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: ASSESSMENT OF THE BACTERIAL COMMUNITY STRUCTURE IN SHALLOW AND DEEP SEDIMENTS OF THE PERDIDO FOLD BELT REGION IN THE GULF OF MEXICO
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript has substantial improvements from the previous versions. However,  there are some considerations still to be fulfilled before acceptance.  First is that raw data allows more reproducibility than the previous review, although the analytical and statistic methodology is still vague. The recommendation is to take a look for the following URL for guidance in the elaboration of a supplementary methods file including the complete methods files:

http://nbviewer.jupyter.org/github/biocore/qiime/blob/1.9.1/examples/ipynb/illumina_overview_tutorial.ipynb

Secondly, some of the observations of the previously reviewed manuscript are discussed in the response letter but not incorporated into the current version manuscript. Specifically:

"How much time left between the sampling, freezing, and DNA extraction? This storage temperature could modify microbial community profiles as microbial metabolism could keep on going at this temperature (Price & Sowers 2004; Panikov et al., 2006). "

Price, P. B., & Sowers, T. (2004). Temperature dependence of metabolic rates for microbial growth, maintenance, and survival. Proceedings of the National Academy of Sciences of the United States of America, 101(13), 4631–6. http://doi.org/10.1073/pnas.0400522101
Panikov, N. S., Flanagan, P. W., Oechel, W. C., Mastepanov, M. A., & Christensen, T. R. (2006). Microbial activity in soils frozen to below −39 °C. Soil Biology and Biochemistry, 38(4), 785–794. http://doi.org/10.1016/J.SOILBIO.2005.07.004

In the current authors' answer, It is like they just nod and then ignore the observations, stating that "microbial communities have evolved to develop the mechanism of cold adaptation" without any supporting reference, It is not even stated that the samples remained for five months at -20ºC.

Please include this into the methods and discuss it, why the authors did not snap-freeze the samples, which is the standard procedure, please take note of the following references as well:

http://journals.plos.org/plosone/article?id=10.1371/journal.pone.0126685
https://www.nature.com/articles/nrmicro3262

Authors answer only states that other studies have done it that way.

Qiime is missing its reference; you are just mentioning the URL.


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: ASSESSMENT OF THE BACTERIAL COMMUNITY STRUCTURE IN SHALLOW AND DEEP SEDIMENTS OF THE PERDIDO FOLD BELT REGION IN THE GULF OF MEXICO
Review round: 2
Reviewer: 2

Output:
Basic reporting: The language used in the manuscript is passable.  There are word choices that are not typical and make some sentences more challenging to read however, this does not significantly affect reader understanding.  I was unable to open the OTU table in the supplemental files.  Perhaps this was an issue on my end but, I usually have no trouble reading .biom files.  Due to this issue, I was not able to access the validity of some of the data presented.
Experimental design: The experimental design and analysis methods were sufficient for the author's objectives.
Validity of the findings: I feel that the taxonomic analysis of the data is a little superficial.  The authors limit themselves to describing the microbial community structure at very broad taxonomic levels.
This causes the authors to make very general and highly speculative statements throughout the discussion which are poorly supported.  I would recommend that the authors take the time to do a detailed assessment of the community at the genus level and highlight those OTUs that appear to be of particular interest.   If necessary, the authors can cross check the taxonomic classification of their OTUs against multiple databases.  This will improve the overall quality of the manuscript and lend more support for some of the claims the authors make related to potential metabolic characteristics.
Additional comments: The manuscript presents a description of the sediment microbial community structure along a transect with varying water column depths. Although the data set is relatively small (11 samples) the is sufficient to begin to address the research question.  Overall, the manuscript is suitable for publication, but I think the authors can do more with the data on hand to improve the quality of the manuscript.

Abstact
L28: change “depth gradient” to “water column depth gradient”.
Introduction
L 59-64:  These statements are not very informative.
L77: change notoriously to notably
Material and Methods:
L149: How long were paired end reads (e.g. 300 bp?)
Data analysis: please provide details about number of reads from the sequencing effort, number of reads that passed QC, etc.  This can be provided in a small supplemental table.
L163: change assignation to assignment
L178: specify package that includes envfit function
Results
L204-205: Are the shallow and deep communities statistically different from one another?
L224-224: provide range of relative abundance for these archaeal groups since they do not show up on your figures.
L230-241:  It would be nice to know what these OTUs actually were at a genus level.  You description and figures lump everything together at a high taxonomic level which make if challenging to draw any significant meaning from this analysis.
Discussion
L246-247: sentence confusion.  I am assuming you are talking about temperature, oxygen concentration, etc as the variables that correlate with water depth, but these are physicochemical properties. Recommend rewording.
L249-251: It is important to note that it looks like your redox values were determined based on a bulk sample of ~4cm.  It is highly likely that the whole sample was not anoxic, but rather that oxygen was quickly depleted after the first few mm to cm as is common in marine sediments.  Unless you have evidence that the bottom waters were hypoxic, this statement needs to be refined.  Also, do your redox profiles show any correlation with TOM or TOC?
L255: define deep sediments.  Are you referring to the water column depth or the sediment depth profile.
L262-264: is your site in an area where water currents and river runoff make it likely to be impacted by terrestrial input ?
L266:  the TOC values that you report are not low but very standard for the GoM (e.g. Escobar-Briones and Garcia-Villalobs 2009).
287-294: see comments relating to lines L249-251. This is not surprising giving the lack of depth resolution in your redox measurement.  Also, several of the groups that you pointed out as being aerobic do have anaerobic members.  Please be cautious about drawing conclusions about metabolic characteristics from such broad taxonomic groupings.
L299: Here you suspect low rates of sediment oxygen consumption but on line 267 you suggest high rates of microbial metabolism.  General high microbial metabolism equates to high oxygen consumption rates…
L300-L303: see comments from L287-294.
L308-310:  There are LOTS of member of the Altermonadales that are neither psychrophilic nor piezophilic.  Do you have evidence that individual OTUs within this family are related to known psychropiezophiles? Again please refrain from making conclusions about physiology and metabolism based on such broad taxonomic groups.
L328: remove strictly. This suggests all member of the Kordiimonadales have these metabolisms which is not demonstrated.


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: CYTOKINE AND MICRORNA LEVELS DURING DIFFERENT PERIODS OF PARADOXICAL SLEEP DEPRIVATION AND SLEEP RECOVERY IN RATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript entitled “Cytokine and microRNA concentrations during different periods of paradoxical sleep deprivation and sleep recovery rats” by Herlinda et. al. has profiled serum cytokines and microRNAs at different length of PSD and after a recovery period. Overall the manuscript is well written with clear background knowledge and discussions of the results. Several previous studies reported either the similar cytokine or microRNA profiles in the PSD animal serum. In this respect, lack of novelty is a major concern of this manuscript. However, this manuscript also focused on the recovery period of PSD with certain extend but not with systemic recovery analysis. Systemic analysis of 192h PSD recovery, for example REM rebound profile and another mid-recovery point analysis, will significantly improve the quality of this study. At the present stage of the manuscript, I suggest considering for publication in PeerJ if a revision address the following concerns.
Experimental design: 1.	What is the status of REM rebound at 20-day PSD animals? Polysomnography of the 192h post PSD recovering animals should help to address this.
2.	I suggest another mid-recovery point analysis of the serum parameters.
3.	Is 20 days enough to reestablished sleep cycle homeostasis? Please explain with proper citations.
4.	Line 260-265; Adiponectin positively regulate IL10 secretion from macrophages (Kumada, 2004). At 96h of PSD there is significant increase in adiponectin but no elevation of IL-10. Do any of these elevated microRNA suppress the early phase (24h, 96h PSD) of IL-10 induction? I suggest performing a met analysis of IL-10 3’UTR for possible microRNA binding, specifically miR-146a/155/223/16. Similarly, for miR-21 binding sites on the 3’UTRs of the serum protein level tested.
Validity of the findings: 5.	I suggest using conclusion of the result as heading of the result sections.
6.	Serum level of IL-6 (Figure1a) is not matching with the data provided in the supplementary file. Please clarify.
7.	The result section should be rewritten with clear rational, experimental design and result of each results.
8.	Please represent serum corticosterone levels as graph instead of table.
9.	I suggest using another independent microRNA reference gene for the serum level microRNA quantification. If the miR-39 was a spike in control, please clearly mention in the materials method section with spiked in copy number.
10.	Please mention concentration unit of the cytokines in the supplementary data file.
Additional comments: I enjoyed reviewing this manuscript. Hopefully the suggestions will help to improve the manuscript.


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: CYTOKINE AND MICRORNA LEVELS DURING DIFFERENT PERIODS OF PARADOXICAL SLEEP DEPRIVATION AND SLEEP RECOVERY IN RATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language should be improved in some places. Beginning with the title, the use of the word “concentration” implies the microRNAs were quantitatively measured, but the data are qRT-PCR. Therefore, a more appropriate word choice would be “levels.” Also within the title, the word “in” should be placed before “rats.”

Conclusion paragraph within the overview (lines 56-60) has several typos and grammatical issues. Final sentence in this section is a bit vague.

More recent citations should be provided in the introduction and discussion. For example, references in lines 76, 78, 93, 255. The introductory background information and contextualization within the discussion should reflect the most recent knowledge.

Line 78, could the authors elaborate on what they mean by “recently-acquired knowledge”?

Within the results, awkward phrasing can be found on line 187 (“major”).

The figure labels (axes and sample IDs) are very tiny and should be increased in size, as well as the significance symbols within the figures.
Experimental design: The inclusion of multiple time points in the study is a strength, as it provides a big picture view of early, late and recovery phases. The methods are very well described.
Validity of the findings: The methods of the study are well-justified by previous literature.

The discussion is very long – it is rather disproportional to the amount of data presented and almost seems to function as a literature review rather than a succinct interpretation of the data. Part of the issue is over speculation about the meaning of the data. Specific areas include lines 249-252, 260-265, 285-289, 297-302, 307-312, 326-333. The authors should condense these discussions or remove them completely.

The final paragraph of the discussion undercuts the rigorous nature of the study the authors have performed. The limitations mentioned should be moved to the methods section where the description of the modified multi-platform method is first presented. The results section should end on line 338.
Additional comments: The study is rigorously performed, well controlled, and the methods are clearly described. The only short coming is the discussion where the main findings are lost amongst over speculation and extraneous literature references.


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: DIFFERENTIAL EXPRESSION OF NF-ΚB HETERODIMER RELA/P50 IN HUMAN UROTHELIAL CARCINOMA
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, this seems like the beginnings of an interesting project identifying P50 and RELA as potential mediators of cancer -specific NFKB signaling in urothelial carcinoma. However, the manuscript is not written in idiomatically correct English, it is disorganized overall, the methods are unclear, and the analysis and statistical statements are often incomplete.

English is uneven. Literature references are satisfactory. Raw data is not shared.

The manuscript needs better organization. For example, the method section for immunohistochemistry does not state controls used for each antibody. In the discussion section, the manuscript explains that staining of macrophages indicates that the two antibodies are working properly. Negative controls are not specified.  Both positive and negative controls should be described in the methods section.

A minor criticism: The introduction is a bit over-broad relative to the findings. Much about bladder cancer course and detection is not relevant to the findings or discussion. It can be shortened.
Experimental design: Although not clearly stated, the investigators appear to have used an online tool to examine differential expression of various proteins in benign urothelium vs. cancer. They identified overexpression of NFKB family proteins in cancer relative to benign. Their thresholds and statistical approach were not specified. The samples used in this online research were not identified. Issues such as false discovery correction were not presented. Degree of over-expression was not specified. It is therefore difficult to evaluate this claim.

The authors then go on to evaluate expression of RELA and P50 proteins in a small tissue microarray. In the text that describes the immunohistochemistry and pathologic evaluation, much of the text was very difficult to follow. As an example, the following sentence was uninterpretable: “Histological findings showed invasive high grade UC with focal squamous differentiation (5 %) 234 and tumor free muscle regions at T1 stage (Fig. 4D).”

There is a sentence in the discussion (Line 331)  “In our study macrophages served as built-in controls of NF-κB heterodimers staining and indicated anti-tumor response suppression by positively staining for p50 as discussed by others (Saccani et al., 2006; Annunziata et al., 2010; Cartwright et al., 2016).” This raises a question, did the authors find that NF-κB heterodimer expressing macrophages were more abundant in cancer than in benign urothelium?

In the discussion, the authors claim that the results have prognostic significance, but this is difficult to assess, as there is no comparison of event-free or overall survival of patients on the basis of RELA or P50 status.
Validity of the findings: Statistical statements in the text are incomplete: As one example, Line 217, “Comparing different grades in UC by Fisher’s exact test revealed significant associations (Table 4).” Which grades are associated with which disease states? Further, there are claims of associations between cancer stage and levels of protein expression, but these associations are not tested for statistical significance.

Further, the biologic context for the work needs improvement, as it never states whether the findings indicate increased or decreased NFKB signaling in urothelial carcinoma, nor its potential association with stage or grade.
Additional comments: Overall, there is some interesting data that needs refinement and further exploration. Once that is done, the manuscript should be edited by a competent professional for completeness, format, and flow.


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: DIFFERENTIAL EXPRESSION OF NF-ΚB HETERODIMER RELA/P50 IN HUMAN UROTHELIAL CARCINOMA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Manuscript fails in the following aspects:
- It has English languaje issues
- The Objective is not clear
- There is no hypothesis

I suggest to use English editing services and state clear objective and hypothesis for the work.
Experimental design: In terms of experimental design, the  manuscript fails in the following aspect.
-There is not a research question properly defined.
-  I recommend to clearly describe how is  Cytoscape app used to predict proteins interaction and how results could be interpreted in conjunction with the immunofluorescence assays.
Validity of the findings: See General Comments to the author section.

Some statements in the discussion section are not validated with the results, but could be written as speculations.  The following is an example:
The cytoplasmic expression of p50 remained significantly extensive across UC tissues similar to RelA subunit which indicated tumor promotion by the heterodimers in the initial stages.
Additional comments: Based on the provided information, although it is not enough clear in the manuscript, the goal of this work was to evaluate if there is a differential expression of NF-KB subunits RelA and p50 which could be associated with the utorthelial carcinoma (UC) and its aggressiveness.

Although the work seems to be interesting and may be relavant due to the critical role of the transcription factor NF-kb in carcinogenesis, i consider that some important issues need to be clearly evaluated and discussed before considering for publication.

1.	Authors may remember that only NF-KB p50 and p52 subunits have the ability to bind DNA but they are not able to activate transcription since they lack the transactivation domain. On the other hand, RelA, RelB and RelC do not have the DNA binding domain, but do have the C-terminus transactivation domain. For this reason,  only heterodimers composed of one of the Rel subunits (A, B or C) plus either p50 or p51 are able to activate gene transcription. On the other hand, p50 homodimers are associated with gene repression because they bind to DNA avoiding heterdimers to bind and promote transcription (Marienfeld R et al., 2003).
Accordingly, I suggest to the authors to thoroughly discuss the meaning of the results from immunostaining and the use of cytoscape app, mainly when authors mention that according with cytoscape analysis, p50 expression was inhibited but RelA target genes were over-expressed.
The same request is for what is said in the discussion section, where authors mention that the heterodimer expression revealed disease aggressiveness being directly proportional to RelA nuclear expression but not 50.
Also, I kindly request authors to explain the mechanism through which the cytoplasmic expression of p50 and RelA could induce tumor promotion as is also mentioned in the discussion section, since to activate gene expression they should translocate the nucleus and form heterodimers.

2.	Other issues in this manuscript include:
a.	In the introduction section I suggest to better justify the study of NF-KB to predict UC status or aggressiveness.
b.	The aim of the study is not clear
c.	In general, the English language should be reviewed to improve the comprehension of your manuscript. The following are some examples where the language may be improved:

Line 60  “Urothelial carcinoma (UC) in industrialized countries is the fifth most common cancer and second most common genitourinary tract cancer. UC is also called as transitional cell carcinoma (TCC) accounts to 5% of all cancers (Schulz 2006) and are the commonest malignancy of the urinary tract with lesser incidence of the upper urinary tract carcinomas “.

Line 105 “UC is not wholly a resultant of gene mutations as inheritance of genes or mutations leading to UC are rare which is confirmed by microarray expression studies”

Line 269. “Our results revealed suppression of NF-κB1/p50, NF-κB2/p52 and RelB in the stage or grade undefined urothelial  tumor tissue presented in PINA4MS app”.

3.	There are several typos along the manuscript. For example:
Line 185: were over expressed of in urothelial cancer cells when compared to normal urothelial cells.


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: DIFFERENTIAL EXPRESSION OF NF-ΚB HETERODIMER RELA/P50 IN HUMAN UROTHELIAL CARCINOMA
Review round: 2
Reviewer: 1

Output:
Basic reporting: Overall improved, although the in silico work is not explained. See section 2.
Experimental design: The manuscript is much improved, but unfortunately does not fulfill the requirements for a mature publication in this field.
The most important problem and the aspect of the paper that is the furthest from taking an acceptable form is the in silico work where no information is given regarding how many patients and samples were analyzed in silico, and what the clinical and pathologic features were for that cohort. Is therefore not possible to review this part of the manuscript for accuracy or for how well the analysis supports conclusions.
Validity of the findings: Beyond the in silico work there is a report  of immunohistochemical analysis of two proteins in the NFKB pathway with little solid data as to whether the results indicate increased or decreased activity of the pathway in disease progression. Overall, the revised manuscript does not provide much clarity on its subject matter and it is difficult to see a path for this information towards clinical utility.
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: BALANCED AND POSITIVELY WORDED PERSONALITY SHORT-FORMS: MINI-IPIP VALIDITY AND CROSS-CULTURAL INVARIANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: I've made a few small suggestions to improve the writing, but it was generally very strong (please refer to general comments).
Experimental design: The procedure section was unclear but can be easily clarified (see general comments).  The design was fairly simple but appropriate given the stated goals.
Validity of the findings: No comment
Additional comments: Overall, I believe this manuscript is likely to make a useful contribution to the study of personality in Spanish proficient / first language samples.  Apart from perhaps the first three, my concerns are largely minor and I suspect could be addressed either with small changes to the manuscript or a persuasive case made to the Associate Editor.  I list these below.

1.	The authors ‘started with’ the Donnellan et al. 20-item measure and translated these items into Spanish to create the mini IPIP.  I see one potential issue with this approach.  It is quite possible that the results that led Donnellan et al. to retain the items that they retained were driven in part by how the items are written and interpreted in English. In other words, items in English could co-vary for reasons that do not apply when those items are translated to Spanish (or, indeed, responded to by people who are from different countries than the original research).  Because the authors did not translate all 50 of the original IPIP items and collect data on all of these, it is impossible to tell from their data whether they have ended up on the best possible short measure.
Having said that, I can see why the authors might be reluctant to revisit the original 50 items; doing so may lead to a slightly different ‘ideal’ set of 20 items, which would then cause difficulty in comparing the new Spanish version of the mini-IPIP to the original English version.   Further, given the cross-cultural invariance results, I also would be surprised, should there be a ‘better’ set of 20 translated items, that this better set would be _that_ much better than the 20 they ended on.  I therefore see this as perhaps an issue worth raising in the discussion but not a ‘deal breaker’ for this study.
2.	The Procedure section of the current manuscript actually does not describe much about the procedure; please provide some more detail.  For example, it isn’t clear until you read the results section what the two different samples actually did (I found myself wondering why the US sample was asked to complete a Spanish personality questionnaire, but it became obvious later that they were not).
3.	I wasn’t clear on what the contribution of the positively worded version of the mini-IPIP provided.  Why would other researchers use that version rather than the traditional version? Both versions appeared to perform well in the latent variable analyses, although I note it’s not easy to compare fit statistics between the two measures since they are not nested models.  My suggestion is to consider removing the positively worded version from the manuscript or perhaps present the analysis of it as a supplement or as a short second paper.
4.	I wasn’t clear on how the validity criterion variables were chosen.  They would seem to be very N and E centric, meaning that they cannot really provide much more than indicative evidence of some of the new mini IPIP scales.  If these were simply convenience measures (i.e., they happened to be available in the data set), then I do still think it is worth presenting the results, however, I feel they should be described as such, and suggestions for a larger variable set be made in the discussion so others can continue the validity exercise.  Further to this point, please make it clear whether the personality scales were those based on the PW version or the ‘traditional’ version of the mini-IPIP (I apologise if it was there but I missed it).
5.	Regarding M2, I was a bit uncomfortable with the description of the decision to allow residuals to correlate being made “a priori” when one of the criteria that were to be fulfilled was that a Modification Index would be large. Unless the criteria for ‘large modification index’ is specified, one could argue that the approach was post hoc rather than a priori.
6.	I liked the idea of testing the RI model, but it appeared that the method factor did not do very much to improve fit (what was the estimated factor loading for the method factor, by the way?).  Given that, I wondered why the authors retained the method factor when conducting the invariance tests.
7.	Please report χ2 and change in χ2 in text for all analyses involving absolute and relative fit.
8.	I’d like to suggest an appendix that allows researchers to download the items in a convenient format.  I appreciate that such an appendix would double up the content of Appendix A, but Appendix A is a bit unwieldy for researchers wishing to copy and paste the items into their survey, and these days, space restrictions are less of a concern.  Further to this, please also provide the precise instructions that the participants received when completing the Spanish mini-IPIP along with the precise response scale that was used.
9.	This may have been a problem with my ability to use the manuscript review system, but I was unable to locate Figure 1.
10.	Some very minor and specific issues, either typographical or for clarity:
a.	I felt the opening sentence was a bit weak; “accounting for a wide range of variables” seemed a bit like a glib ‘throwaway’ line.
b.	I suggest replacing “metric” with “psychometric” except with respect to the discussion on invariance testing (the term “metric invariance” is often used to describe a test where factor loadings are fixed).
c.	On page 5 paragraph 2, I wasn’t clear what ‘the wording effect’ was.  Perhaps a preceding sentence that provides this paragraph with context would assist.  E.g., “Many psychometric scales contain a mix of positively and negatively keyed items because….   But….”.  I don’t expect you to use my sentence of course, but I just provide it to make my point here more concrete!
d.	Please replace “porpoise” with “purpose”.
e.	What did “size fraction of sample 1 after attentional control” mean?
f.	Under measurement models (page 10), please specify which data were fitted to the big five model.
g.	I would argue that the “Cross-cultural invariance” tests/analyses should in fact be referred to as “Cross cultural and language invariance” tests/analyses.
h.	“Explained in a medium-high way” seems a bit awkwardly worded.  Perhaps “explained to a medium to strong extent”
i.	I wasn’t clear on how the last sentence of the first paragraph on page 19 followed from the previous discussion.


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

Input:
Title: BALANCED AND POSITIVELY WORDED PERSONALITY SHORT-FORMS: MINI-IPIP VALIDITY AND CROSS-CULTURAL INVARIANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The basic reporting in this paper is generally clear, but I have a few suggestions for improving it.

p. 5: “Laverdière, Morin, & St-Hilaire (2013) found poor fit with the confirmatory model, requiring the freeing of correlations between three pairs of residuals because of semantic similarity of items belonging to the same facet.... On short scales, the wording effect is even less known.” It is unclear what the authors mean by “semantic similarity” and “wording effect.” I therefore recommend defining these terms.

p. 5: “The reasons why the creation of negative wording items was usually justified (e.g., avoiding acquiescence) are no longer so clear (Arias & Arias, 2017).” I am not convinced that this statement is supported by the psychometric literature. For example, there is considerable evidence that uncontrolled individual differences in acquiescent responding can bias the observed structure of an item set (e.g., Rammstedt & Farmer, 2013, Psych Assessment; Soto, John, Gosling, & Potter, 2008, JPSP), and can also bias trait-criterion validity associations (Danner, Aichholzer, & Rammstedt, 2015, JRP; Soto & John, in press, Psych Assessment). This is because scales with an imbalance of positively and negatively keyed items confound individual differences in the psychological trait being assessed with individual differences in acquiescent responding. These biases tend to be especially problematic among samples with low levels of formal education, including children and adolescents (Rammstedt & Farmer, 2013; Soto et al., 2008). In the present research, the Mini-IPIP-PW only includes items keyed in the socially desirable direction for each of the Big Five traits. It therefore perfectly confounds substantive trait variance with both acquiescence and social desirability. This strikes me as an important limitation.

To address this issue, I recommend (a) adding a couple paragraphs to the Introduction to summarize objections to scales that include only positively keyed (or only negatively keyed) items, and to respond to these objections, (b) adding a paragraph to the Discussion to acknowledge and discuss the confounding of trait variance with acquiescence variance and social desirability as a limitation of the Mini-IPIP-PW, and (c) expanding the Limitations subsection to acknowledge that the Mini-IPIP-PW may be less appropriate for younger and less well educated samples, due to the possibility of more-pronounced individual differences in acquiescent responding. (I certainly acknowledge that negatively keyed items can have their own limitations and complexities, and the authors are of course welcome to discuss these as well.)

pp. 7, 9, 10: The writing is generally clear, but the authors repeatedly refer to “porpoises” when I believe they mean “purposes.” I recommend editing these sentences.
Experimental design: The research design and analyses are generally well conducted and reported. As the authors acknowledge, the most important limitation is the small number of validity criteria (p. 19). Beyond this, I only have one suggestion for improvement.

Tables 2, 3: The authors report factor loadings, discriminant correlations, and criterion correlations for the Mini-IPIP but not the Mini-IPIP-PW. I recommend adding the Mini-IPIP-PW results to Tables 2 and 3.
Validity of the findings: The interpretation of findings is generally appropriate, but I do have one important suggestion for improvement.

pp. 13, 15, 17: The authors clearly state their criteria for evaluating model fit and measurement invariance (p. 13, lines 315-320). However, they do not apply these criteria consistently when interpreting the present results. Specifically, they conclude that the Mini-IPIP and Mini-IPIP-PW show strong and strict measurement invariance, despite fit statistics below the stated thresholds, as well as non-trivial changes in fit compared with the configural invariance models (pp. 15, 17). To address this inconsistency, I recommend revising either the criteria or the conclusions so that they match with each other.
Additional comments: The Spanish-language Mini-IPIP and Mini-IPIP-PW appear to be reasonably reliable, structurally valid, and brief measures of the Big Five. As noted above, I do have some important recommendations for improving the paper, but on balance I think these measures can be useful tools for personality assessment.


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: BALANCED AND POSITIVELY WORDED PERSONALITY SHORT-FORMS: MINI-IPIP VALIDITY AND CROSS-CULTURAL INVARIANCE
Review round: 2
Reviewer: 1

Output:
Basic reporting: Please see general comments
Experimental design: Please see general comments
Validity of the findings: Please see general comments
Additional comments: Overall I am satisfied by the changes to the manuscript. Several issues remain but these are easily fixed:
1. Please report degrees of freedom for the change in chi-square tests
2. Please give the manuscript a proof-read.  There were two deleted track-changes (a priori) that remained, and line 367 I believe needed commas added in between the statistics in parentheses). line 458: is probably best not to start a section with "However, it..."   Maybe replace with "Several limitations of this study should be acknowledged" or something similar.
3. Figure 1 didn't seem like a CFA model. Rather, it appears to be a SEM as the single headed arrows imply regression of (1) LS on PA, O, C, and NA, (2) NA on N, and (3) PA on E.  My understanding of CFA models is that they are models of correlated factors.  In any case I don't beleive that SEM is necessary to provide evidence of convergent validity of the new B5 scale.
4. Please add all inter-factor correlations to Table 2 as there is no reason to suppress those and they may be helpful for future analyses (e.g., comparing results of this study to that of future studies using the same measure). I understand that supressing small factor loadings makes FA tables easier to interpret.


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: BALANCED AND POSITIVELY WORDED PERSONALITY SHORT-FORMS: MINI-IPIP VALIDITY AND CROSS-CULTURAL INVARIANCE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have adequately addressed my concerns regarding basic reporting, except for one. Here was my original comment:

***

p. 5: “The reasons why the creation of negative wording items was usually justified (e.g., avoiding acquiescence) are no longer so clear (Arias & Arias, 2017).” I am not convinced that this statement is supported by the psychometric literature. For example, there is considerable evidence that uncontrolled individual differences in acquiescent responding can bias the observed structure of an item set (e.g., Rammstedt & Farmer, 2013, Psych Assessment; Soto, John, Gosling, & Potter, 2008, JPSP), and can also bias trait-criterion validity associations (Danner, Aichholzer, & Rammstedt, 2015, JRP; Soto & John, in press, Psych Assessment). This is because scales with an imbalance of positively and negatively keyed items confound individual differences in the psychological trait being assessed with individual differences in acquiescent responding. These biases tend to be especially problematic among samples with low levels of formal education, including children and adolescents (Rammstedt & Farmer, 2013; Soto et al., 2008). In the present research, the Mini-IPIP-PW only includes items keyed in the socially desirable direction for each of the Big Five traits. It therefore perfectly confounds substantive trait variance with both acquiescence and social desirability. This strikes me as an important limitation.

To address this issue, I recommend (a) adding a couple paragraphs to the Introduction to summarize objections to scales that include only positively keyed (or only negatively keyed) items, and to respond to these objections, (b) adding a paragraph to the Discussion to acknowledge and discuss the confounding of trait variance with acquiescence variance and social desirability as a limitation of the Mini-IPIP-PW, and (c) expanding the Limitations subsection to acknowledge that the Mini-IPIP-PW may be less appropriate for younger and less well educated samples, due to the possibility of more-pronounced individual differences in acquiescent responding. (I certainly acknowledge that negatively keyed items can have their own limitations and complexities, and the authors are of course welcome to discuss these as well.)

***

In response, the revised manuscript includes a brief discussion of how a mix of positively and negatively worded items can introduce the need for a method factor (p. 5), as well as a brief acknowledgement that the Mini-IPIP-PW may be less appropriate for non-university participants (p. 21). However, I continue to believe that the paper would benefit from a more thorough discussion of balanced vs. imbalanced item keying. In particular, I suggest adding a paragraph about the limitations of positively-worded-only (or negatively-worded-only) scales to the Introduction (p. 5): Fully imbalanced scales perfectly confound substantive personality variance with acquiescent response style. It is therefore impossible to determine whether a high score (or low score) on the scale is due to the respondent’s (a) true standing on the trait being measured, or (b) tendency to consistently agree (or disagree) with items regardless of their content (i.e., acquiescence). This is a long-standing issue in the psychometric literature that is relevant to the Mini-IPIP and Mini-IPIP-PW, and it deserves additional consideration in this manuscript. Readers choosing between the Mini-IPIP and Mini-IPIP-PW should be made aware of the psychometric advantages and disadvantages of each version.
Experimental design: The authors have adequately addressed all of my concerns regarding experimental design.
Validity of the findings: In my original review, I noted that the manuscript’s conclusions regarding measurement invariance did not match the stated criteria regarding tests for measurement invariance. That continues to be the case in the revised manuscript. Specifically, the authors conclude that the Mini-IPIP obtained strong invariance but not strict invariance (p. 16). However, the fit statistics for strong invariance and strict invariance are quite similar to each other, and neither meets the stated criteria for testing invariance (p. 14). In particular, both the Mini-IPIP and Mini-IPIP-PW show substantial decreases in CFI (delta > .035) and TLI (delta > .022) for both strong and strict invariance.

To address this issue, I recommend further revisions to bring the conclusions regarding measurement invariance into alignment with the stated criteria.
Additional comments: This revised manuscript has thoughtfully addressed some, but not all, of my concerns with the original manuscript. I therefore recommend further revisions before accepting the paper 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: MOLECULAR TYPING AND PROFILING OF TOPOISOMERASE MUTATIONS CAUSING RESISTANCE TO CIPROFLOXACIN AND LEVOFLOXACIN IN ELIZABETHKINGIA SPECIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Comments for the author:

This is an interesting study done by Shang and coworkers. Authors have done extensive work to understand the resistance in Elizabethkingia spp against ciprofloxacin and levofloxacin drugs. 131 Elizabethkingia spp isolates were used in this study. Authors have done extensive molecular biology, microbiology to identify the bacterial strains, mutations, and calculated the MIC values. They have also found that most of the mutations are detected in GyrA gene which is responsible for the drug resistance. The conclusions of the study are well stated and linked to the original research question. This study will be highly appreciated by mechanistic researcher who are trying to understand the drug resistance mechanism in Elizabethkingia spp against ciprofloxacin and levofloxacin. The study has been carried out with great care and caution, however, two small issues demand attention by the authors.

1. The last word of the title of the paper should be “species”

2. The font size of the Figure labels is small. Please increase the font size for the better visibility.

Clear and unambiguous; and professional English used throughout in the manuscript. I would recommend this important piece of work for the publication in PeerJ, after raised issues are taken care.


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: MOLECULAR TYPING AND PROFILING OF TOPOISOMERASE MUTATIONS CAUSING RESISTANCE TO CIPROFLOXACIN AND LEVOFLOXACIN IN ELIZABETHKINGIA SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The article entitled "Molecular typing and profiling of topoisomerase mutations causing resistance to ciprofloxacin and levofloxacin in Elizabethkingia species", determined fluoroquinolone susceptibility profiles of clinical Elizabethkingi. These results provide information for further research on the variations of the resistance mechanism and potential clinical guidance for infection management. I recommend it for publication in PeerJ, but there are some parts to be improved and revised before acceptance:

>The quality of Fig1 is poor, please update this figure so that the readers can clearly understand it.

>Please label any significance analysis’s value on the figure(s).

>All figure’s legend must be described in detail.

>Fig2 (A, B, C) must be merged into one page.

>Fig3 (A, B, C) must be merged into one page.

>The authors should give the corresponding information about use of the sequences and how to construct the phylogenetic tree in Fig3.


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: MOLECULAR TYPING AND PROFILING OF TOPOISOMERASE MUTATIONS CAUSING RESISTANCE TO CIPROFLOXACIN AND LEVOFLOXACIN IN ELIZABETHKINGIA SPECIES
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 revision authors have made. It is an excellent paper and worthy of publication in PeerJ.


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

Input:
Title: MOLECULAR TYPING AND PROFILING OF TOPOISOMERASE MUTATIONS CAUSING RESISTANCE TO CIPROFLOXACIN AND LEVOFLOXACIN IN ELIZABETHKINGIA SPECIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The revised MS is OK for publication in PeerJ.


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

Input:
Title: EXPLANATION OF OBSERVATIONAL DATA ENGENDERS A CAUSAL BELIEF ABOUT SMOKING AND CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: Thank you for the opportunity to review this manuscript. I had the opportunity to previously review this manuscript for another journal and the authors have addressed nearly all of my previously stated concerns. I summarise how these have been addressed and note a few minor outstanding comments.

The authors highlight the problem that the results of observational studies are frequently reported using causal language in the literature and media. They conduct a randomized controlled trial in the context of a massive online open course on data analysis to test the hypothesis that explaining an inferential analysis will cause readers to interpret the result as causal. The authors have made a strong case for why “it may be dangerous to explain” observational results. The nature of the “danger” is clearly articulated, and supported by salient examples.

A strength of this experiment is that it was replicated in the context of a second offering of the online course and the results were consistent. The manuscript is well-written and clear for a generalist audience, though I found that the Tables (particularly the titles), could be further streamlined/pared down to avoid repetition with the text.

The first example in the first sentence of the main text (“Facebook could raise your risk of cancer”) does not suggest a causal relationship to me as it uses the word “could” and “risk” where the other two are excellent examples. Could you replace the first with a stronger example?

The authors retrospectively sought and were granted IRB approval for their experiment. Since consent was not obtained prospectively, it might be important to note on what grounds a waiver of informed consent was granted. I would also be interested to know the relationship between the study authors and the course (e.g. were they instructors? Course designers?) and whether they had access to participants’ identities.
Experimental design: This is a novel experiment that provides a strong level of evidence to understand the impact of explanatory statements on readers' interpretation of inferential results.

Since the primary outcome was measured using only a single quiz question, the authors have appropriately highlighted the limitations of the study design in terms of measurement, the context in which results can be interpreted and suggested future research that would strengthen the causal claim that explanation accompanying an inferential result prompts causal interpretation.

The authors have helpfully provided some information about the sample enrolled in the MOOC, which will aid in generalizing these results. However, why was the course enrollment/sample size so much smaller in the replication (October 2013 results)? That said, the authors have adequately justified why the smaller replication sample is unlikely to bias the replication results.
Validity of the findings: The results are robust, statistically sound and the design is of low risk of bias.

The authors have  provided a useful discussion of the role of explanation and interpretation in scientific writing and suggested future work that would reduce bias in reporting.
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: EXPLANATION OF OBSERVATIONAL DATA ENGENDERS A CAUSAL BELIEF ABOUT SMOKING AND CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well-written. I only miss some points and discussion (see below)
Experimental design: Investigating the impact of reporting a (substantive) explanation of an association found seems to be closely related to Bradford Hill's considerations of "plausibility" and "coherence". Maybe, the explanation for the effect described by the authors is that researchers use this heuristics. The authors might want to comment on when this really increased the probability that the causal conclusion is valid*.

*
Höfler M. The Bradford Hill considerations on causality: a counterfactual perspective. Emerging Themes in Epidemiology 2005; 2:11

Similarly as the authors, I suspect that most of the study participants yet take the example of the association between smoking and cancer as a study with a causal aim - because this has been debated for many decades, and it has been obvious for long that there truly exists a (strong) causal effect. However, the experiment is valid anyway because it is randomized, wherefore difference in outcomes can be attributed to the different further information provided. Surprisingly for me, the base rate is surprisingly low for this example. The low base rate, on the other hand, indicates validity. But I don't understand why the authors assume a smaller effect in a larger study (discussion).
Validity of the findings: I would not use the term "prove" because, strictly speaking, a causal effect can never be fully proven.

A description of the student sample is required (beyond the short discussion part on this). At least this has to provide basic socio-demographical information. Ideally, the study has collected any variables assumed to modify the effect under consideration. Then their distribution in the sample inform on possible direction and amiunt of selection bias when inferring on whatever target population (remains unclear here).

Besides, the authors need to report which statistical methods they have used.
Additional comments: I consider experimental studies on the impact of reporting study results on the correctness of conclusions very promising (personally, I also consider doing experiments on that). This is because it has been found that using better statistical methods and reporting (confidence intervals, even Bayesian bias models) does not solve the basic cognitive problems*.

Especially, when a causal conclusion is done or subtly suggested, it remains often unclear on which assumptions this is based - leaving the reader unable to decide whether to follow the logical path of argumentation and, thus, a conclusion or not. Instead, I (also) suspect, the decision is based on hidden heuristics. Accordingly, this experiment investigates a mechanism that is not pretty obvious but might be relevant: whether a substantive explanation is suggested.

*
Greenland S. Invited Commentary: The Need for Cognitive Science in Methodology. Am J Epidemiol. 2017186(6):639-645

**
Höfler M, Venz J, Trautmann S, Miller R.. Writing a discussion section: how to integrate substantive and statistical expertise. BMC Med Res Methodol. 2018 Apr 17;18:34.


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: EXPLANATION OF OBSERVATIONAL DATA ENGENDERS A CAUSAL BELIEF ABOUT SMOKING AND CANCER
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is well written and is easy to follow. The authors’ hypothesis is clearly defined. The analyses and results are easy to understand and interpret.

1) line 18: “includes explanation” should be “includes an explanation”

2) (very minor): in analysis_FINAL.Rmd, line 269 says “causal” but it should be “inferential”
Experimental design: The authors test the hypothesis that providing a causal explanation for an observational study makes it more likely that readers will believe a “causal analysis” was used for the study. After describing an observational study where smoking is associated with lung cancer, participants were asked to choose which type of analysis was used for the study. Four of five types of analysis were given as choices (inferential, descriptive, predictive, mechanistic, and causal) in a multiple-choice format.

3) It’s not clear why the authors didn’t present all five choices to each participant. I made the assumption that this was a technical limitation with the online course that students were participating in, but the reasoning for this should be made explicit. Because of this design, the authors had to repeat the same analysis four times, and only one analysis was presented in the manuscript (the rest are in the supplementary material).
Validity of the findings: The authors find that when given a causal explanation for the results, participants are much more likely to select “causal analysis” and less likely to select “inferential analysis.” I have major concerns about whether these results would extrapolate to other analyses and explanations.

4) My biggest concern is that the explanation given to participants is true: smoking does cause lung cancer. I suspect this has a large influence on participant’s belief about the study’s design. The authors allude to this in the Conclusions and call this an example of the availability heuristic, though I believe it is better explained by belief bias.

5) The authors state that researchers often include “hypothesized mechanistic explanations,” but the link between smoking and cancer is not presented as a hypothetical explanation. It is presented as a true fact: they say “cigarette smoke contains known carcinogens,” which is tantamount to saying “cigarettes are known to cause cancer.” This is exactly what the observational study is supposedly testing.

6) Participants are asked to identify “the type of analysis for this results.” Is it clear to participants that the explanation is not part of “the analysis”? To non-scientists, the distinction may not be clear; we often use the word “analyze” in common vernacular to mean “explain” (e.g., “analyze the situation”). If participants consider the explanation part of the analysis, they are not wrong for judging it to be causal. The experimental design should make this clear, e.g., by clearly labeling “ANALYSIS” and “EXPLANATION OF THE ANALYSIS”.
Additional comments: 7) The authors test their hypothesis using only a single example (smoking and cancer). This is not sufficient evidence to support their broader hypothesis. The authors need to expand their materials and present many more examples/explanations that vary in different ways.

8) No mechanism is hypothesized for why participants draw an erroneous conclusion. Would the same results be observed if the explanation provided were non-causal? What if the explanation were presented as conjecture, and not fact? Is this inference affected by participants’ prior beliefs? Does it hold only in biological domains, or would it work for social science (psychology/economics) explanations as well? The authors need to diversify their materials and test a range of possible scenarios to determine where and why this effect occurs.

9) The authors fail to report statistical tests throughout the manuscript, though their R code (supplementary material) shows they performed these analyses (chi-square tests). These should be presented whenever comparisons are made in the manuscript.

10) The authors provide a definition of “causal analysis”, as well as other types of analysis. I don’t have any major qualms with the definition, but exact definitions of causality are debated in the psychological and philosophical literature. Would you expect the same results if participants were instead given examples of each type of data analysis? If the results differ, this might suggest that participants are more likely to believe the study is causal in part because they don’t understand what a causal analysis is (as opposed to mis-understanding the experimental design).

11) In the abstract, the authors say that their “results suggest that […] qualification of explanations could be a useful avenue of exploration to counteract the problem.” This is never actually tested.

I think the authors have an interesting and reliable effect in their data, and their research question is broadly worth pursuing. It should be explored more fully with additional studies.


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

Input:
Title: EXPLANATION OF OBSERVATIONAL DATA ENGENDERS A CAUSAL BELIEF ABOUT SMOKING AND CANCER
Review round: 2
Reviewer: 1

Output:
Basic reporting: None
Experimental design: None
Validity of the findings: None
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: EXPLANATION OF OBSERVATIONAL DATA ENGENDERS A CAUSAL BELIEF ABOUT SMOKING AND CANCER
Review round: 2
Reviewer: 2

Output:
Basic reporting: (minor) Sloman & Rabb citation is listed twice in the references
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I thank the authors for considering my suggestions and those of other reviews. In particular, I appreciate the inclusion of statistical comparisons, the expanded discussion on the definition of causality, and a more nuanced discussion of the particular smoking example used.

However, I still believe that the singular “smoking” example used in the experiment is not sufficient to test the broader hypothesis that the authors contend (that “explaining an analysis will lead readers to interpret an inferential analysis as causal.”) To be clear, I agree with the authors that this specific example provides some evidence for that hypothesis (though limited), and I would like to see this manuscript published with additional stimuli that support this claim.

I am worried that what the Action Editor calls a “conversation starter” will actually be a “conversation ender.” Other researchers who take the time to test multiple stimuli more thoroughly may have their manuscript rejected on the grounds that the effect is no longer novel. If the authors plan on testing additional stimuli themselves, then why not include them in this manuscript?

The authors addressed four of my points at least partially in the rebuttal letter by a call for “future” research to resolve these issues. I agree, most of the issues I raised require additional studies. I should have been more clear in my initial review that I was suggesting the authors conduct an additional study to address some of these concerns. I realize it is common practice to assuage minor methodological disagreements through a padded discussion of the limitations of the current experiments. In this case, I don’t believe such discussion is sufficient.

If this manuscript is to be to published without additional studies, I would highly recommend making it very clear that the broader hypothesis was tested in a very limited scope, in both the abstract and the manuscript title (e.g., “Explanation of observational data engenders a causal belief that smoking and cancer”). Presently, the abstract does not mention that the hypothesis is tested with a single “smoking” example, which could give the false impression that the authors used a diverse set of stimuli (particularly because they conducted two massive experiments). I realize that this conveys a much more limited finding, but given that the effect has not yet been generalized beyond this singular example, I think it is warranted.


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

Input:
Title: A CLOSE RELATIVE OF THE AMAZON RIVER DOLPHIN IN MARINE DEPOSITS: A NEW INIIDAE FROM THE LATE MIOCENE OF ANGOLA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Lambert et al. provide a valuable contribution with a description of a new genus and species of imiid from Miocene marine rocks of coastal Angola. The fossil record of Iniidae (a group solely represented by the extant Amazon River dolphin, Inia geoffrensis) consists of a variety of fossil forms recovered from both within and outside of the Amazon Basin. In some cases, extinct relatives more closely related to Inia than any other odontocete (living or fossil) have been recovered well outside Amazonia, including North and Central America. In this way, the discovery of an Inia relative from Africa is important: its phylogenetic relationship, geographic, and geological provenance all bear on the origins and evolution of Inia’s broader group.

The manuscript is well written. The introduction is fine, and the manuscript is characteristically crisp and strong in its descriptive sections — there are no real issues there. I think a Specimens Observed section is warranted, especially given the mention of an Inia study sample — it’s also useful for specialists to know what the authors saw, especially firsthand versus via literature or shared imagery among colleagues. It’s one thing to pick this up or infer it from the Acknowledgments; it’s better to see it early on in the manuscript. Also, I am not particularly a fan of bullet item conclusion sections — is it really that hard to write it as a paragraph? In some cases, I am not convinced the perfunctory nature of a conclusion section is warranted, but I think it is fine to have one here.
Experimental design: The manuscript is weakest both content-wise and analytically with its phylogenetic analysis. The authors do not report any sub-clade support values (Bremer nor bootstrap), so there is really no basis for knowing about how well each sub-clade is supported. I think this is a real issue with this manuscript because there is a lack of stability in so-called “family Iniidae” sub-clades. The authors completely side-step any of the issues raised in Pyenson et al. (2015, PeerJ) about Cozzuol’s Ischyrorhynchinae, nor any mention of Saurocetes spp., and only one mention of Goniodelphis. Yes, Pyenson et al. (2015) used a different matrix for their analysis of Isthminia, but I would really like to see the authors make some effort to discuss the different topologies and memberships of sub-clades within Iniidae and Inioidea from previous work. It wouldn’t take much, and the recovery of a monophyletic Pontoporiidae, along with a different composition to a stem-based Iniidae, is valuable to specialists. A paragraph of comparative systematics would greatly enhance the utility of this paper, beyond a mere description of a new fossil Inia relative.

The biggest issue with the phylogenetic analysis is the decision to exclude Isthminia panamensis from the character taxon matrix and phylogenetic analysis. Why? This taxon was published in 2015, in PeerJ, with a full description; 3D models and CT datasets were released publicly with the paper. It is completely available for coding and integration. The authors spend a fair amount of space in the comparative morphological sections with Isthminia, along with Brujadelphis — the latter being a taxon published in 2017, a seeming sister taxon to Isthminia, although it is impossible to know because Isthminia wasn’t included in the phylogenetic analysis of that paper either. Unless it is explicitly stated, I don’t see a reason for excluding Isthminia from an all-inioid phylogenetic analysis and urge the authors to include it as a part of their analysis in their revisions. It would really help move things forward, rather than leaving that integration as an outstanding problem.
Validity of the findings: The manuscript does a good job in its end sections of identifying the significance of a putative Inia sister taxon from the late Miocene of Africa, but if we don’t know the relationships among Isthminia, Brujadelphis, Ischyrorhynchus and Kwanzacetus, then there really is no point in presenting any potential evolutionary hypothesis for how Iniidae evolved. Overall, I find the manuscript generally well worth publishing in PeerJ, but hope that the authors can address outstanding concerns (identified above) in their revisions.
Additional comments: Some detailed comments:

- l. 21, “Thanks” is not really the appropriate word here; it implies that freshwater invasions in odontocete history happened _because_ they could echolocate, when in reality we don’t know why these invasions happened. There are potentially many, unrelated reasons (or common ones). In essence, the sentence joins potentially unrelated ideas. I suggest stripping echolocation from the argument.

- l. 59, It’s not exactly clear to me that a broad geographic range equals evolutionary success, specifically in the case of Inia versus Lipotes or Platanista. In other words, it’s a bit arbitrary to focus on geographic range instead of say, stratigraphic duration, or molecular divergence time. Tying success to any of these factors is an arbitrary decision.

- ll. 69-71, Again connecting two ideas that are not necessarily related: vertex morphology and ecological transitions — why are these linked? Yes, I understand that the vertex of Ischyrorhynchus is very similar to Inia’s — so what? What does that particular complex mean for the timing or mode of fresh-marine transitions? I suggest editing for clarity.

- l. 81, Materials and Methods section could use a Specimens Observed section.

- ll. 118-119, I presume X and Y are lat/lon coordinates; please harmonize for consistency with geographic reporting standards by providing cardinal directions for each value.

- l. 122, “south” should not be capitalized here.

- l. 143, “supposed” is not correct, either delete or replace with “likely”

- l. 151, “evocated” is not the correct verb here; substitute “described”

-  ll. 163-164, There are no rules (and PeerJ enforces none), but it is confusing to list a ranked taxonomic hierarchy with intercalated with clades names — this is why, for instance, some authors describing new taxa choose to harmonize by listing only clade names (either stem- or node-based ones, following phylogenetic taxonomy). The authors clearly get the meaning of the clade names, but the lack of rank poses a problem that is not easily solved. For intellectual consistency, I strongly advocate either deleting these two clade names, or completely de-ranking all taxonomic names. Opting for a middle ground really makes no sense. See Joyce et al. 2004 J Paleo for more; and Pyenson et al. 2015 PeerJ for the issues with imposing higher taxonomic names on monospecific ranks, such Iniidae (directly relevant to this manuscript). This latter problem is exactly why Pyenson et al. (2015) did not assign Isthminia to family Iniidae and instead used a pan stem definition of Inia that defined the clade in a stable way that could accommodate future discoveries, such as this one (see l. 192)

- l. 182, again X and Y coordinates are not standard reporting, please control and identify the relevance of “GPS Bc65”

- l. 185, italicize the ichnogenus Ophiomorpha

- l. 188, it would perhaps be worth the authors’ time to explain a bit more about Douglas Adams’ relevance or connection to cetaceans, especially a fossil one from Angola — in general, don’t assume too  much about a reader’s background unless the intent is to vague and cheeky (and, in which case, recognize that can bother some readers).

- l. 190, hopefully the Table with measurements will be inserted prior to this point in the manuscript, but the author assert a large size without quantification or comparison. I’m not sure it’s relevant in the differential diagnosis.

- l. 192, a nuance: Pyenson et al. (2015) did not assign Isthminia to a ranked family Iniidae — that is a classification interpretation of the authors, using a Linnaean hierarchy.

- l. 199, if mentioning a study sample of Inia, please list Specimens Observed (see also l. 407).

- l. 209, “heel” is an unusual descriptive word for dental anatomy; suggest lingual cusp or keel or enlargement — although the more I consider it, it is actually apt for the morphology of posterior cheek teeth in Inia.

- l. 251, typically reported as “2.50 m”

- l. 274, typo, premaxilla (right?)

- ll. 472-473, suggest a hyphen for post-tympanic; no hyphen between adverb and subsequent verb “posterolaterally facing”

- l. 537, please list the taxa removed from Post et al. (2017)’s matrix instead of forcing the reader to make the comparison.

- ll. 541-556 and also ll. 582-584, the authors provide no support values for sub-clades, and thus it is impossible to evaluate any statements about support for relationships among key taxa in their phylogenetic analysis. I urge the authors to report Bremer decay index or bootstrap values in their revision.

- ll. 570, can you clarify what’s meant by “part of the inioids”? Or spell out which ones? Recommend avoiding single sentence paragraphs and recommend stitching this sentence to the subsequent paragraph.

- ll. 587-589, the statement that a single new genus and species confirms the late Miocene as the heyday of Inioidea is unsupported. I tend to agree in broad outlines (e.g., see the stratigraphically calibrated inioid tree Fig. 15 in Pyenson et al. [2015, PeerJ]), but it’s not a statement evinced by any data in this manuscript — can the authors offer any? Perhaps a tally of taxonomic richness through time for Inioidea? Or a count of range-throughs for the Tortonian from Fig. 15 in the Isthminia paper?  But really, the statement has no teeth lacking comparative data — heyday for Inioidea…so what? Compared to what other groups? Aren’t all odontocetes (and cetaceans) experiencing a richness peak at this marine stage? I suggest moving this sentence to a way more appropriate place around l. 623

- l. 597, “ecological/functional anatomy” is conjoining terms that are not really the same thing. I understand the authors are trying to draw functional interpretations from a suite of morphological characters, but painting ecological categories and “functional anatomy” as the same thing is not really constructive or intellectually vigorous. Please be explicit about diction — ecology is not really easily inferred by ecomorphology alone (if that’s what’s meant here).

- l. 644, Generally, I am not impressed with bullet item Conclusions — to be frank, I find it lazy. Each sentence could just as easily be constructed as part of a paragraph,

- l. 692, please capitalize Etienne Steurbaut’s surname.

Fig. 2 caption, italicize Ophiomorpha.

Fig. 3 caption, italicize Ophiomorpha.

Fig. 7 caption, typo on “cranium”


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

Input:
Title: A CLOSE RELATIVE OF THE AMAZON RIVER DOLPHIN IN MARINE DEPOSITS: A NEW INIIDAE FROM THE LATE MIOCENE OF ANGOLA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general, the article is well written and based on current and pertinent literature. It describes a very interesting new iniid dolphin from Angola, which greatly improves our understanding of the evolution of the group.

Nevertheless, I do have some minor suggestions and questions about some terms (I am no expert on English grammar myself) to be checked for the authors (see annotated pdf, please). Also, the figures and tables are well prepared in a general manner. But as it is a description of a new species and figures need to be as clear as possible, I think they could be improved in some punctual aspects:

1) Figures 5, 7, 8 and 9 have a bit much of uneven illumination. Of course, light shadows are very important for correct interpretation of the morphology but in these images, the contrast between very bright and very dark portions are misleading and prevent observation of all structures. I recommend trying to compensate it in trough photo edition but if it cannot be accomplished please considered taking new photographs with less intense illumination in different positions.

2) there are some structures mentioned in the text that are not indicated in the figures. For example, the orbitosphenoid is not indicated in figure 8 as promised in the text. Please double check for all structures.

3) Figure 3 is very helpful, but as it comprises a lot of information it would be more intuitive to understand if the numbers of parts A and B were also indicated on part C of the figure, not relying only on color to make its correspondence. In the same way the red color of the contact on "part C" would be helpfully also noted in "part B". Also please provide the captions for all structures annotated on the sedimentary column (part C) and indicate what means the letter T on part B of the figure (is it the fossil recovering position?).
Experimental design: It is a well designed descriptive and phylogenetic tested paper. My only comment on this respect is about the comparisons with extant Inia, which is very necessary but could be improved if the authors considered the variation of shapes and structures between different specimens of the species (I. geoffrensis, in this case), especially regarding different ontogenetic stages. The specimen that is figured (fig. 10) is probably a subadult, older specimens can show much more developed structures that in some cases would significate closer similarities (ex. thick nuchal crest) and in other cases fewer similarities (ex. frontal boss development and shape of the ascending process of the maxilla).

This is even reinforced for the large size of the specimens and very well closed and fused sutures in the new species which contrasts with the open sutures of the maxilla and frontal (laterally) of the Inia specimen. Also, for future studies and comparisons, it is needed to add a catalog number to the specimen of Inia mentioned and figured.
Validity of the findings: no comments
Additional comments: Please see attached pdf for further suggestions on your very nice work!


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

Input:
Title: A CLOSE RELATIVE OF THE AMAZON RIVER DOLPHIN IN MARINE DEPOSITS: A NEW INIIDAE FROM THE LATE MIOCENE OF ANGOLA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The specimen is a relatively well-preserved skull of an odontocete that certainly has some Inioid affinities. Description and comparison may be improved and a broader taxonomic comparison background may help.
Despite the mention of parts of the anterior limbs, they were not described, which is relevant because some of the most interesting features of Iniidae are in that region.
My main concern with the manuscript regards the phylogenetic analysis. The size and complexity of the data matrix prevent detailed revision for the journal review time, however, it has several problems that the authors tried to "fix" using a molecular constrained tree, that, unfortunately, does not help much for clarifying the position of the new species here described.
Experimental design: No comment
Validity of the findings: The new species seems to have inioid affinities, but more extensive comparisons should be made.
The phylogenetic analysis is problematic. The matrix used is too large to allow a proper review for the time the journal needs but after running it, it was clear that it has serious problems of character coding. It seems the authors are aware of that because they try to "fix" that with a molecular constrained tree. Despite this may help to resolve the major arrangement of the tree, it certainly does not help for the interrelationships of the smaller groups of the tree, especially when most of the group is extinct, as is the case of the Inioidea.
The use of problematic matrices may explain, for example, why every single new reputed iniid taxa described in the last years comes out as the sister group of Inia, despite some well know species, as Ischyrorhynchus vanbenedeni is by far morphologically close to Inia than any of them.
The use of a large number of ordered characters needs, at least, a detailed justification. None is said about this in the manuscript.
The searching technics used here are quite old and more accurate a modern search algorithms are now available and should be used, including the consideration of use implied weighting since this may help to deal with the large number of homoplasies that a so large matrix obviously contains.
Additional comments: I suggest improving the description including other inioids (ie pontoporids) and basal Delphinida.
The phylogenetic analysis must be revised, perhaps reducing the matrix to a subset of the one used here to better understand the relationships inside Delphinida and reduce the distortions introduced by a lot of homoplasies.
I suggest also to eliminate character state ordination or a careful justification for them.
Using better search algorithms may also help.
Despite I cannot comment in detail, after a rapid analysis of the matrix I am convinced that it is necessary to review codification of several characters.


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

Input:
Title: A CLOSE RELATIVE OF THE AMAZON RIVER DOLPHIN IN MARINE DEPOSITS: A NEW INIIDAE FROM THE LATE MIOCENE OF ANGOLA
Review round: 2
Reviewer: 1

Output:
Basic reporting: I reviewed the initial submission of this manuscript, and I think the revised version is much improved. The authors have done a commendable job at addressing not just my comments and suggestions, but also those of the other two reviewers. Describing important new taxa can be an annoying ordeal when faced with non-overlapping edits and suggestions from different reviewers; the authors have done an excellent job in their Rebuttal document to clearly address all of the concerns. That document, these tracked comments, and most importantly the resultant publication will be a very useful to specialists in their future work — in other words, this work will get cited.

I think the authors have done a satisfactory job including Isthminia in the phylogenetic analyses, explained the elimination of other taxa from the analyses, and included (and discussed) support values for divergences and topologies in their revised manuscript. I think the discussion of comparative phylogenetic results relative to previous studies make the revised manuscript especially useful.

The revised text, figures and tables are solid and really do not require much more attention for publication — see very minor items below.
Experimental design: Again, the authors have mollified my concerns.

One note, on L. 100, the material from Angola is currently on loan to ISEM in France. Neither of the field study approval documents (please note that they use the original taxonomic name from the initial submission) provide any kind of substantive declarations about the status of this material, especially with respect to future disposition in Angola. Will it ever be returned? Under what conditions? I understand the precarious status of natural history institutions in Angola, and I laud the inclusion of many collaborators as co-authors, to increase the stakeholder base, as a means of science diplomacy. But I would say that the authors are ethically obliged to clarify the status of the material not just currently, but their future intents — especially with their open gesture to Angolan culture with their decision for the current species epithet of the new taxon.
Validity of the findings: I think the revised version does a good job fairly parsing the significance of a marine inioid from Angola, relative to all other known inioids. Yes, it would be great if we knew more about the freshwater fossils from South America, but the authors are correct in pointing out that until someone honestly tackles a thorough revision/redescription of putative ischyrorhynchines, we won’t really be able to decipher the timing of marine-to-freshwater transitions in this group. (I say this as someone who has observed and help recode some of this material in Argentine institutions). So, in other words, the revised text is good to go.
Additional comments: Minor comments, but still should be addressed:

L. 208, use indigenous instead of authochtone. I also really encourage the authors to make sure they have contacted members of this group (if they survive) or discussed this species epithet with Angolan citizens. It is an important courtesy.

L. 317, eliminate the stand-alone sentence. It doesn't help the paragraph. Connect it with the preceding one, please.

L. 594, Pan-Inia requires italicizing. I know, it's annoying, but PhyloCode will be happen. One day.


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

Input:
Title: A CLOSE RELATIVE OF THE AMAZON RIVER DOLPHIN IN MARINE DEPOSITS: A NEW INIIDAE FROM THE LATE MIOCENE OF ANGOLA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The modifications introduced improved the manuscript.
I have just two observations but are more a matter of opinion and choice.
1. Despite it is true that Ischyrorhynchus has no ear bones preserved (despite one was referred to it) the available specimens in La Plata and Buenos Aires museums provide more information than the specimen here described, which also has no preserved ear bones. So, this is not a good argument to explain the "problematic" position of Ischyrorhynchus in the proposed phylogeny.
2. I insist that I consider a problem to use an extremely large and taxon extensive matrix as the used here. There are in it lots of non-applicable and missing characters which can introduce more "noise" than rather help in the analysis.
But, as I said, this is not an obstacle for the authors to present their position.
Experimental design: None
Validity of the findings: Acceptable
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: CHILDREN ARE NOT LIKE OTHER LOADS: A CROSS-CULTURAL PERSPECTIVE ON THE INFLUENCE OF BURDENS AND COMPANIONSHIP ON HUMAN WALKING
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is very well written. It uses scientific language of the right level and the manuscript will be understandable for anyone with a basic science background who is interested in it.
The Introduction is excellent and provides a very good overview of the background, i.e. what determines gait and specifically walking speed across environments, genders, social contexts etc. I feel this is fascinating to read as it is very relevant not just to biomechanists but also to e.g. cultural and physical anthropologists, and psychologists.
The figures and tables are suitable. I checked the raw data and it is clearly presented ad an Excel sheet.
The Results and Discussion refer nicely to the Introduction. The paper in not too long nor too brief for the contents.
What I really appreciate about this paper is that it uses the simplest techniques possible – anyone with a timer and a roll of marking tape could do this! The manuscript shows that there is still scope for highly relevant research without having to rely on high-tech. What suffices, in this case, is to have an innovative and scientifically interesting idea, which the authors have. This is a refreshing manuscript that is a pleasure to read.
Experimental design: There is primarily an observational study, but the data are well used to test specific hypotheses set out in the Introduction. The main purpose of the study is to compare how various loads are carried across cultures and the authors have highlighted the importance of such research very clearly and describe how their data fill a knowledge gap. The data have been collected to a high technical and documented ethical standard. The research could be replicated with the information provided in the paper, although the description of the study sites (lines 139-141) should be more detailed (names and concrete details of locations, GPS coordinates).
I do have some concerns about the actual data which I hope can be clarified by the authors in a revised version. Whilst the number of subjects is high (1721), the authors used a single site per “culture” (North American vs. Ugandan). Whilst they justify their choice, it can be asked whether a single suite can correctly represent the culture. This concern is amplified by the absolute speeds of the participants being much lower than described in virtually any previous study. There are some other uncommon findings such as children walking at the same speed as adults (see section 3 below). Therefore, at this stage, I am not convinced that the speeds recorded are representative of the populations measured. Whilst the paper focuses on _relative_ speed differences between conditions and populations, I feel that if the _absolute_ speeds (even for individuals walking alone) deviate from normal, the relative differences might be skewed as well.
Validity of the findings: The findings are interesting for scientists from different backgrounds and the analysis as such (statistics etc.) is valid. As outlined previously, it should be justified better why the raw data are representative of “American“ and “Ugandan” cultures even though only one site per culture was used, and some aspects of the data suggest they are not what would normally be expected based on a fairly large body of existing literature.
The clearest example is the self-selected walking speed of the American adults in this paper. Whilst the text discussed only relative numbers, the absolute speeds can be seen in the figures and in Table 3. They are nearly always below 1 m/s. This is very slow for self-selected walking speed and well below what would be the optimum walking speed in terms of Cost of Travel. The mean speed for the American adults is 0.8 m/s. The authors very briefly mention this in the Discussion (lines 283-288) and suggest the speeds are similar to some ethnographic data (female foragers etc.) but I would argue that neither these populations, nor their walking contexts, are good bases of comparison for the subjects in the current study. Levine & Norenzayan (1999) and Ishaque & Noland (2008), both cited in the manuscript, report on comparable populations to the Americans and they find self-selected walking speeds of typically around 1.4 m/s. This observation is my main concern about the manuscript and I feel this issue should be tackled convincingly by the authors as it might affect the results and their significance.
A smaller but not insignificant concern is that the substrate is different between the sites; concrete in the US and packed dirt in Uganda. It is a pity that the same substrate (concrete) was not used in both locations and some rationale should be given why this is judged to have no relevant effect on the data (if so).
Additional comments: Here I offer some additional and more minor comments to the authors which might help them to further improve the manuscript.

-	An issue that I hope can be clarified is seen in the raw data but is not discussed in the manuscript itself. When checking the raw data, apart from the first author there is an additional observer “A. Bellville” (who is currently mentioned in the Acknowledgements) and potentially another one labelled “3”. The Acknowledgements mention more people involved in data collection (but not mentioned in the raw data). Have the authors checked for a potential observer bias? Were these observers crucial to the study (have they had intellectual input in it?) and if so do some of them deserve co-authorship? I have no reason at all to doubt the academic judgment on authorship of the authors, but I suggest that at least observer bias is tested. The authors have argued that the American and Ugandan populations are similar in terms of body size and that the contexts are also comparable. Yet, they might want to provide additional arguments why the difference between the populations is just (or mostly) cultural. E.g. did the American subjects include African Americans? Are they different? Please provide some references for the statements about culture in lines 130-133.
-	Line 106: “closer to the CoM” – but carrying on the head in African women and Nepalese porters is very efficient?
-	Line 158: “estimated” center of mass.


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: CHILDREN ARE NOT LIKE OTHER LOADS: A CROSS-CULTURAL PERSPECTIVE ON THE INFLUENCE OF BURDENS AND COMPANIONSHIP ON HUMAN WALKING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language is clear and professional throughout. I saw no typographical or grammatical errors. The article is also structured in a straightforward way. Data is shared effectively by means of graphs, tables and the main text, and discussion is focused on the data itself.
Experimental design: The primary research on walking speeds, group size and particularly child-carrying amongst American and Ugandan walkers is original and significant. The research questions derived from this are all well defined, and a range of relevant literature is referred to in the opening part of the paper and the discussion. Methods are described clearly and there are no problems with technical or ethical standards.
Validity of the findings: The findings are clearly stated in the results section and their meaning and implications are discussed in the following section. Of particular interest was the finding that child caring groups in Uganda walk slower, as do men walking in groups, compared to in America. This is explained by way of the possibility of a higher person-to-person contact norm in Uganda, and the relative lack of male competitiveness in America. These are both intriguing argument that support the general hypothesis of the paper that culture is a significant factor in walking behaviour. The conclusion to the article is clearly put in this regard to suggest alternatives to biological and morphological difference as explanatory models.
Additional comments: In general I found this to be a very readable and interesting paper. It would be interesting to compare these observational results with some qualitative data exploring the walkers' own perceptions of why they walk in the way they do.


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: CHILDREN ARE NOT LIKE OTHER LOADS: A CROSS-CULTURAL PERSPECTIVE ON THE INFLUENCE OF BURDENS AND COMPANIONSHIP ON HUMAN WALKING
Review round: 1
Reviewer: 3

Output:
Basic reporting: Review: Bouterse, L. and Wall-Scheffler, C.; Children are not like other loads: A cross-cultural perspective on the influence of burdens and companionship on human walking.
Submission to: PeerJ.
This manuscript is an analysis of variation human walking behaviors, including load carrying and child transport, derived from non-invasive observations made in two urban public settings: Central Uganda; the United States. The researchers have recorded walking speed, load carriage, and group composition and specifically highlight distinctions in group walking and load carrying behaviors seen between the two cultural settings. suggest that the different location, thereby concluding that cultural factors play a role in altering the dynamics of human locomotion in different world settings.
	The current manuscript is acceptable for publication in PeerJ as it addresses several unexplored topics of interest to locomotor researchers, namely what impact may the carrying of children as well as group composition have human locomotor behavior and are the dynamics of walking and load carrying dependent on cultural context. The authors demonstrate that the answers to such questions are yes, locomotor dynamics are influenced by cultural factors and that future models of human walking behaviors should attempt to account for cultural context. The current manuscript is a tightly streamlined paper. It is succinctly written with an introduction that clearly states the goals of the study, a methodology that provides the necessary descriptions for the variables of interest and those used, a results section highlighting the clear differences and similarities between the two groups sampled and analyzed, and a discussion section that contextualizes the implications of these results without overstating them. The implications of the current study should have an influence on future locomotor research by indicating that cultural context is an important factor rather than an unquestioned practice used in most current locomotor models that “one size fits all.”. While the study could have been enhanced with subsequent controlled locomotor observations and analyses of the individuals initially examined, the non-invasive methodology created limits on such follow-up. Regardless, the current paper does in fact stand on its own with respects to its results and conlusions. Thus, it should be published.
Experimental design: For this particular observational study, the research design holds.
Validity of the findings: The authors have not overstated the implications of their results.
Additional comments: See basic reporting.