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: DO PATIENTS WITH CHRONIC UNILATERAL OROFACIAL PAIN DUE TO A TEMPOROMANDIBULAR DISORDER SHOW INCREASED ATTENDING TO SOMATOSENSORY INPUT AT THE PAINFUL SIDE OF THE JAW?
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper does an excellent job referring to past literature both in terms of background and referencing relevant past work.

Raw data is shared - one small suggestion would be to also provide a key that identifies what each abbreviation refers to (for example, add an extra tab to the spreadsheet entitled Variable Key that has one column that lists each variable name and one column that provides an explanation of what the variable name refers to).

Overall, professional article structure.

I would recommend an extra read of the paper from a person with English as first language. Overall, the paper is very well written and clear, but there are some sentences where the grammar used is a bit awkward and could be improved, which would assist in readability. For example, lines 51-52: "Also observed are abnormalities in tactile processing". This could be combined with the first sentence to read: "Temporomandibular disorder (TMD) is typically characterized by chronic pain in the temporomandibular joint that is often accompanied by abnormalities in the processing of tactile input to this area." And lines 60-61: "However, these studies did not include unilateral TMD patients, but also bilateral TMD patients who were "asked about the most painful side"." This could be re-worded to: "However, these studies did not exclusively include patients with unilateral TMD; rather,  patients with bilateral TMD were included, using the most painful side (self-reported) as the TMD-affected side in analyses." Also lines 103-104: "The majority of the sample (70%) did not yet receive treatment at the moment of testing". This could be re-worded to "The majority of the sample had not received treatment for their TMD pain at the time of testing". Also line 343 - "To pain further insight...." I am not sure what this is meant to read.
Experimental design: Overall, well done.

Hypotheses: Currently, hypotheses in both directions are given. That is, according to the 'spatial neglect hypothesis', patients will have slower processing of tactile stimuli at the painful vs non-painful joint, where as based on the 'hypervigilance hypothesis' the opposite is expected. I think it needs to be clearly written that the overarching hypothesis of the paper is that there will be a difference in spatial processing of tactile input in people with unilateral TMD, but based on the literature, the direction of this spatial bias (prioritising painful vs non-painful tactile input) is unclear. At the moment, it is not clear if the authors have gone with the last hypothesis presented at their main hypothesis. Also, it is unclear to the reader why there is no hypothesis specific to comparisons between the TMD patients and the healthy control group (we find out later that this hasn't been compared).

Analyses: I do not understand why a statistical comparison cannot be made between TMD and healthy controls. The current argument is that because people with TMD had pain on different sides (left vs right-sided jaw pain), then the meaning of the PSS is different than in the control group. However, if healthy controls have no difference in spatial processing bias between stimulation on the left and the right, and if TMD patients have no difference in spatial processing bias based on whether they had left-sided TMD pain or right-sided TMD pain, then a between group comparison should be fine to make. At the least, you could take half of the healthy control sample and switch the test stimuli to the left joint and the reference stimuli to the right joint such that the data is matched to test and reference stimuli of the left-sided TMD patients (n=10 left sided pain and n=10 right sided pain). Or perhaps compare the right-sided TMD patients to the whole sample of the healthy controls (and vice versa for the left, switching the healthy control test and reference stimuli). I would suggest including some sort of comparison of PSS between groups in the analysis.
Validity of the findings: Abstract: I don't think that the first sentence of your abstract's discussion aligns with your results. The results found no difference in spatial processing in patients with unilateral TMD (although I do agree this was close - 0.07 -  and may have been underpowered). However, the way it  currently reads is that there was a difference in tactile processing even in people without fear-avoidance beliefs. I would argue that this should read: "The results suggest that patients with unilateral TMD show a tactile processing bias toward the painful side of the jaw, but only when high levels of fear-avoidance beliefs are present." Then you could specifically state that this supports the hypervigilence hypothesis.

Similarly, the conclusion of the paper needs to be updated to reflect this.
Additional comments: 1. Introduction: Consider adding in the 'why do we care' aspect of spatial processing bias, e.g., understanding the presence and nature of any spatial processing bias may help us determine new treatment for these patients.
2. Methods, Line 115: "attaining the requested performance criteria during the task". At the moment, the reader is unaware of what this refers to. Please reference the appropriate section, e.g., (see TOJ data handling).
3. Cronbach Alpha results for self-report questionnaires: This is commendable that this was evaluated in the study sample. I might suggest providing an overall statement at the start of this section saying that internal consistency was acceptable for all questionnaires and then refer to a supplementary table that has the Cronbach alpha values for all measures. At the moment, this section is quite text/number heavy.
4. Methods, lines 210: Perceived intensity of tactile stimuli during testing - if it differed between left and right side of the jaw, was the intensity used updated in real-time during testing? I don't think this is a problem if not, but important to know.
5. Results, TOJ, Line 282: Should this read mean difference?
6. Perceived tactile intensity between painful and non-painful side, lines 295 - 297: Given that tactile stimuli was matched between sides at baseline, is this not just a validity check (i.e., to ensure that any differences in spatial processing were not due to differences in perceived intensity)?
7. Discussion, line 403: contextual factors - please provide an example of what you mean by this.


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: DO PATIENTS WITH CHRONIC UNILATERAL OROFACIAL PAIN DUE TO A TEMPOROMANDIBULAR DISORDER SHOW INCREASED ATTENDING TO SOMATOSENSORY INPUT AT THE PAINFUL SIDE OF THE JAW?
Review round: 1
Reviewer: 2

Output:
Basic reporting: I think this is very high quality. My only suggestion is that the authors think whether there might be better papers to cite in some instances than their own. This is particularly relevant for the methods and discussion.
Experimental design: I think the study is within the scope of PeerJ.
I think the knowledge gap is defined but should focus on the potential benefit of knowing this stuff in TMD, which is a highly problematic condition.
I think the experimental design has solid fundamentals, but it is not well suited to test the hypotheses the paper suggests it is testing. I actually think that the study is testing the hypothesis that TMD pain patients will have a spatial bias to the affected side. The other hypothesis they mention has not been proposed for TMD and in fact has been discussed as a potentially characteristic to just CRPS and perhaps unilateral low back pain. It seems odd and the rationale not well presented, to pitch these two hypotheses, which relate to different situations, against each other.
I think any experiment nowadays should build on a protocol and analysis plan that is ideally peer reviewed - if the analysis here was as planned, it would not have got through peer review. These things should also be locked prior to data collection and analysis so the reader can be assured that the study is undertaken in line with the principles of transparency and replicability. That this process was not followed represents a limitation of this work, which should be mentioned in the discussion.
The wider design is in my view highly problematic because there are about 15 analyses and no mention of the risk this presents to findings. Moreover, there is not a clear presentation of what results would be required to support or refute the hypothesis about vigilance. That is, the authors use several measures and several sub factors but don't stipulate a priori what would be required to refute. This leave it highly vulnerable to false results and as it stands, i can't interpret the results in light of this substantial threat to validity.
Methods are very well described and could easily be replicated.
Validity of the findings: The authors do not accept the negative results. Rather they suggest that despite the statistical analyses clearly not supporting the hypotheses, that a positive result existed. I find this very surprising. This means that the discussion, which focusses to a large extent on the positive result, is inappropriate because the result was negative. In my view, the discussion needs to be completely rewritten to reflect the results, not the predicted results. The authors report that 65% of the patient group did what they predicted they would, but they don't state how many of the control group did. The positive finding on one sub factor of one outcome for one hypothesis can not in my view be given any weight on the grounds mentioned above.
There is a large literature on spatial biases and their implications and possible interactions with other systems, yet this literature is not really addressed even though the current findings are very relevant to it. That unilateral TMD does not have a spatial bias is important and interesting (i suspect that they may have a smaller one, but your study wasn to powered to detect that).
Additional comments: I have attached an annotated PDF with a range of specific comments that i hope you find helpful.


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: DO PATIENTS WITH CHRONIC UNILATERAL OROFACIAL PAIN DUE TO A TEMPOROMANDIBULAR DISORDER SHOW INCREASED ATTENDING TO SOMATOSENSORY INPUT AT THE PAINFUL SIDE OF THE JAW?
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper is very well-written. It has a clear structure and is easy to follow. I particularly liked the clear explanation of how the data may help us differentiate between two rival hypotheses.

The dataset should have a key to explain what each of the variables are and how they are coded. For example, hand dominance and pain location are both coded as 1 and 2 but I don't know which side is 1 and which side is 2.
Experimental design: The paper meets all of the criteria for this section and I have no suggestions for improvement.
Validity of the findings: For clarity I would prefer exact p values to be reported rather than "ns" (e.g. lines 118 and 119).

The authors say they used the TOJ analysis guidelines proposed by Spence, Shore and Klein (2001), but they appear to be slightly different. Spence et al said "Participants were excluded for one of three reasons: if any of the eight correlations were less than 0.4, if two or more of the calculated PSSs were greater than +/-250, or if the z score for a particular stimulus pairing at the +250 ms and -250 ms SOAs were, when averaged, less than 1.29 (i.e. less than 90% correct)" (p. 805-806). Could the authors add an explanation for the differences and/or add a note to say whether the results would be any different if using the original exclusion criteria.

I thank the authors for including details of their power analysis. It is a shame that there wasn't sufficient power for the key effect, which is reported as d=0.42 (i.e. medium-sized), to be significant. Future studies should be powered to detect the smallest effect size that would be considered interesting or relevant, rather than that found in previous studies, possibly even with 90% power.

At several points in the results I wondered whether the control was really necessary since the key hypotheses being tested didn't require one and the PSS was not compared between groups. Perhaps the authors could make the need for the control group clearer in the manuscript.

I think the authors could say more about their analyses of the perceived intensity of the tactile stimuli in the introduction and discussion. The intensity on both sides and in both groups was tailored to be a 3 on a 1-5 scale  (lines 132-141) so was the analysis comparing sides (lines 295-298) and groups (lines 293-295) intended as a manipulation check or a hypothesis test? What are the implications of the difference between groups? Does this mean that the TMJ group must have experienced increasing pain over time?

On line 340 I think it would be better to say "did not reach significance" rather than "just failed to reached significance". Also I think the authors could be more nuanced on line 338  by saying something to the effect of "which had it been significant would suggest enhanced...".

On line 354 the authors note that the correlation should not be overstated given the small sample size, but equal important is that is was an exploratory analysis rather than a hypothesis test, so I think this should be noted here too.

On line 364 I think it is incorrect to say that the result contradict previous findings, since there were significant. It may be more correct to say that the results failed to support previous findings.
Additional comments: I enjoyed reading the paper and I think it should be published. Although I have written quite a bit in the 'Validity of findings' section, these concerns should be fairly easy to address.

I appreciate that the authors have stated whether most analyses were hypothesis tests or exploratory (which many authors do not do) but I hope that pre-registeration of analysis plans will become more common in this field.

A few minor points:
Line 82: "Rivalry hypotheses" should be "Rival hypotheses".
Line 127: "procedure is highly similar as" should be "procedure was highly similar to".
Line 168: is "...your relation..." correct? It would make more sense without the "your".
Line 226: Should this be "(virtual) interval", as with the PSS description on line 227?
Line 375: "and is this feature" should read "and this feature is".
Line 377: "More specific" should be "More specifically".
Line 380 "Anyway" sounds quite informal and "Nevertheless" may be better.
Figure 1 would benefit from a note in the description to say what the scale of the y axis was (-200 to +200?).


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: DO PATIENTS WITH CHRONIC UNILATERAL OROFACIAL PAIN DUE TO A TEMPOROMANDIBULAR DISORDER SHOW INCREASED ATTENDING TO SOMATOSENSORY INPUT AT THE PAINFUL SIDE OF THE JAW?
Review round: 2
Reviewer: 1

Output:
Basic reporting: I thank the authors for their changes. The grammatical changes make the manuscript much easier to read.
Experimental design: Thank you for clarifying the analyses and for including analyses with the healthy control sample.
Validity of the findings: The only thing that I would recommend would be to avoid stating that you found a non-significant trend (abstract and conclusion). Otherwise, using the same logic, we could argue that the correlation between PSS and the somatic focus subscale of the TSK (p=0.03) is actually supporting a trend towards non-significance (given that it is quite close to p = 0.05).
I would just state that you had non-significant results. You could then clarify that based on your findings, you could not rule out inadequate power as a reason for this (given the higher variability in PSS than anticipated).
Additional comments: Excellent work on the revisions!


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: DO PATIENTS WITH CHRONIC UNILATERAL OROFACIAL PAIN DUE TO A TEMPOROMANDIBULAR DISORDER SHOW INCREASED ATTENDING TO SOMATOSENSORY INPUT AT THE PAINFUL SIDE OF THE JAW?
Review round: 2
Reviewer: 2

Output:
Basic reporting: Still very happy with this.
Experimental design: I think this has been greatly improved, particularly with regard to clearly labelling primary and exploratory analyses.
Validity of the findings: The new version is much more faithful to the results in my view. I appreciate the timing of data collection may have preceded the real push for publishing protocols etc, but i do not think that the rarity of the practice is very good justification for not doing it. I am pleased the authors mention this in limitations. I am also still submitting papers that were started before we adopted this policy and I too see it as a limitation of those papers.
Additional comments: I think the response to all reviewers has been excellent. I think the paper is very interesting and moves the field forward.


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: DO PATIENTS WITH CHRONIC UNILATERAL OROFACIAL PAIN DUE TO A TEMPOROMANDIBULAR DISORDER SHOW INCREASED ATTENDING TO SOMATOSENSORY INPUT AT THE PAINFUL SIDE OF THE JAW?
Review round: 2
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I think the authors have done a good job in responding to my and the other reviewers' previous comments. There are a few typos throughout (e.g. in line 40 "my" should be "by" and in line 387 "we the spatial bias" does not make sense) but otherwise I think the paper is suitable 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: GENOMIC SIGNAL PROCESSING FOR DNA SEQUENCE CLUSTERING
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, the paper is well-written and easy to understand. There are a few minor spelling and grammatical errors present in the manuscript that the authors should correct. Here are some examples:
	1	Line 13 should read "...popular method that has been used to..."
	2	The sentence on lines 33-35 should read "However, the K-means algorithm relies on the frequent computation of similarity metrics.."
	3	The reference on line 159 is incorrectly formatted.
	4	The algorithm's name, STARS, is misspelled as SATRS on page 5 of the installation guide and page 1 of the user manual.
	5	The title is shown as "Genomic signal processing for DNA sequence clustering" and "Genetic signal processing for DNA sequence clustering." I suggest using the former, as it reflects the wording in the main body of the text.
	6	The word "Matlab" on line 322 should be stylized as MATLAB
I also would like to make the following minor suggestions (starting from most important to least important):
	1	The figures have very small font, making them very hard to read. I suggest that the authors increase the font across all figures, especially for Figures 3-6, which have a lot of unused white space.
	2	According to the user manual in the link provided by the authors, the name of the algorithm is STARS. However, this name does not appear anywhere in the manuscript. The authors should include the algorithm's name at least once in the manuscript.
	3	The first two lines of the abstract (11-12) and the introduction (23-24) are exactly the same word-for-word. For some readers, this may come off as repetitive and distracting. I suggest that the authors change the wording of either the openings of the abstract or introduction.
	4	I suggest removing the word "novel" in the sentence on lines 58-60.
	5	Lines 303-309 are a little confusing to me. I am not exactly sure what the authors mean by phylogenetic trees requiring an external class. Either the authors should clarify this statement or remove the paragraph altogether.
I have one major comment for this section:
The papers "A new method to cluster DNA sequences using Fourier power spectrum" (Hoang et al., 2015) and "A novel clustering method via nucleotide-based Fourier power spectrum analysis" (Zhao et al., 2011) also cluster DNA sequences by first computing power spectra and then converting spectra to constant length vectors. I suggest that the authors cite these works and describe what sets their method apart from these previous methods. If possible, the authors should include a comparison in terms of running times and accuracy against these methods.
Experimental design: The authors describe their method with sufficient detail for others to replicate. Briefly, they convert DNA sequences to power spectra, and then group DNA sequences together using the K-means clustering algorithm applied on the frequency components of the power spectra. In order to make the power spectra of varying length DNA sequences comparable, they apply zero padding, as suggested by Borrayo et al., 2014. They applied their method to a set of 141 COXI sequences from several different organisms. I have the following major comments for the author that I believe will help improve the manuscript:

	1	The authors claim in lines 50-57 that sequence alignment algorithms like ClustalW and UCLUST are limited in the number of sequences they can cluster due to their heavy demand of computational resources. However, the authors do not provide a comparison of their algorithm with any of these algorithms, nor do they mention the running time of their algorithm. I would like to see a comparison against other algorithms like ClustalW and UCLUST that includes running time, memory usage, and/or clustering quality to justify their claims.
	2	As stated in lines 322-324, the authors have made their program as a standalone package. I commend the authors for making their algorithm readily available for users. However, I was unable to actually test their algorithm since it could only run on Windows. Most bioinformatics researchers use either Linux or Mac OS X, and hence replicating the authors' results would be difficult for such readers. The authors should provide the code open source (preferably on Github) so that users can run the code on their own copies of MATLAB or Octave.
	3	As depicted in Figure 2, hierarchical organization of the selected organisms plays a very important role in the manuscript's analysis. The hierarchical clustering algorithm is an alternative to the k-means clustering algorithm, and seems like a more appropriate fit for phylogenetic studies. I suggest that the authors repeat their experiments using hierarchical clustering and report the results in the manuscript.
	4	The authors should explicitly state how many frequency components each COXI DNA sequence is converted to (i.e. the value of "n" in line 103).
Validity of the findings: The authors applied their method on COXI sequences from various species and find that the resulting clusters reflect known biology. They also provide a thorough discussion of their results.

	1	I would like to see the authors repeat their experiments for sequence sets other than COXI. The Hoang et al. 2015 paper, for example, applies their clustering algorithm on 5 different datasets. Perhaps the authors can include the analysis on other sequence sets as a supplementary.
	2	Figures 3-5 show clusterings for the COXI set for various values of k. The values of k are chosen to reflect kingdoms, phyla, and classes. However, the clusters do not exactly correspond to these taxonomic ranks. The authors should compute centroids corresponding to the "true" kingdoms, phyla, and classes and compare the "true" clusters with the discovered clusters. A comparison of the inertia, or the within-cluster sum of squares criterion, between the "true" and discovered clusters should suffice.
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: GENOMIC SIGNAL PROCESSING FOR DNA SEQUENCE CLUSTERING
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this manuscript, the authors present a method for clustering
sequences in which the K-means algorithm is applied to a numerical
representation (the Voss representation) of DNA sequences to which
spectral analysis (a discrete Fourier transform) is applied.

The authors also present a visualization method to report the
resulting clustering.

Data sharing
-------------

- Link to the method is mentioned (lines 322-324) but not provided. Thus, I could not test the method.

- Datasets not provided

- The authors mention that they will provide "... executable and the dataset" (line 323). The executable
  is not enough. They need to provide the source code as well. Without the source code, the paper should
  not be published.

Professional English
---------------------

The article reads well.

Only comment: Avoid repetition of whole sentences. The first two
sentences at the beginning of the Abstract are identical word-by-word to
those at the beginning of the Introduction.

Self contained
--------------

In order to fully understand the methods, it would be relevant to have a full definition
of the

"power spectral density (PSD) {\hat S^\alpha}}" (lines 86-87),

as well as the

"frequency power spectra d(Sa,Sb)" (lines 89-90)
Experimental design: The authors apply their method to one gene: Cytochrome c oxidase I
(COXI), using different numbers of clusters. It is unclear why this
particular gene was selected, and why only one was analyzed.

The authors make a point of this method being fast. I would like to
see a experiment in which they show how much faster they are, compared
to, for instance, the other two methods they mention as slow: CD-HIT
and UCLUST
Validity of the findings: The description of what is found in the different clusters for COXI
is not very informative, as we do not know what the ground truth is.

Any clustering algorithm, is going to produce clusters. Assessing the
validity of the method presented in this paper, would require some
proof of principle. I would like to see the analysis of a gene for
which the phylogeny is well established (as different methods agree),
and how that compared with the method presented here.
Additional comments: Here I report some small changes that could improve the manuscript

- Abstract: GPS abbreviation used prior to definition

- All Figure need a more descriptive legend, and explanation of terms.

- Figure2: name of species are not readable

- Figures 3, 4, and 5: labels are not readable.


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: GENOMIC SIGNAL PROCESSING FOR DNA SEQUENCE CLUSTERING
Review round: 2
Reviewer: 1

Output:
Basic reporting: Grammar and spelling is still a minor issue in this paper. Here are a few examples from the added text:
A) "To determine the validity of the results, we computed centroids for true kingdoms and we compare these centroids to these you discovered with our method.” (263-264)
B) "UCLUST have a constant time, of 1 second for every experiment…” (282-282)
3) "However, since the K-means method promote the generation of centroids in highly populated regions of the feature space it results are more likely to obtain clusters of organisms that are highly related among them instead of organisms related by possible common ancestors or groups with a small number of less homogeneous organisms" (317-320)
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: GENOMIC SIGNAL PROCESSING FOR DNA SEQUENCE CLUSTERING
Review round: 2
Reviewer: 2

Output:
Basic reporting: This revision has taken into account most of the questions raised by the reviewers.
I do not have any further comments.
Experimental design: no comment
Validity of the findings: no comments
Additional comments: no additional comments


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

Input:
Title: EU PROTECTED AREA NETWORK DID NOT PREVENT A COUNTRY WIDE POPULATION DECLINE IN A THREATENED GRASSLAND BIRD
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Dear authors,

I really enjoyed reading the manuscript. The study has important implications for the conservation of the Little Bustard, and it can help support the reporting obligations of Portugal in relation to the Bird Directive. It also shows how management policies should be targeted at maintaining not only habitat availability but also habitat quality within protected areas, and highlights the need of going further from a mere designation of protected areas if an effective conservation wants to be achieved. I consider the data robust and the statistical analysis is sound.

Therefore, I recommend accepting the manuscript after addressing a few minor issues:

Minor changes

Line 31. “within the species remaining European stronghold”. Sorry, but it is not clear to me what the authors mean. The authors could indicate that Little Bustard is included in the Annex I of the Bird Directive, which is clearly related to the objectives of SPAs.

Lines 32. Please remove “(the European Union network of protected areas)”. Natura 2000 has been already defined in line 30.

Line 34-35. These SPAs are designated only for farmland bird conservation? I would say that SPAs are designated under the EU Bird Directive to protect bird species listed in the Annex I. In general SPAs are aimed at protecting also other species that do not have to be necessarily farmland species. Also, I am wondering if these “30 areas without EU protection” can be under national or regional protection. Please clarify it.

Line 36. Awkward sentence. Please rephrase, e.g. “the bustard national population declined 49% over the last 10-14 years, especially outside SPA.” Please indicate the population trends inside and outside the SPA system, or the difference between within and outside to show more explicitly the degree of effectiveness of SPAs.

Keywords: I would suggest “steppe birds” instead of ‘farmland bird’ which is already mentioned in the abstract

Introduction

Lines 57. Can be the author a bit more specific? Some examples of these biodiversity values? Do the authors refer to e.g. habitat or climate suitability?

Lines 58. I mostly agree, but instead of using Cabeza (2013) as reference (there are many others), I would show one of the few studies that uses population trends as follows: “(but see Pellissier et al., 2013).”

Reference:
Pellissier, V., Touroult, J., Julliard, R., Siblet, J. P., & Jiguet, F. (2013). Assessing the Natura 2000 network with a common breeding birds survey. Animal Conservation, 16(5), 566-574.

Line 85. This reference is very old, I would suggest adding a more recent reference to show the last trends for this species. According to BirdLife International (2016) “The European population is estimated to be declining by 30-49% in three generations (30.9 years)”.

Reference:
BirdLife International. 2016. Tetrax tetrax. The IUCN Red List of Threatened Species 2016: e.T22691896A90095419. http://dx.doi.org/10.2305/IUCN.UK.2016-3.RLTS.T22691896A90095419.en. Downloaded on 07 November 2017.

Line 170. What do the authors mean by “proportionally”?

Appendix S1 seems to be incomplete (see last sentence). “Because these IBAs were not subjected to any sort of management, for the …” Please revise it.

Discussion

Although the discussion and the main conclusions are well stated and linked to the research questions, previous studies have already showed that field management and timing can play a key role in the aptitude of fallows for steppe birds such as Little Bustard during the breeding season, affecting the vegetation structure as well as the amount and type of food resources at microhabitat level. For instance, early herbicide application and shredding were found to be the best treatments for Little Bustard in steppe areas of NE Spain (Robleño et al 2017). Thus, to improve the effectiveness of management actions, conservation guidelines for farmland birds should consider microhabitat preferences, given the importance not only of the amount of habitat provided but also of vegetation structure and food availability. I think that these issues deserve attention and could be mentioned in the discussion to better understand the relevance of habitat quality (and not only availability) for the conservation of Little Bustard in particular, and farmland species in general. In addition, previous research also highlighted the importance of intraspecific interactions in the definition of the habitat selection pattern of females and families (Tarjuelo et al 2013), issues also relevant for the conservation of the species.

Ponjoan et al (2012) can help to support the statement in lines 238-239, these authors found that ranging behaviour of males could be partially explained by age, habitat quality and site.

References

Ponjoan, A., Bota, G., & Mañosa, S. (2012). Ranging behaviour of little bustard males, Tetrax tetrax, in the lekking grounds. Behavioural processes, 91(1), 35-40.

Robleño, I., Bota, G., Giralt, D., & Recasens, J. (2017). Fallow management for steppe bird conservation: the impact of cultural practices on vegetation structure and food resources. Biodiversity and Conservation, 26(1), 133-150.

Tarjuelo, R., Delgado, M. P., Bota, G., Morales, M. B., Traba, J., Ponjoan, A., ... & Mañosa, S. (2013). Not only habitat but also sex: factors affecting spatial distribution of Little Bustard Tetrax tetrax families. Acta ornithologica, 48(1), 119-128.


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: EU PROTECTED AREA NETWORK DID NOT PREVENT A COUNTRY WIDE POPULATION DECLINE IN A THREATENED GRASSLAND BIRD
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript seeks to evaluate the efficiency of Natura 2000 areas in truly protecting habitat and encompassed biodiversity. The authors show a remarkable decrease in the population size of the little bustard (Tetrax tetrax) in Southern Portugal, one of the most important areas for the conservation of the species. Tough results are valuable and discouraging, I consider that they only constitute an initial step in the more profound and important evaluation that the authors propose. Fundamentally, I found as main problems that: (1) collected data and used methods do not allow to properly evaluate a trend of the population size of this or any other species (only two periods, 2003-2006 and 2016 were considered), (2) causal factors of changes in the phenomenon under study are not evaluated and poorly discussed (e.g. climatic conditions, hunting pressure, farmland use), except for the area under grasslands. (3) the area under grasslands is analyzed as a dependent variable, and not as a causal factor.

I acknowledge that data collection can be too expensive in economic and human effort terms, but alternatives exist to achieve to a more exhaustive analysis (e.g. by reducing the number of areas sampled but increasing temporal sampling, by exploring the land use or cover trends). I hope that my rejection decision does not discourage the authors since I found that they have many options to improve their findings and finally manage in a more efficient way these protected areas.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: ANTIFIBROTIC EFFECT OF XANTHOHUMOL IN COMBINATION WITH PRAZIQUANTEL IS ASSOCIATED WITH ALTERED REDOX STATUS AND REDUCED IRON ACCUMULATION DURING LIVER FLUKE-ASSOCIATED CHOLANGIOCARCINOGENESIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: (i) Very unclear figures and its legends
Quality of figures seems to be good, but it is unclear what should be focused.
I recommend to use arrows and circles to point out important parts so that readers can focus.
It is also unclear how many sections the authors analyzed to make their conclusion. If they prepared immune-stained sections from all the treated mice (5 mice in each group?), that should be described.
(ii) No legends in supplementary figure.
What do weigh 1~8 mean in body weight?
Hamster No.5 seems to die 60 days after XON treatment. How did author measure liver weight per body weight of Hamster No. 5 at later stages?
(iii) It is very confusing because figure numbers are sometimes missing in Result section. Readers will not understand which figures they need to see in each description.
Experimental design: No treatment control (without Ov infection and NDMA) should be performed.
If authors have done, the results should be shown or clearly described.
Validity of the findings: (i) Quantitative and subsequent statistical analysis should be done to compare the difference between control and treated groups in immune-histochemical analysis. That will enable us to evaluate the effects of drugs more precisely.
Especially, it is difficult to judge whether there is any synergistic inhibitory effect of XN and PZ treatment on periductal fibrosis development. Evaluation of fibrosis stages (describe in methods) is not reflected on any figures.
(ii) XN and PZ treatment reduced several abnormalities, which are induced by Ov infection and NDMA treatment, such as DNA damage, CD44v8-10 expression, and fibrosis. Main concern is that only one of five hamsters in the ON group developed CCA. Although Ov-mediated ROS responses, inflammation and fibrosis result in CCA genesis, it seems very difficult to evaluate the effects of XN and PZ on CCA genesis under the condition used this study (just “suggest” will be better). In addition, it is not clear whether the provided figures in ON group are from CCA-developed hamster or from non-CCA hamster.
(iii) Figure 7 is confusing. For example, XN suppresses periductal fibrosis through reduction of the oxidative stress responses or independent of them? If the former is the case, what does the line from XN to periductal fibrosis mean?
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: ANTIFIBROTIC EFFECT OF XANTHOHUMOL IN COMBINATION WITH PRAZIQUANTEL IS ASSOCIATED WITH ALTERED REDOX STATUS AND REDUCED IRON ACCUMULATION DURING LIVER FLUKE-ASSOCIATED CHOLANGIOCARCINOGENESIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this manuscript, Jamnongkan et al. described the effects of xanthohumol (XN) in combination with praziquantel (PZ) on various aspects of liver fluke (Ov)-associated cholangiocarcinogenesis, including DNA damage, redox status change and periductal fibrosis induced by Ov and NDMA administration in hamsters.  The overall experiments seem technically sound. However, the interpretation of the results is hard to follow (particularly the data on immunohistochemistry) due to the lack of quantitative data on immunohistochemistry as well as the lack of experiments with control hamsters.

A number of suggestions are as follows.
1)	A major problem along the Results section is the lack of quantitative data on immunohistochemistry.  The authors’ interpretation on the effects of XN treatment with or without PZ on histopathological findings, DNA damage, redox status, iron accumulation is largely based on their subjective impression, and no statistical analysis was performed to objectively evaluate the effectiveness of XN on liver fluke (Ov)-associated cholangiocarcinogenesis.  They should classify the abnormal findings associated with (Ov)-associated cholangiocarcinogenesis, such as bile duct proliferation, hyperplasia, dysplasia of bile ducts, cholangio-fibrosis in each group during the progression of CCA (Figure 2).  The graphs showing the number and/or levels of pathological abnormalities along time course should be included in the Figures.

2)	In the same line with item 1, in order to validate their claim that either XN or PZ treatment could effectively reduce the accumulation of 8-oxodG, and that XNOP group could reduce DNA damage more effective than other groups (lines 253-255), the quantitative and the statistical analysis on the effect of XN with or without PZ on DNA damage should be performed.  Also, the immunohistochemical data in Figure 4-6 requires quantitative measurements to validate their interpretations such as “no synergistic effect was observed in XNOP (line 265) or effective reduction in iron accumulation and TfR-1 expression for the XNOP as compared with other groups (lines 274-275).

3)	In addition, the authors should include the data from untreated hamsters in Figures 1-6.  Furthermore, the authors should indicate (by arrows or arrosheads) abnormalities such as the “white granules and small foci (line 229)” and “the obstruction of gall bladder” in the relevant Figures.

4)	In the Introduction section, their description and the rationale on PZ treatment was insufficient.

5)	I don’t’ understand the rational for measuring the CD44v8 to evaluate the redox status. Authors should describe the mechanisms as to how XN-induced alterations in oxidative stress would alter the expression of CD44v8-10.

6)	In the Conclusion section, it is very vague whether their data indicate the effectiveness of sole XN treatment on Ov-associated CCA or their data indicate that the synergistic effect of XN in combination with PZ.  These ambiguous conclusions could be derived from the lack of the quantification and rigorous statistical analysis.

7)	There are numerous grammatical errors and typos.

8)	Several papers are cited without being listed in the References, including Andriopoulos et al. (2007)


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: ANTIFIBROTIC EFFECT OF XANTHOHUMOL IN COMBINATION WITH PRAZIQUANTEL IS ASSOCIATED WITH ALTERED REDOX STATUS AND REDUCED IRON ACCUMULATION DURING LIVER FLUKE-ASSOCIATED CHOLANGIOCARCINOGENESIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: See general comments
Experimental design: See general comments
Validity of the findings: See general comments
Additional comments: 1. In the first sentence of Results, "The liver per body weight of carcinogenesis in hamster groups either …." does not make sense. "The liver per body weight of hamster groups either …." will be better.

2. Body weight in supplementary figure is still confusing. If one column corresponds to the average of body weight from 5 mice, what does “Time 1-8” at each day (60, 90, 120, 180) mean?

3. Hamster No.5 seems to die 60 days after XON treatment. How did author measure liver weight per body weight of Hamster No. 5 at later stages?
Authors’ response: We measured liver per BW in the hamsters that were alive at each time point.

This is not the answer!
You put “death” into a column of hamster No.5, XON groups in the liver per BW sheet.
If the mouse died 60 days after the treatment, you can’t measure anything as in the case of ON groups.
However, you put values in 90, 120, 180 days about the hamster.

4. Showing figures are not necessary. However, the authors should, at least, describe the results from untreated groups anywhere in 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: ANTIFIBROTIC EFFECT OF XANTHOHUMOL IN COMBINATION WITH PRAZIQUANTEL IS ASSOCIATED WITH ALTERED REDOX STATUS AND REDUCED IRON ACCUMULATION DURING LIVER FLUKE-ASSOCIATED CHOLANGIOCARCINOGENESIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: In this manuscript, Jamnongkan et al. described the effects of xanthohumol (XN) in combination with praziquantel (PZ) on various aspects of liver fluke (Ov)-associated cholangiocarcinogenesis, including DNA damage, redox status change and periductal fibrosis induced by Ov and NDMA administration in hamsters.  The overall experiments seem technically sound and their conclusions were well supported by various experiments with quantification analysis.
Experimental design: The manuscript has been significantly improved by the revision, with additional data that strengthen the authors' model.
Validity of the findings: All the concerns I raised about the previous version have been adequately.
Additional comments: The revised manuscript is much improved and I have no further 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: MORPHOLOGY AND STRUCTURE OF HOMO ERECTUS HUMERI FROM ZHOUKOUDIAN, LOCALITY 1
Review round: 1
Reviewer: 1

Output:
Basic reporting: The following numbers refer to line number, followed by my comments. All are minor corrections.

55-58: I don’t think the catalogue of citations is necessary to support this point. Please pick the few (five at most) most relevant citations out of this list.

68-74: Very long sentence.

76: Grammar: Missing word – “broaden [the] current understanding”

78: Grammar: “humeri” not “humerus”

108: “seminal”—please replace with “initial” or some synonymous word. “Seminal” is gendered and archaic language.

121: Grammar: “modern-human like”, correct to “modern human-like”

134-136: A citation to support this statement would be appropriate.

276: Referencing format error: “…mobility)(Shang et al.,…)” ”…mobility; Shang et al.,…”

346: Referencing format error: (Weidenreich, 1941) not italicised

361: Referencing format error: (Weidenreich, 1941) not italicised

396: Missing word—“5% [of] length”

418: Missing terms: “identify AP and ML”  “identify anteroposterior (AP) and mediolateral (ML)”. As a matter of form, these should always be defined before they are abbreviated, despite being common terminology.

499: Syntax: the opening sentence alludes to the %CA of Humerus II being similar to something else, other than KNM-ER 1808. Is something else being compared to Humerus II, or should the sentence read: “The midshaft of Humerus II exhibits a high estimate of %CA, similar to the %CA of the KNM-ER 1808 cross section…”?

674: Language accuracy—Change “inferiorly-rotated and human-like scapula” to “human-like laterally-oriented scapular glenoid”

Figs 3 & 4: Labels for the axes required, as well as a legend for the abbreviations in Fig. 3.

Tables 1 & 2 should be swapped. The results for Humerus II are discussed before the results for Humerus III, but Table 1 refers to Humerus III. Please make Table 1 the results for Humerus II and Table 2 the results for Humerus III.

Figure S4: Grammar—“proximalmost”  “proximal-most”. Please also label the unit of measurement, either in the figure itself or in the caption.

Figure S5: Please include a legend for the abbreviations used in the figure.
Experimental design: With regard to the methodology and experimental design, I have few criticisms; they are, for the most part, appropriate to the objectives of the study. I do, however, have a few comments on the comparative samples and would like some clarification on other points.

The African Homo erectus sensu lato sample quite understandably consists only of KNM-ER 1808 which shows evidence of pathological apposition of bone on the long bones, though significantly without entheseal involvement. Initial assessments by Walker et al. (1982)attributed the pathology to hypervitiminosis A by way of the consumption of bee brood. Hypervitiminosis A, however, affects the entheses. Noting the lack of entheseal involvement, the pathology has more recently been attributed by Rothschild et al. (1995) to treponematosis in the form of yaws, which does not affect muscle attachment sites and causes extensive bone destruction. While Ruff (2008) used Leakey and Walker’s “corrected” cast of KNM-ER 1808 in his analyses and his values are used in the present paper, a justification of the use of this specimen would be appropriate at this juncture. If not a justification, then at least a discussion of the limitations and possible effects the pathology of the specimen may have on the results, especially as they could be profound.

278-280: “we report separate right and left humeral properties of Tianyuan 1 and emphasise same-side comparisons when possible” – why were left humeri not sampled for the recent modern Chinese samples, especially as you emphasise same-side comparisons?

339-356: This section is somewhat convoluted to read, so perhaps some time could be spent clarifying it. Did you create an artificial volume rending of Humerus II by rescaling a volume rendering of Humerus III? These two humeri differ quite notably in cortical thickness it seems, so was some warping/morphing conducted to match the published measurements or the radiograph? If so, this needs to be made more explicit. I understood all the steps independently, but the reasoning for doing it was not clear.
Validity of the findings: The results appear to be of interest to the field and the findings have the potential to add much-needed information about temporal and geographic variations in humeral strength and rigidity properties in H. erectus sensu lato. I do have concerns that the pathological status of KNM-ER 1808 may be confounding the results, and the authors will need to address this.

In lines 636—665, the authors’ discuss observed humeral robusticity, rigidity, and strength differences between African and East Asia hominin populations. The African H. erectus material, including KNM-ER 1808, has previously been attributed to a different species, Homo ergaster. They do not touch on it in the text, but it would be worth discussing the implications of a separate species attribution for the African material in relation to their findings.
Additional comments: Xing et al. have conducted much-needed humeral diaphyseal robusticity and strength comparisons of material attributed to H. erectus sensu lato from Africa and East Asia. The article is well-written, barring the occasional grammatical error. The results, while interesting, must be tempered by acknowledgement of the pathological status of KNM-ER 1808 and the unclear impact this might have on the interpretation of their results. Greater clarity is also required in the methods section when explaining how the Humerus II medullary cavity estimates were arrived at considering the fossil itself was lost and only Weidenreich’s documentation exists. These and other concerns will need to be addressed before publication.

This study comprises largely of direct comparison of values for populations without any statistical analysis. This is understandable due to the small sample sizes; however, Humerus II has been associated with a femur from Locality 1 and KNM-ER 1808 has associated femora. It would have been interesting to perform reduced major axis regressions (a la Ruff, 2009) with the African and East Asian samples to add some statistical power to the evaluations of relative strength proportions in the present study.


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

Input:
Title: MORPHOLOGY AND STRUCTURE OF HOMO ERECTUS HUMERI FROM ZHOUKOUDIAN, LOCALITY 1
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript if very clearly written, in professional English, and easy to follow and understand.  The background and context is adequate, and the tables and figures are professional.
Experimental design: The research hypothesis is very clear.  Due to the nature of the fossil samples, multiple levels of estimation were necessary in order to complete the analysis.  The authors are quite clear about the process involved in these estimation, and provide details on exactly how the estimation was undertaken.  Their commitment to total transparency in this is notable.  While estimations were necessary, they explain them well, and I feel they are justified within the scope of the analysis.
Validity of the findings: Conclusions are clear and robust, and based on the evidence.
Additional comments: In general, this is a clear, well-written manuscript about an interesting and important topic.  Little has been published explicitly quantifying levels of long bone robusticity prior to Neandertals, and this paper will expand this slowly growing body of literature.  I recommend this manuscript for publication with only one small revision:

Please mention somewhere how the KNM-ER 1808 cross-sections were corrected for the periosteal pathology on the long bones of this specimen.  I realize this data was borrowed from Ruff, 2008, but I had to go look up that article to figure out whether or not this current analysis could possibly be affected by the documented pathology on this specimen.  Just a sentence or two in the methods section would spare readers from having to look this up in the original 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: MORPHOLOGY AND STRUCTURE OF HOMO ERECTUS HUMERI FROM ZHOUKOUDIAN, LOCALITY 1
Review round: 1
Reviewer: 3

Output:
Basic reporting: In this manuscript, Xing et al provide an assessment of cortical robusticity (using uCT) from the East Asian humeri of H.erectus (HE) to compare with their African counterparts, and to provide the first anatomical description and cortical data on humerus III from Zhoukoudian Locality 1. They conclude that the humeri of East Asian HE are more robust than African HE, but tend to fall within the lower end of the range of standardized robusticity for more recent hominin samples from the same geographical area.

The paper is well written, detailed, and technically competent. However, I found it to be overly long and descriptive, and had lost interest by the time I had begun reading the results. The material and conclusions could have been delivered in about 1/2 the space, without compromising the scientific integrity or relevant details. I would suggest severely reducing the length of the manuscript, even if there are no page limits in this journal, it is the readers that should be kept in mind.

As an example of places that could be cut, the methods of dating are not germane to the study, only the dates. Readers can move onto the original material on this, on the environmental reconstructions, etc. if they choose to. The anatomical description of Humerus III was also overly detailed for this reviewer - perhaps some of this duplicates Woo and Chia (1954) as well. I would like to see them summarized in graphical format, with labels pointing out the most salient features on the excellent digital photographs in Figure 1. This would also benefit future users of the material for presentations, etc.

I think it is also important for the authors to provide a clearer rationale for the study. Specifically, what new information is gained that was not available before in Weidenreich (1941) + Woo and Chia (1954)? It seems we might have arrived at the same conclusion from reading those two papers without the additional benefit of the uCT cortical data.
Experimental design: Inasmuch as this is mostly an anatomical description of Humerus III and other East Asian HE humeri, the data reporting and experimental design are sound.

I do have two comments, however:

1) I am unclear on why there is a section that reports on standardization by length only (L478-494), and one (more correct) on standardizing by the product of length and estimated body mass? It was not clear why the former was included, since body masses were estimated for the latter anyway? Perhaps I am missing something, but I could not determine the point of the length-only standardization, as all cortical variables were reported in the L*BM standardization as well in the relevant tables.

2) I would like to know why the standardization for length included up to three possible values (even though these varied only by 5.3%), while the mean body mass values were taken as a single value, for the standardization. The BM data, for example on KNM-ER 1808 varies by as much as 40kg. Using Grabowski et al's estimate of 39.5, rather than 60kg mean, would dramatically increase the robusticity of the African HE, putting it much closer to the East Asian hominins. Since much of the results depend on this estimate, it seems more prudent to include a range of values for BM as well as for HL.
Validity of the findings: The findings are valid, to the extent that one agrees with the chosen body mass estimates of Tianyuan and KNM-ER 1808.

For the former, I have a hard time seeing that this individual would be 85 kg with an inferred humeral length of 327mm. By my admittedly quick calculations, this individual would have had a stature around 170cm (Trotter and Gleser 1952, though there may be better ones out there now). This would give this individual a BMI of 29.4, very close to what would be considered obese by modern standards. This is not to say that such large individuals couldn't exist around 40kya, but I personally find this to be a stretch. While on this topic, can the authors speculate on the more than 25% difference in total cortical area between the left and right humeri of this individual? Seems extreme as a R-L asymmetry.

For the latter, see my comments in point 2. I would like to see ranges of body mass estimates here to provide a proper comparison with the other samples.
Additional comments: I have attached an annotated manuscript with some minor editorial suggestions in addition to the above.


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

Input:
Title: MORPHOLOGY AND STRUCTURE OF HOMO ERECTUS HUMERI FROM ZHOUKOUDIAN, LOCALITY 1
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have done an excellent job of addressing the concerns of all three reviewers, and I am satisfied with the response to my own comments. The manuscript reads much better after these edits.
Experimental design: No further concerns, the authors have adequately justified the choice of methods, and the incorporation of multiple estimates of body mass for KNM-ER 1808 is appreciated.
Validity of the findings: No further concerns
Additional comments: Thank you for addressing these comments thoroughly, and for the opportunity to review this 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: COMINIGUT—A SMALL VOLUME IN VITRO COLON MODEL FOR THE SCREENING OF GUT MICROBIAL FERMENTATION PROCESSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well writen and the English is, as far as I can evaluate, appropriate.
Appropriate references have been used and the structure is clear.
However, the article addresses basically two topics; the CoMiniGut and the in vitro fermentation of selected substrates. It would better to discuss these topics in more detail (in particular the CoMiniGut) separately
Experimental design: The manuscript describes the targets and these are in scope with the Journal. The research question is well defined, but not fully achieved as far as the CoMiniGut is concerned. Methods are described in sufficient detail.
Validity of the findings: The novelty is not as much as it could be. In the end, the simulations are pH-controlled faecal batch fermentations, which are assessed after 24 h. While this generates interesting preliminary data on what groups in the faecal microbiota are or are not able to grow in the presence of the tested HMOs, this could have been investigated in more depth as the authors actually suggest themselves in the discussion of the model.
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: COMINIGUT—A SMALL VOLUME IN VITRO COLON MODEL FOR THE SCREENING OF GUT MICROBIAL FERMENTATION PROCESSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript of Weise et al develops a low volume batch system for modelling microbial changes in the gut. The systems low volumes lends itself to sparse compounds. This could therefore prove a useful model. I have a few associated questions for the authors.
Line 115 - FOS often isolated from vegetable sources, rather than enzyme can extraction.
Experimental design: I note that fecal stocks frozen in glycerol; has this been tested to see the loss in viability brought about by freezing? Were fresh samples run side by side?
Were timings kept the same for infant and adult models? Literature suggests adult RT is longer than 24hrs.
Were samples taken at the different times to echo the differences caused by changing the pH? Did this match what would be expected at the colonic regions?
Which time-points chosen - could you have missed peaks in microbial growth?
Validity of the findings: The points raised in 2 would impact on the validity of the findings. However, the authors have related the findings to literature
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: COMINIGUT—A SMALL VOLUME IN VITRO COLON MODEL FOR THE SCREENING OF GUT MICROBIAL FERMENTATION PROCESSES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have answered the concerns I raised in a satisfactory way.
However, I noted that in the description of the basal colon medium, no reference is made to Saulnier et al. 2008 eventhough the article is included in the references, it is not included in the text; I guess it should be mentioned in lines 186-187. Furthermore, I noted there are actually some words in UK English while the overall paper seems to be meant to be written in US English; e.g. 'harboured' (lines 432-434)
Experimental design: No further comments.
Validity of the findings: No further comments.
Additional comments: No further comments.


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

Input:
Title: THE IMPORTANCE OF LOCAL SETTINGS: WITHIN-YEAR VARIABILITY IN SEAWATER TEMPERATURE AT SOUTH BAY, WESTERN ANTARCTIC PENINSULA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well written, clear in the aims, results and in the take home messages. The use of English is correct and the language intelligible. The MS structure conforms to what is expected by PeerJ and the kind of research performed well fall within the Journal aims.

The most important ‘issue’ is that the results are based on local findings recorded in an area, i.e. the WAP, which is extensively studied by the scientific community in terms of climate change. Authors report for the first time (and as far as I know this is really the first time that such data are reported) that in shallow areas summer temperature increase already match levels that at the moment are only predicted to occur in the future. The article is logically and correctly based on this. However, I doubt that there are no other research programs in this area monitoring sweater temperature, at least in deeper waters (e.g. based on the use of oceanographic moorings, see for example here: http://www.soos.aq/activities/soos-at-sea/moorings) and these should be cited/commented.

I would therefore improve the Introduction by placing their study in a wider international and geographical context, and by better explaining and characterising the uniqueness of this dataset (i.e.: “this is the first of ever record of shallow water temperatures recorded in the WAP showing this this and this” or “despite there are several research stations recording seawater temperature in the shallow in this area (say where these are, if any) this is the unique yearlong record available showing this increase”…or “this is so far the unique available temperature record showing this increase”). These sentences will help the reader in understanding the scale of their finding and, in general, will underline since the introduction the importance of studies at the local scale (not only the big picture is important!) as well as the desperate need of more observation in the shallow which are urgently needed.
At the moment I consider the Introduction too brief (although correct) and I would suggest adding these details to complete the background information needed to properly introduce the topic.

The title, despite being clear in reporting the topic of the paper, does not contain any indication that the focus is the Antarctic and, since the fact that “treatments might be just controls” has been documented only here, it would be more correct to adding this information in the title as well in order to give a complete overview of the topic since the beginning.

Introduction, line 45. It is true that Antarctica has been considered one of the most stable environments on Earth but we are now well aware that major changes are occurring in some areas, such as the WAP, as well as that not all areas are warming up at the same speed. Some, such as the Ross Sea, are not warming up at all and show instead a reversed trend. Again, I would suggest completing this brief outline of the current Antarctic climatology taking into account (and referencing) this variability at the continental scale. This info will complete the findings reported in this paper and will underline even more the need to design site-specific thermal experiments in the future.

Introduction, lines 62-63. This sentence is not clear: what do Author mean with “to examine water temperature directly from observations”? Here in situ instrumental records are reported, which are (for sure) not commonly available for most inshore Antarctic environments. On the other hand, in situ measures of temperature are currently and constantly registered by a number of moorings deployed at sea all year-round in off-shore areas (see above link to SOOS). If their intention is to compare the accuracy and reliability of in situ measures vs indirect ones, e.g. those that can be obtained from satellites or remote sensing, this concept has to be better explained. Another point is the general lack of data in form of long-term series…and this is true both for shallow and deep environments. It is reported in Discussion (line 143) that long-term observational data sets in the WAP are limited to a few areas, but Authors do not mention which are these areas and if these data sets are available. It is not therefore possible to properly verify the uniqueness of their dataset.

The findings reported in this paper are about of two summers only and the real temperature trend (if any) is still unknown as well as the real interannual variability. This is implicit in the duration of their observation, but I think that other data about interannual variability for the WAP might be available. I would therefore invite Authors to comment about the possible causes of this variability and, again, if available, report about other projects from the same area.

All the literature cited is relevant.

Figure 1 is clear but I think it would be more useful if also bathymetric contours were included. I have no idea of the water circulation in the area but if any local pattern of is know (and relevant to explain any of the observed variability) This should be commented as well.

Figure 2 is not really necessary but, if considered relevant, add scale bar on Fig. 2B and depth information for both figures in the legend.

Figure 4 shows a series of ‘outliers’ for the station PY2 at -20 m (red dots) at the beginning of February. I have found no comments on this in the MS. Any hypothesis? It is possible that these data are due to instrumental failures or can be interpreted with a temporary introgression of colder waters? Does the general picture change if removed? Please comment on these records.

R scripts, raw data and input files have all been provided by the Authors and the scripts run. There is just a mismatch in the names of files compared to that given in the scripts (files now start with the “peerj-19157-“) but this is not an issue to run the scripts. However, in the final version of the paper this difference should be avoided. Figures do not appear to have been altered in any way.
Experimental design: The registered temperatures have been acquired to answer to a different research question (i.e. which are the responses of Antarctic sponge assemblages to climate change) from the one reported in the paper. Despite this, this is the first time to my knowledge that this topic is tackled in such a clear way and the finding that temperatures expected to occur in the next future are already met is of relevance to a variety of studies. For your info only: there is a specific SCAR group (ANTOS), which will provide protocols for monitoring nearshore environments and, hopefully, in the next future there will be a coordinated network of monitoring stations from which year-round temperature data could be obtained.

The analyses of temperature trends are all necessary, well done and effective in supporting the findings.

The experimental design is very simple and based on the use of HOBO data loggers at three different sites. Despite these loggers are of common use there may be differences in models and sensitivity. Please report manufacturer nominal data about sensitivity and specify the model used in order to allow comparison with other similar data in the future.

M&M line 77. Selected sites cannot be separated by 1.5 meters only. Please correct and report max and min distance between these sites. A scale on Fig. 1 would also help in figuring out the distance between these sites.
Validity of the findings: The data produced in this contribution are of relevance for the whole scientific community working on the thermal tolerance of Antarctic fauna as they indicate that the design of such experiments has to be carefully reconsidered and adapted to local conditions and temperature trend (of which a good knowledge is now required in advance!).
Since the WAP and the Ross Sea, for example, do show opposite temperature trends, with the latter not warming up at all, temperature experiments even on the same species would have to be modified and adapted in order to expose the specimens to temperature that are outside the range of those reached locally. In short, this means that temperature ranges cannot be ‘generalized’ in a ‘one size fits all fashion’ and that the same species might have populations, which have different thermal tolerances.
All these facts increase the complexity of thermal experiments, which will have, from now on, to take into account this ‘newly observed’ variability This introduces a higher level of complexity in studies dealing with thermal tolerance and will represent a challenge for researchers. Given this, I think that this paper is really important.

I would suggest to mention the paper by Ashton et al., 2017 (Current Biology 27, 2698–2705, http://dx.doi.org/10.1016/j.cub.2017.07.048) where ‘dramatic’ changes at the population and assemblage levels were found on settlement panels constantly heated just at 1 to 2 °C above the surrounding seawater temperature. In their experiment the increased temperature has been maintained for about one year, i.e. animals were exposed to higher temperature for a longer time. These two experiments, i.e. Ashton et al., 2017 and the data here presented, both cast new light on this topic and increase our understanding of the effect of climate changes and the need of carefully design thermal experiments.
Additional comments: No additional comments


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

Input:
Title: THE IMPORTANCE OF LOCAL SETTINGS: WITHIN-YEAR VARIABILITY IN SEAWATER TEMPERATURE AT SOUTH BAY, WESTERN ANTARCTIC PENINSULA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript requires more editing. I started to make notes, but pretty quickly gave up as the amount of grammatical issues appeared too large to be handled in a review. Instead, I suggest the authors hire an editor or have a native speaker edited the manuscript.

The figures appear well developed, data are shared.

Article structure is ok, but the article does not test any specific hypotheses.
Experimental design: The study does not test any specific hypotheses. It simply summarizes data from three sites (different location and depth). The site selection does not have any apparent logic (or is related to a hypothesis) and locations are not sufficiently described, i.e., there is no reason to assume that site conditions are comparable, what specific inference scope the sites represent, or what factors are responsible for differences among sites.

Statistical tests indicate whether temperature is constant throughout various times of year, but the results of significant tests are not described in the text. Thus, the results only show that temperatures vary with seasons.
Validity of the findings: A basic assumption appears to be that quantifying the speed of temperature change within the year will provide information about the ecosystem responses to slower temperature changes due to climate change. The authors provide no convincing evidence that this is the case and it appears to me to be unlikely (note that I am not a marine biologist). Instead, it is more likely that organism have adapted to the annual temperature patterns and consequently critical temperature values will vary throughout the year, making the basic assumption invalid. Similarly, the data provide no information that changes in temperature (warming rates) are increasing, making a discussion about “heat shock” pure speculation (lines 161+). Why is the difference in warming rate before and after October relevant, is the difference even significant? In the same context, the data provide no information which site conditions are indicative of higher and lower environmental variability (lines 175+).
Additional comments: The general argument that experimental conditions should reflect natural trends makes sense, but is not new. The data at this stage are not sufficient to support the conclusion of the study. A better description of the sites and longer measurement period may be necessary. Alternatively, the data can provide a baseline for comparison with future measurements.


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

Input:
Title: THE IMPORTANCE OF LOCAL SETTINGS: WITHIN-YEAR VARIABILITY IN SEAWATER TEMPERATURE AT SOUTH BAY, WESTERN ANTARCTIC PENINSULA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors clearly and professionally report their methods and findings in the present manuscript in which they report the temperature variation at three sites around Dourmer Island, Palmer Archipelago, WAP over the course of one year to better understand local variation and inform experimental set point in climate change experiments.

The authors present multiple figures describing the temperature dynamics, however I think that some of the figures depicting the raw data measurements might be better suited to be included as supplementary material. It seems like the same data are depicted in multiple graphs and it is unclear to me as written, what the added value is for including each of these figures. Perhaps more detailed description and interpretation would help put these different figures into context. Otherwise, maybe consider including some of these figures as supplementary material. The map (Figure 1) is very helpful in putting the present study site into geographical context.

The premise that temperature treatments should be put into a local context of exposure is extremely important. However, I think that the relatively narrow focused area observed somewhat geographically limit how applicable these results will be to other studies outside of this geographic region. Maybe some additional information on percent and duration of sea ice cover might help other researchers better gauge how applicable the results in the present study are their region of interest. They cite Schram et al. 2015, who appears to have data mined the Palmer LTER site for additional sea surface temperatures (range similar to that reported here). Perhaps the inclusion of this type of freely available data could add some weight to the data presented here?
Experimental design: The research presented is within the scope of the journal and their research question is well defined, relevant and meaningful – particularly in light that it appears that not all studies take local conditions into account when setting experimental levels for climate change experiments.
Validity of the findings: While I agree that it important know something about the local exposure of your experimental organisms, this information is not always available and therefore I would recommend caution when discussing the temperature levels used in previous experiments. I also believe that the authors could perhaps include some additional discussion on why studies that expose organisms to different temperatures are/are not still informative in the light that organisms may briefly experience those temperatures.

The authors point out that for their one year of data, organisms were exposed to “temperatures of more than 2.5C for more than 10 days within a year and over 2.0C for more than 25 days, temperatures that have been used experimentally to test responses to acute heat stress” (lines 124-126). I am not convinced that this is sufficient exposure to call these temperatures a control temperature. These elevated temperature days do not appear to have all occurred within the same week, therefore this may still be at the extreme temperature range of what organisms experience. Perhaps some additional justification is needed here? As it stands, I do not agree that the data presented for this one year study is sufficient to make the case that all Antarctic organisms experience these temperatures often enough to call this another control temperature.
Additional comments: When listing citations, if not an exhaustive list, perhaps precluding the list with"e.g."


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

Input:
Title: THE FRENCH PRESS: A REPEATABLE AND HIGH-THROUGHPUT APPROACH TO EXERCISING ZEBRAFISH (DANIO RERIO)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study proposes in a clear and a well-grounded way a novel, cost-effective and high-throughput method for exercising zebrafish, using a coffee plunger and magnetic stirrer. The introduction has a good scientific background and makes the study’s aim clear, in addition to being well-contextualized regarding the literature. The study was developed and discussed so that it answers the main questions that were proposed. The structure of the text and the format of the figures are in accordance with this journal’s norms and the authors supplied enough data to understand the results analysis. There are, however, some minor shortcomings as follows:
Experimental design: a. Bearing in mind that this study aims to standardize a new technique using animals and this kind of study is very sensitive to various interfering factors, it is paramount to add a “Zebrafish maintenance” paragraph in the “Materials and Methods (line 70)” section, detailing: the strain, age and nourishment of the zebrafish; the water control parameters; light/dark cycle. It is also important to add the ethics committee approval for the use of these animals in the experiments.
b. Please include the time of the day in which the “Maximal swim performance (line 90)” and “Exercise training (line 101)” were conducted.
c. Please add the French Press brand used in the tests (line 72).
d. In the “Maximum swim performance” section (line 90), what was the method of weighing, sexing and measurement of the animals?
e. In the “Exercise training” section (line 101), how long after the “maximal swim performance” test were the animals taken to the following “pre-intervention maximum swimming speeds” test (hours, days etc.)?
f. The authors should provide a better explanation on how the effects of exercise training were assessed (line 149-151), at the end of the 5 days of the swimming regime at a sub-maximal exercise speed, to evaluate the difference in relation to the control group.
 g. As the study has different stages, the methodology would be clearer if a figure were added with a timeline to better express the events, at the authors’ discretion.
Validity of the findings: a. Both the statistical analysis and graphs seem adequate for this type of study.
b. In the results section is described “Maximum swimming speed significantly increased in the exercise-trained, but was unchanged in the control group (lines 149-150)”. It would be interesting to include a graph of these data.
c. Although the authors wrote a conclusion at the end of the discussion (lines 201-203), it would be appropriate to emphasize the conclusion, by writing a conclusion section in a new paragraph.
Additional comments: Taking into consideration that this study proposes an innovative method that could be used in different approaches, I consider this article relevant to be published after improvements are made.


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

Input:
Title: THE FRENCH PRESS: A REPEATABLE AND HIGH-THROUGHPUT APPROACH TO EXERCISING ZEBRAFISH (DANIO RERIO)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript describes improvements to existing exercise protocols for zebrafish and proceeds to investigate the repeatability of the measurement approach. The manuscript also reports to investigate improvements in maximum speed following exercise training, mass increases following training, and the effects of sex and length on the results. Most of the results are missing from the manuscript and those that are present are largely reported in supplementary tables.

1)	In order to address this the results relevant to each of the questions listed above need to be included in the main text.

2)	Data investigating the similarities between different plungers can be moved to the supplementary data
Experimental design: In the methods it is reported that 40 fish were measured.

1)	Given that multiple questions were asked this should be further explained to give the n number for each experiment. For Example to look at the effects of sex and exercise there was only 10 fish in each group.

2)	A single experiment with n=10 was carried out to address the questions raised. It is not clear if this is sufficient power to detect the effects proposed. The authors need to justify the size of the experimental group based on power analysis to indicate the level of change in swimming speed, mass etc, they are able to detect If the number of fish is insufficient the experiments should be repeated with greater numbers to support the findings.

3)	The repeatability was assessed by using measurements pre and post-exercise training. It is not possible to use the same data to assess repeatability as the training could induce a difference. Repeatability should only utilise the unexercised fish.

4)	For the analysis of water speed and stirrer speed using different French press units, 2 units is not sufficient to say there is no variation between units, and additional measurements are required. Standard practice would suggest a minimum of 3 but given that the authors have access to many more they are encouraged to increase the number significantly.

5)	The make and model of the coffee plunger used should be supplied in the methods section.
Validity of the findings: The authors introduce a useful advance on the previous exercise approaches for zebrafish. The conclusions regarding the effects of exercise however, are questionable given the low number of fish utilised and the lack of experimental repetition.

It will be vital to demonstrate that the experiments were sufficiently powered to address the questions raised to demonstrate the validity of the findings.
Additional comments: No additional comments


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

Input:
Title: THE FRENCH PRESS: A REPEATABLE AND HIGH-THROUGHPUT APPROACH TO EXERCISING ZEBRAFISH (DANIO RERIO)
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Thank you for making the proposed changes.
I consider that your article is now much more clear and elucidative.
Therefore, the article is ready for publication.


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

Input:
Title: THE FRENCH PRESS: A REPEATABLE AND HIGH-THROUGHPUT APPROACH TO EXERCISING ZEBRAFISH (DANIO RERIO)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The new figure (Fig2) presenting the change in swim speed with exercise is a very useful addition. However, measurements from individual fish should be presented to allow visualisation of the variation, which is currently hidden by only presenting the estimate from the mixed model? (presumed, not given in figure legend) and standard error bars rather than standard deviation or confidence intervals.
Experimental design: The reviewers have made some changes as a response to the previous review but some key concerns remain to be addressed.

The clarification of n numbers and variables in the mixed model is an improvement.
However, the response to the question of sample size has not addressed the concern.

The authors are correct to suggest that post-hoc power analysis are not ideal, but it is still critical to ensure that sufficient animals have been examined. The authors themselves have previously published on the important of prospective power analysis, and if they are not willing to conduct a post-hoc analyses then details of the prospective power that determined that n=20 would be sufficient.

The authors also state that the sample size was sufficient to detect an improvement in swimming speed in the experimental group. This does not indicate that sufficient numbers were present in the case of sex, length, or mass where the effect may be less. Furthermore, for the effect of sex on exercise response there were only 10 exercised males and 10 exercised females (n=10).

Identifying issues with post-hoc analyses is not sufficient address the concern that the number of animals in this study is probably too low to identify effects which must be addressed. The lack of experimental repetition has also not been addressed and there is no indication in the methods that experimenters were blinded to treatment group.
Validity of the findings: Given the lack of justification of the number of animals examined, lack of experimental repetition, and the fact that observers were not blinded to treatment group there are still concerns over the validity of findings.
Additional comments: Overall this is an interesting method that is of interest to the field but the examination of the effect of exercise on maximal swimming speed is not conducted with sufficient numbers and experimental repetition to address the questions raised.


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: ALPHA-ACTININ OF THE CHLORARCHINIOPHYTE BIGELOWIELLA NATANS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, Backman follows up his previous work on microbial alpha-actinin. This paper analyses the first example of an alpha-actinin from a photosynthetic organism that I'm aware of. The aim of the paper is well stated and generally the manuscript is written in a clear and engaging manner. The manuscript is well structured and well presented.

In terms of reporting the current data, I have some points for the author.

1.1 It would be helpful to include a table of Pfam and Smart E-values for the domain assignments alongside the Superfamily data already given in the text. The spectrin triple helix in the rod domain is clearly very divergent, as the author indicates. It is not recognised by Pfam or Smart as far as I can tell, and this is a worthwhile point to bring out.

1.2 On the same issue, I think it would be appropriate to put in a sequence alignment of the triple helix in the rod domain with those of Entamoeba histolytica, and S.pombe alpha-actinin, and representative repeats of one (or a few) four-repeat actinins.

1.3 Am I right in thinking that this is the first alpha-actinin that has just one spectrin repeat to be experimentally characterized? If so, I think this should be brought out more clearly in the text. This is particularly important in terms of the mechanism of dimerisation. In other alpha-actinins, dimerisation occurs by interaction of R1 with R2 or R4 (depending on the number of repeats). This alpha-actinin presumably dimerises by homotypic interactions of a pair of R1-equivalents. This should be stated clearly, and used to qualify the abstract (line 29:"all common characteristics of a typical alpha-actinin).

1.4. It would be helpful to include a diagram to indicate where Bigelowiella sits in eukaryotic phylogeny, and how its structure relates to other alpha-actinins.
Experimental design: The experiments are designed generally very well and reported in a way that would enable reproduction by another worker.

2.1. It would be helpful to explain a little further how the assignments for the beginning and end of each domain construct were made. I assume these were essentially from the superfamily assignments? The construction of the rod domain is reasonable, but I wondered if the author attempted to make other constructs of the triple helix that would be soluble? It's generally the case that triple helical repeats can be prepared in soluble form providing the phasing of the repeat is correct and there is a minimal number of residues at the end of the construct. In that sense I am not surprised that the rod domain construct was insoluble.

Major point
2.2. It is characteristic of alpha-actinins that they dimerise. The author correctly states that a dimeric alpha-actinin should bundle actin filaments, and this is indeed observed. But it does not prove that this alpha-actinin is a dimer. In order to substantiate the author's contention that this alpha-actinin is indeed a dimer (e.g. line 26 - "probably forms anti-parallel dimers"), I think it is important that this should be directly investigated. The gel filtration data in figure 2 indicates that unaggregated alpha-actinin can be obtained from the column. In my view, the author should analyse this for the oligomeric state of the protein. There are numerous biophysical methods that could be used for this, or alternatively chemical cross-linking and gel electrophoresis. In this context, given that the alpha-actinin has a tendency to aggregate, the results shown in figure 6 and figure 7 for bundling actin could result from aggregation of the protein rather than specific dimerisation. The author is correct to point to the tendency of the full length alpha-actinin to aggregate in the conditions used for the bundling assays, therefore the dimerisation is not proven.
Validity of the findings: Subject to my concerns in point 2.2, the data seem entirely valid. The protein clearly has functional actin-binding and Ca2+-binidng domains, characteristic of alpha-actinins. The structural modelling of the domains seems good (and for my own interst, I obtained the same results using Phyre).
Additional comments: Overall, I think this is a generally very helpful study of a microbial alpha-actinin from a novel class of organism. The author is to be commended on the clarity of the paper and the direct and straightforward experimental design. However, I think the author should directly address my point 2.2 before this paper could be published.


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

Input:
Title: ALPHA-ACTININ OF THE CHLORARCHINIOPHYTE BIGELOWIELLA NATANS
Review round: 1
Reviewer: 2

Output:
Basic reporting: With the exception of a few minor errors the article is well written and referenced and the data are appropriately presented.
Experimental design: The research question is well defined and the experimental design is appropriate and well documented.
Validity of the findings: The number of times that each experiment was performed needs to be stated in each figure legend.  This is important so that the reader can easily assess the reproducibility of the data.

Statistical analysis has been performed where appropriate.
Additional comments: The manuscript represents a thorough analysis of the a-actinin like protein from Bigelowiella natans.  Given the interesting phylogeny of this organism, this analysis has some significance in terms of understanding the evolution of the actinin family of actin cross linking proteins.  Overall the experiments are executed carefully and interpreted appropriately.

I would recommend publication upon completion of the following minor revisions.

Line 76 typographical error: isolatiOn
Line124/125 reference needed for sentence ending …. as before.
Line 199/200/201 This sentence is repeated in Line 212/213 – it seems a bit redundant to describe this in both places.
Line 219 change reliable to reliably.
Line 333 change a-actinin to alpha-actinin
Legend for figure 2: Use rcf rather than rpm when describing centrifugation conditions
Each figure legend containing experimental data should state the number of times that the experiment was performed.  For example:  “Data shown is representative of 3 independent experiments.”  This is important so that the reader can easily assess the reproducibility of the data.
Figure 6: It would be useful to present the quantification of the co-sedimentation data.  For example, plotting the proportion of actin in the pellet against actinin concentration in a line graph.


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: ALPHA-ACTININ OF THE CHLORARCHINIOPHYTE BIGELOWIELLA NATANS
Review round: 2
Reviewer: 1

Output:
Basic reporting: OK
Experimental design: OK
Validity of the findings: OK
Additional comments: The issues raised in my review of the manuscript have been adequately addressed in the revised version.