such as: 'We recommend estimating the general VBGF in cases when predictive power and bias reduction are preferred (such as in fishery stock assessments), although we note the special case VBGF remains a parsimonious model in many cases.' This is a really key result but the sentence structure masks the finding.

Another key problem I found was that I didn't fully understand the key objectives of the paper until the very end. Neither the Abstract nor Introduction clearly sets up the main objectives.

The objective is loosely stated on line 75, but I don't think this does a suitable job describing what is being done. What are the two dimensions? What variability is referred to? Are you more interested in reducing unexplained variability? Is it variability in growth parameter estimates themselves?

Also, some paragraphs need to be merged or separated. For example, line 257 and line 263 are new paragraphs but their topic sentences refer to results in a previous paragraph. Either merge these points into a single paragraph or make the paragraphs more independent of previous paragraphs.
Experimental design: I found the experimental design very competent. The presentation of the model development and the analyses conducted is clear and expert. I congratulate the authors on this!

The research questions are defined, but not always very clear or meaningful. The authors can see my above comments about the language problems. I think the authors need to use active tense and state quite directly what the knowledge gaps are, what the objectives are, and what the hypotheses were (conjecture is too weak of a word, in my opinion). These are all hinted at in the introduction, but not clearly and I think the average reader may get lost on the points in the Introduction and Methods which set up the study design.

For example, Line 257 suggests there was a hypothesis that a and b would be correlated, and that optimal SSE would be found along the diagonal of the a -> b grid search. Where was this hypothesis stated? The methods hint at it, but make this more clear.

I would recommend a single paragraph early in the Methods which is a "Study Overview" where the authors use very general language to describe the problems and general solutions/approaches to solve these problems. By the time we get to the other sections in the Methods, the authors expertise is obvious and the details are useful for replication by other expert readers.
Validity of the findings: At times reading the Discussion and Conclusion, I was still unsure what the take home conclusions ought to be. Should we use the general VBGF or should we still use the special case VBGF. These nuances are described, but I think the authors should be clear about when it works and when it doesn't. I think this is mostly a language issue though, and so some revisions in the Discussion and Conclusions should solve this problem. Without a suitable revision on these problems, I think the main findings will remain elusive for a lot of readers.

The grid search estimation of the general exponents reduced bias via SSE but was not the most parsimonious model via AIC. I like the use of the two model performance criteria, I wonder if these benefits could be expanded further in the Discussion. What about bias reductions in fishery stock assessments?

The lead sentence in the Discussion poses a question, but it is so specific to the results that a general reader doesn't know what to take home. What 10% reduction? What SSE? What two exponents?

Instead, I recommend simply saying a more general conclusion like: "Estimating the general VBGF reduced bias in growth estimates but increased model complexity. We are thus left with the remaining question: is this improved performance worth additional complexity? According to parsimonious model selection, like AIC,  the answer is no. However, this bias reduction may be worth the tradeoff with complexity in some situations where predictive power is solely preferred, like natural resource management, which relies on careful quantitative assessments to recommend policies for sustainable resource usage." Obviously this can be changed up, but I think it makes the key points and remaining questions more clear to the average reader (which may be fishery/resource managers and practitioners).
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: OPTIMAL AND NEAR-OPTIMAL EXPONENT-PAIRS FOR THE BERTALANFFY-PÜTTER GROWTH MODEL
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This is a very good paper.


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

Input:
Title: OPTIMAL AND NEAR-OPTIMAL EXPONENT-PAIRS FOR THE BERTALANFFY-PÜTTER GROWTH MODEL
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors were able to make my recommended revisions on sentence structure, and I found the reporting in the paper improved and sufficient. Thanks for making those changes!
Experimental design: I really enjoy the way the model design for the paper. I think the revisions helped to clarify what the overall questions were, to which the design then helps address and find answers for.
Validity of the findings: I think the findings are quite robust, as evidenced by the statistical design the authors used. I think the findings are somewhat expected (that the special case VBGF is generally the most parsimonious, but not always the best for prediction).

The discussion is useful to couch these findings more generally in the fisheries literature.
Additional comments: Good job on the revisions, I was very satisfied with the new changes in the discussion and the framing of the objectives/hypotheses.


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: EFFECTS OF A SIX-WEEK WEIGHTED-IMPLEMENT THROWING PROGRAM ON BASEBALL PITCHING VELOCITY, KINEMATICS, ARM STRESS, AND ARM RANGE OF MOTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors support their arguments throughout with more than adequate references. There are recommendations in the attached document that suggest the authors use more sub-headings for their methods and results section. The figures are of sufficient quality. Table captions could use greater detail - a table with its caption should be able to stand alone from the document.
Experimental design: The study as it is currently written suffers a design flaw in that other studies examining the effect of weighted baseballs on velocity and injury risk have all had control groups. This study does not have a control group. The novel contribution this study provides is a set of exercises which are targeted at building a pitcher's tolerance to throwing. Theoretically, these exercises should provide a protective effect for the pitcher. The study as currently designed does not effectively deliver this message. The researcher's findings indicate there was an unexpected effect in this study - not all pitchers gained velocity. There is a post-hoc analysis of the velocity increase and decrease groups, but the main focus of this study should be centred around that (unless the researchers would agree to collecting a 6 week trial with a control group that performed weighted baseball training without these exercises - but that is neither practical or ethical).
Validity of the findings: The influence of the HTKC exercises on this type of training are significant and could be stated more prominently in the article. Kinematic data analysis appears to be done well. The fact these data were not collected in a traditional academic environment, but still had state of the art technical collection methods should be applauded and encouraged.
Additional comments: Very important work with the rise of weighted baseball training. It's also very important to shift some of the research being done from purely academic labs to the places where athletes are actually going to get better. Sometimes there are things overstated that don't make that big of an impact to your study, and sometimes there are things understated that would make a huge impact. I would be happy to review this research again, as I see it as being very important to the industry and sports science.


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: EFFECTS OF A SIX-WEEK WEIGHTED-IMPLEMENT THROWING PROGRAM ON BASEBALL PITCHING VELOCITY, KINEMATICS, ARM STRESS, AND ARM RANGE OF MOTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors presented a well written manuscript on a very topical subject that requires much more experimental study (especially in the open literature). For their efforts, the authors must be commended.

With respect to basic reporting, there are only minor reviews suggested at this time. They are as follows:

Abstract: In the results section of the abstract, can you clarify which experimental group the outcome variables were higher for to make it clear for a reader that only reads the abstract?

Lines 271-275: This appears to be a planned post hoc analysis and therefore should be described in the methods section before it is introduced in the discussion
Experimental design: From an experimental design perspective, the study presented in the mansucript has some severe limitations that must be addressed. The authors are attempting to study the effects of a "weighted-impleneted throwing program" on velocity and biomechanical outcome variables. The gold standard for this study would be a RCT. The presented study is not that type of study. The reviewer understands there are often logistical limiatations (or other constraints) that cannot be easily overcome to produce a gold standard study, and the reviewer concedes that it is still often valuable to present other studies in the literatrue. With that being said, there are options the authors could explore to improve the design of their study.

Specifically:

Lines 91-98: In terms of exclusion criteria, where participants asked about previous training modalities they have utilized? Was this training modality novel to all participants or had some undergone similar types of training previously? This comment is designed to tease out whether or not previous training could be a confounding factor.

Knowing more about each individual participants training history would help provide context for the pre- post- changes being statistically tested in this study. Although they would not be able to technically serve as their own within subject controls, the study results could be presented and interpreted with much greater confidence.

From a methodological perspective, one last concern remains:

Lines 157-161: For the reader not familiar with the new Fleisig method cited as Fleisig et al. 2017, does this biomechanical marker comply with ISB suggested model (Wu et al. 2005)? Based on the extensive marker set described in Lines 131-140, the biomechanical model may be assumed, but an explicit statement on the model is still beneficial for the reader.
Validity of the findings: The validity of the finidngs are difficult to comment on given the limitations in experimental design.

Lines 526-534: This comment is a fair comment and in the strength and conditioning literature this problem is somewhat systematic. One suggestion this reviewer can make is for the authors to go back to their participant pool (if avaiable) and get detailed training histories for the weeks or months leading up to the study. This will help provide context for the results and improve the validity of the findings.

Lines 567-568: Small sample size is a difficult problem to overcome in any human experimentation that involves as extensive an intervention as that described in this manuscript. One suggestion to increase statistical power is to include control matches in the study.
Additional comments: Two summeraize, this reviewer's two major suggestions for the authors are:

1. Include a control matched group of participants that use a non weighted-implemented throwing program so that the true effects of the weighted implemented throwing program can be properly teased out. (Understood this may not be possible)

2. Alternatively, go back to the participants of the study and survey the participants with respect to their training prior to the study. This will provide better context for the results and discussion and improve the validity of the findings.


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: EFFECTS OF A SIX-WEEK WEIGHTED-IMPLEMENT THROWING PROGRAM ON BASEBALL PITCHING VELOCITY, KINEMATICS, ARM STRESS, AND ARM RANGE OF MOTION
Review round: 1
Reviewer: 3

Output:
Basic reporting: see attached document
Experimental design: see attached document
Validity of the findings: no comments.
Additional comments: Well done study and impressive literature review for this paper.


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

Input:
Title: EFFECTS OF A SIX-WEEK WEIGHTED-IMPLEMENT THROWING PROGRAM ON BASEBALL PITCHING VELOCITY, KINEMATICS, ARM STRESS, AND ARM RANGE OF MOTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: Limitations/Conclusions
Reinold reference – either include first initial in reference, or don’t include the initial – consistency throughout.

Table 1: Some inconsistencies in this table. This table has some inconsistencies. We know the n = 19 - the header on first column should be Age (Years), and following columns switch between all caps or lower case for units (CM vs. cm). Be consistent with these.
Experimental design: Line 72: Suggestion for this paragraph leading into the purpose: I think this more clearly states what the intentions of this study are and makes no inferences to an RCT: Feel free to disagree or modify, but I feel this clarifies your purpose, without indicating that we’re doing some sort of an RCT. Purely looking at the changes that occur during this training alongside the manual therapy and HTKC program, and we can do control group studies in the future.

Driveline baseball (Seattle, Washington, USA) has developed weighted baseball training programs, which have been used by many professional and collegiate pitchers. Those pitchers who completed the weighted implement training programs Driveline Baseball’s summer training programs have on average increased pitching velocity 2.7 MPH in 2016 and 3.3 MPH in 2017 (Driveline Baseball, 2016 and 2017). However, there remains no conclusive evidence explaining the mechanism of the velocity gains, and research indicates the phenomenon of weighted-ball training increasing “arm strength” may be incorrect (Cressey, 2013).

Line 84: Purpose Statement: Suggest rephrasing:
The purpose of this study is to examine changes in kinetics, kinematics, and performance, occurring in pitchers who complete weighted implement and individualized training routines geared around combating the negative effects of throwing. We hypothesize the previously described program will increase external rotation, ball velocity, and elbow varus torque.

Line 90: Use of sub-headings is helpful to break up a detailed methods section like this one. I think you can break the methods down even further, particularly after line 112.
•	Range of motion testing
•	Kinematics
•	Pitcher testing preparation
•	Data Analysis

•	Training Methods
o	Warm up
o	Resistance training
o	Plyometric training
o	Long toss
o	Etc

Line 316: Define what “cleaning data means”. Grubbs Analysis and data replacement?
Validity of the findings: Results section: wherever there are values reported, present variance as well as means. +/- SD or SE.
Additional comments: Authors made significant improvements in the manuscript. Suggestions included are to just strengthen the manuscript - it is acceptable 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: EFFECTS OF A SIX-WEEK WEIGHTED-IMPLEMENT THROWING PROGRAM ON BASEBALL PITCHING VELOCITY, KINEMATICS, ARM STRESS, AND ARM RANGE OF MOTION
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have addressed each of this reviewer's concerns with respect to basic reporting.
Experimental design: The authors were not able to address the authors primary concern with respect to including a true control matched group. Nor were the authors able to re-connect with participants to include detailed training histories prior to the study. With that being said, the authors were able to provide a general description of the participants' training prior to the study and have been able to acknowledge the limitation in their experimental design.
Validity of the findings: Given the addition of a general description of the participants' training history and the acknowledged limitations of the experimental design, the study is now better framed to provide valid findings within the limited scope.
Additional comments: None.


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

Input:
Title: HEAVIER- AND LIGHTER-LOAD ISOLATED LUMBAR EXTENSION RESISTANCE TRAINING PRODUCE SIMILAR STRENGTH INCREASES, BUT DIFFERENT PERCEPTUAL RESPONSES, IN HEALTHY MALES AND FEMALES
Review round: 1
Reviewer: 1

Output:
Basic reporting: NA
Experimental design: NA
Validity of the findings: NA
Additional comments: GENERAL COMMENTS

Overall, this is an interesting study that adds value to the literature. However, there a few serious problems that needs to be improved before the manuscript is approved for publication.

First, the manuscript is written with a clinical orientation despite the fact that participants were healthy. This is misleading and should be changed throughout.

Second, there is a serious confounder in this study. Participants practiced the test on each and every session with the MVCs. This needs to be acknowledged and discussed as a limitation and as a possible reason accounting for the lack of differences between the groups.

Third, some of the results are presented in an unclear manner. Specifically, Table 2 can be improved and graphs are needed to illustrate the individual responses in both groups for the main outcome measures.

Forth, there are a number of overreaching conclusions and mismatches between the claims and the citations.

SPECIFIC COMMENTS

ABSTRACT

Line 40 – Add “to momentary failure.” After MVC.

Lines 40-43 – Add an indication of effect size. Maybe CIs of differences for the main outcomes or even percent difference. P values are not enough.

Line 43 – I would say that the present study “shows” rather than “supports”.

Lines 44-47 – You need to change the practical suggestion part as is not supported by the data. You tested healthy, uninjured participants. It remains unclear if the results of the present study will persist with CLBP patients.

INTRODUCTION

The message of the first paragraph is not fully agreed upon. I suggest writing it in a more balanced and suggestive tone and possibly discuss the conflicting perspectives. Also, I believe that citing Schoenfeld’s meta-analysis on reaching failure is important and relevant.

The second paragraph begins with a detailed discussion on perception of effort and discomfort but it is unclear what these perceptions are as they have not been defined. Begin this paragraph with a brief introduction to these scales and their definitions. The rest of the paragraph would then be easier to understand and follow.

I wonder if you can reduce the amount of abbreviations. Already, by the second paragraph, excluding the physiological abbreviations (e.g., lactate), I counted four. Personally, I find it harder to read a paper this way.

Lines 75-80 - I disagree with the way you set up setting up the research question around rehabilitation. You did not test injured participants and thus the results do not generalize to such populations.

Lines 81-96 – This paragraph is somewhat confusing. The topics seem to change suddenly without flow.  Perhaps just discuss the comparison studies and their limitations and remove the sentences dealing with causes of CLBP.

Line 90 – Morton did not directly confirm that all fibers are activated when going to failure.

Line 92 – I am not sure what the purpose of citing it and discussing the study by Risch et al as based on this sentence, no comparisons to other loads were made and low loads were used. I fail to see the relevance here.

Lines 93-96 - Based on the short literature review in this paragraph, I am left confused as to what it is showing us and to what holes in the literature it points to. It seems as if studies that used low loads and did not implement failure led to beneficial effects.

Lines 97-101 – I would definitely use softer language. “Often almost completely passive” is too strong and likely inaccurate. Physiotherapists regularly use exercises and there are indeed many studies showing effectiveness of exercise to CLBP with ILEX RT being one of them. I would set up the questions in a “fairer” way: exercise seems to be effective to reduce CLBP, with ILEX RT being one strategy found to be useful.

Line 102 – I would make a clearer distinction between prevention (which I think is a more suitable angle for your study given that you examined healthy adults) and pain reduction to those already suffering from CLBP. While the distinction is there, I think it needs to be emphasized more.  But again, I disagree with the strong clinical emphasis.

Line 109 – “reaching true MF and incurring the desired adaptations over a training intervention.” Since it is not mandatory to reach MF to achieve desired adaptions, I would soften this sentence and make it more suggestive.

METHODS

Line 122 – Did you conduct a power analysis? Please provide justifications/explanations for the utilized sample size.

Can you please provide more details about the subjects training background? Given that this is a RT study, more information about their RT experience is required.

Line 136 – Given that the descriptions are likely composed of a few sentences, include them in the manuscript rather than referring to reader to other articles.

Lines 142-145- It says that “…building force up to maximal effort over 3 seconds, and then relaxing over a further 3 seconds.” And then that “…and were permitted ~10 seconds recovery between testing angles.” Is it 3 or 10 s of rests between MVCs? This needs to be clarified.

Lines 149-170 –Did the MVC tests at every angle take place on the same day and prior to the single set to failure? Were they conducted every session? How did you select the exact % of MVC given that the presumably the forces differed at each angle? Which angle (or what is the average?) served as the anchor?

Line 151 – “…due to the potential for overtraining when the lumbar extensor muscles are isolated.” The citation provided to justify this rationale does not concern overtraining. It was a reliability study. I find it very difficult to believe that there is a risk of overtraining if participates complete more than a single training session involving a single set a week. Unless direct evidence is available to support this claim remove this sentence.

RESULTS

Table 2 is unclear. First, is the variability presented as SE or SD? This needs to be clarified in all columns. In case the data is presented as SE in the pre-interventions values please change it to SD. Second, please include a post-intervention column to the right of the pre-intervention column with means and SD. Third, it is unclear why the 95%CIs of the differences aren’t enough here? Including both the estimate marginal means (±SE) for changes in each outcome measure, and 95%CIs for the changes is confusing and redundant. I would include the 95%CIs of the within subjects under the means and SD of the pre and post intervention columns and include a separate column for the change score 95%CIs to make the results easier to interpret.

Please prepare a graph of some sort to visually present the individual responses (pre-post changes) for MVCs and SI. Estimation plots would be ideal.

DISCUSSION

Line 202 – I am not sure why this study is introduced and discussed solely in view of rehabilitation whereas the population was healthy. I find this misleading. Anything to do with rehabilitation is speculation and at most should be discussed as a secondary possibility after discussing the results for what they are: training with low and high loads with the ILEX seem to lead to similar strength adaptions among recreationally active subjects over a six week period using only a single set to failure once a week.  Thus, professionals can let their trainees and clients choose the loads as the strength adaptions seem to be similar when using this particular protocol.

Lines 209-219 – This is not accurate as subjects trained the task once a week during the MVCs tests. Thus, and similar to the results reported by Morton, the lack of differences observed between groups may stem from the fact that subjects trained the test with each and every training session. I think that you introduced, rather than controlled for the very confounder you aimed to avoid with the regular MVC testing. This is a considerable confounder of this study and should be discussed as such in the limitation section.

Lines 212-2016 – I am not sure that this sentence adds to your discussion and suggest removing it.

Lines 244-248 – Most studies on central fatigue actually reported that it plays a larger role in submaximal extended efforts. I wonder if this is too speculative to discuss central fatigue here.  Another possible pathway is psychological. It could be that with lighter loads the end point of a set is considerably further away than heavier loads which could influence the perception of difficulty.
In the limitations section I strong suggest you mention the confounder discussed above: the fact the MVCs were tested before each testing sessions allowing subjects to gain experience in how to conduct the test which could have confounded/reduced the real differences between conditions. Furthermore, while you did cite articles showing relationships between ILEX and other, more common exercises that practitioners have access to, I think it is fair to mention the reduced degree of external validity as very few practitioners have access to ILEX and thus the degree of generalizability is reduced.

CONCLUSION

First, as mentioned before, the study was not done on those with low back pain so the discussing should not revolve around clinical populations. Second, while reaching failure is discussed throughout the manuscript as a key and very important variable, studies show that reaching failure is not mandatory to achieve positive and similar strength increases when volume high enough. Thus, to avoid having the readers assume that this is the case, it will be beneficial to touch on this fact in the introduction.

Lines 268-272- Perhaps emphasizes what is unique about this study compared to the others you cited. At present, it is unclear.


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: HEAVIER- AND LIGHTER-LOAD ISOLATED LUMBAR EXTENSION RESISTANCE TRAINING PRODUCE SIMILAR STRENGTH INCREASES, BUT DIFFERENT PERCEPTUAL RESPONSES, IN HEALTHY MALES AND FEMALES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well-written manuscript with good use of language. There are a few points of correction needed in regards to grammar and punctuation. Please see the specific comments.
Experimental design: Clear and sound with only a couple of suggestions as indicated below. The major point of clarification needed is around the statistics for the primary measure. Please see the specific comments.
Validity of the findings: See specific comments for a few issues around limiting conclusions to data presented and clarify the issues with statistics.
Additional comments: Specific comments
50-58 - first sentence is out of place. I would suggest leading with the second sentence and moving the content of the first sentence to later in the paragraph. It doesn’t seem appropriate to lead with motor unit recruitment. The remainder of the paragraph doesn’t flow well. Can this paragraph be re-written to better explain the main point?
60-64 – please explain the RPE anchoring in more detail and define it at this point.
82-84 – while this may be true, there is also a contrary body of literature around pain and strength. I do agree with the rehab implications of your work, but perhaps it could be framed around optimizing rehabilitation approaches, rather than on the relationship between strength/endurance and pain? In addition, I would highlight your group’s previous review (Sports Med, 2016) stating that the lumbar extensors appear to be one of the only muscle groups that would benefit from direct isolation training over and above that that occurs with compound training (at least for strength measures).
113-115 – Poorly worded – If all of the outcome measures can be considered “primary”, they should be stated together with strength. If not, please reword to include primary and secondary outcomes.
126 – reference for the PARQ
136 – as suggested for the introduction, it would benefit readers to have a simple description of the anchoring process here and appropriate references to the scales themselves
178-179 – I would ask the authors to explain their rationale for using the change scores as the DV in the ANCOVA. In general, change scores are quite liberal (even when controlling for baseline measures as you have) compared with using the actual raw values in an ANCOVA. Were the baseline measures between groups significantly different? If so, using the change scores assumes a similar degree of adaptation would occur between groups, which may not be true. Lower strength/endurance levels would likely adapt to a greater degree to a similar stimulus. The other side of this is that the higher baseline scores (if changing similarly) would result in a lower % change than the group with the lower baseline scores. All of these factors lend me to question the validity of this approach for a training study. In my opinion, the more robust method would be to use the actual scores in the ANCOVA (still controlling for baseline). Please consider these points, provide your rationale, and/or adjust your statistics accordingly.
All other statistics appear to be appropriate and presented well.
206 – I’m not sure of the relevance of the phrase “when tested by impartial means”. Can you please clarify the meaning and importance of this?
208 – Please revise “This is hypothesized” to “The similarity of strength increases is hypothesized”
208 – 209 – This is a vague sentence. It is unclear what is being referred to with the addition of the word “respectively” as to HL and LL.
209 – 211 – The reference to “impartial methods” again here is unclear. You’ve emphasized this a few times, but your methods weren’t designed to compare such methods with others. Please temper the language and conclusions around this throughout the manuscript.
212 – 216 – Practically, I don’t disagree with these statements. Having said that, these statements neither seek to explain or interpret your findings of this study, nor are referenced appropriately. Please refocus and revise.
244 – change is to it
244-247 – Please add punctuation to the following sentence as follows: “As such, it appears that when performing HL resistance exercise, cessation occurs as a result of central fatigue; whereas, during LL resistance exercise, peripheral fatigue is responsible for an inability to transmit the impulse across the neuromuscular junction.”
244-247 – Please provide references for each aspect of this sentence. Check to ensure the accuracy of these statements as well, as I don’t believe the literature shows that this is definitive.
260 – comma needed between “mind” and “it”. There are several instances throughout the manuscript where similar such commas are missing.
References – please check for consistency. There are several citations referenced with periods at the end, and several without, for example.
Tables – please provide footnotes for acronyms and abbreviations for each table