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: DETECTION AND VISUALIZATION OF ABNORMALITY IN CHEST RADIOGRAPHS USING MODALITY-SPECIFIC CONVOLUTIONAL NEURAL NETWORK ENSEMBLES
Review round: 2
Reviewer: 1

Output:
Basic reporting: It is perceived in this revised version of the manuscript that the authors attend the major question demanded in the evaluation of the first version. The authors provided a more clear justification for the main questions and salient the contributions of the work.

Then I consider that some minor questions (listed below) should be attended to allow the acceptance of the work:

a.	About class weight for the imbalance issue, the authors should cite at least one strong study to prove the efficiency of this kind of approach, I saw it specification only in practical issues and I consider it a little dangerous to rely just on the implementations without a deeper investigation if there are other recognized approaches to treat the imbalanced data. This issue is very pertinent for the success attained by the work and for the proposed approach;

b.	In relation to this question: “Q12. In ensemble CRM is not clear how the CNN models complement each other if there is some disagreement with the different models? How the aggregation of this supposed discordance of the individual architectures to compose a final suggestion works? For example, if there is a more precise CNN model, why I have to believe in a CNN model that disagrees with this decision? It is suggested to authors provide more elements and better explanations to justify this question.”, I do not see an explicit manifestation of the authors in the text to provide improvements in relation to this question;

c.	I consider the questions: “Q18. It is not clear the methodological process applied for evaluating the ROI of abnormal images (RSNA pneumonia). The figures 10 and 12 (in the first version of the manuscript) demonstrated didactics aspects but should be specified if this evaluation was done under the 17833 abnormal images from the dataset. And what was the success rate obtained from this set of images?” and “Q20. …What justifies these differences? Why just this metric is presented, and mAP?” until unclear and I believe that the authors could explain in more detail to clarify this question. I understand that the reported values for IoU and mAP are the maximum reached, but how representative are the values reported in tables 7 and 8 in terms of the expected range of them? For example, if the range of them is the interval [0.1 0.6], the 0.383 for IoU or 0.377 for mAP to VGG-16 reported in table 7 or a 0.433 for IoU or 0.477 for mAP to ensemble-5 in table 8, not seems very good values. And, in figure 11, the example provided for individual or ensemble CRM not reflect the values reported in tables 7 and 8. How was reached these superior values of IoU presented in the example (sometimes superior to the range 0.6) in figure 11 for individual and ensemble CRM?

d.	I suggest an improvement in the conclusion section, I see several evidences that conduct for extension of this work in future works, like for example a comparative with salient maps method for visualizing, or the extension of another test data set not related to only an abnormality, like pneumonia. But the authors did not mention any future strategy.
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: DETECTION AND VISUALIZATION OF ABNORMALITY IN CHEST RADIOGRAPHS USING MODALITY-SPECIFIC CONVOLUTIONAL NEURAL NETWORK ENSEMBLES
Review round: 2
Reviewer: 2

Output:
Basic reporting: 1. I appreciate the continued efforts the authors have made to improve this work. The clarity of the methods used in the manuscript are substantially improved.

The additional captions on the tables clarified a number of my questions. The improved figures, especially those highlighting how ensemble CRMs can improve performance, are helpful.

The suggestions provided by Reviewer 1 and implemented by the authors have further strengthened the literature review.
Experimental design: 2. Re: significance testing. I did not understand the authors' reply about cross-validation. I am not suggesting that cross-validation be performed. Significance testing for AUCs can be performed with the predictions they have already generated on a fixed test set. For an example, see Gulshan et al providing confidence intervals for an ROC curve:

https://jamanetwork.com/journals/jama/fullarticle/2588763

and see testing available in in

https://cran.r-project.org/web/packages/pROC/pROC.pdf

In the machine learning literature, it is unfortunately standard to report results without any statistical testing. Given that this work is oriented towards the medical/biological community, I believe significance testing -- at least of the core claims asserted in the conclusion -- is needed. It is not obvious to me that an experimental AUC of 0.97 (ensembling classifier performance on Chexpert test) is truly superior to an AUC of 0.96 (VGG-16 performance on same), but it is claimed that ensembling improved classification performance in the paper. There should be a statistic to back up each of these claims made in the conclusion:

"The combination of modality-specific model training and ensemble learning helped to: a) transfer modality-specific knowledge that is repurposed to improve classification performance in a similar task; b) reduce prediction variance, sensitivity to the training data, and model overfitting; and, c) improve overall performance and generalization. The proposed strategy shows improved performance and generalization as compared to other non-ensemble methods."

3.  As excerpted above, the authors assert that both modality-specific model training and ensemble learning offered a range of benefits. I believe they now show that ensembling offers benefit for generating more reliable bounding boxes and possibly classification performance on their data, but I still do not find their claims credible that modality-specific model training offers any benefit.

The authors are fine-tuning a classification model twice -- once on Chexpert data, then separately on RSNA data. The results in table 5 do *not* support that there is a benefit from this procedure. They compare 'baseline' model performance (ie, ImageNet-initialized, then fine-tuned on Chexpert data only) to 'fine' model performance (i.e., ImageNet-initiailzed, then first fine-tuned on Chexpert data, then fine-tuned on RSNA data).

Their results are consistent with there being a benefit from fine-tuning on RSNA data. This is not surprising, since the classification task is different. Normal/abnormal classifications based on Chexpert evaluates for a wider set of pathology than RSNA, where normal/abnormal only evaluates for pneumonia. It is entirely expected that fine-tuning on more accurate labels would improve performance. (This fact needs to be addressed by the authors in the Discussion.) This does not demonstrate any benefit from first fine-tuning on Chexpert data.

If the authors wish to claim that the modality-specific model training pipeline of fine-tuning twice on separate datasets with different labels offers value, they would need to include a new category in Table 5 for each type of CNN for a model that was initialized to ImageNet pretrained weights and then only fine-tuned on RSNA data. That could demonstrate that initializing to the Chexpert fine-tuned weights helped them learn a better solution than initializing to ImageNet only before fine-tuning. Otherwise, this claim is not defensible. This is a core claim of the paper, so it is very important that it either be convincingly made or removed.

It would also be helpful to use the same terminology of 'coarse' instead of 'baseline' in Table 5 so that 'coarse' and 'fine' can be contrasted.

4. Related to the above - since the model is again fine-tuned on RSNA data, comments about generalization ("improved generalization in transferring knowledge") should not be included, as there is no real test of generalization being performed. Only if there were a new test dataset that was not used for training could we really assess generalization.
Validity of the findings: 5. Overall, I think the strongest part of this work as it stands is demonstrating that ensembling can be useful for creating better CXR saliency maps, and possibly classification performance if statistical testing bears it out.

I believe that this contribution is obscured by the complexity of the pipeline created to facilitate modality-specific model training. My primary remaining concern is that claims about the benefit of the modality-specific training be either substantiated or removed, as discussed above.
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: DETECTION AND VISUALIZATION OF ABNORMALITY IN CHEST RADIOGRAPHS USING MODALITY-SPECIFIC CONVOLUTIONAL NEURAL NETWORK ENSEMBLES
Review round: 3
Reviewer: 1

Output:
Basic reporting: I consider the authors provided satisfactory answers to my questions and clarify some points obscured in the previous version.

The question about class weight was attended with the addition of pertinent literature.

In relation to ensemble CRM was provided a better explanation that helps the reader to understand the superiority of the ensemble strategy.

Although I consider 20% to test few samples to be evaluated, the authors provided a better explanation for the readers.

Additionally, the authors follow the suggestion from Reviewer 2 with the inclusion of confidence intervals.

In relation to the rates for IoU and mAP, was clarified the determination from the precision-recall curves. However, I consider that this explanation "We agree to the fact that some images have the IoU scores superior to the range 0.6 because this score quantitatively indicates the degree of overlap between the bounding box surrounding the detected ROI and the ground-truth bounding box" should be incorporated into the manuscript to avoid miss interpretations.
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: DETECTION AND VISUALIZATION OF ABNORMALITY IN CHEST RADIOGRAPHS USING MODALITY-SPECIFIC CONVOLUTIONAL NEURAL NETWORK ENSEMBLES
Review round: 3
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Thanks again to the authors for their detailed and thoughtful revisions of their manuscript. These revisions constructively address my previous concerns, and I recommend acceptance of this manuscript in its current form.


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: CLIMATIC VARIATION IN AFRICA AND EUROPE HAS COMBINED EFFECTS ON TIMING OF SPRING MIGRATION IN A LONG-DISTANCE MIGRANT WILLOW WARBLER PHYLLOSCOPUS TROCHILUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English language should be improved in several places to ensure that an international audience can clearly understand your text. Some examples where the language could be improved are given below. The current phrasing, particularly in the field methods section, makes comprehension difficult.
The introduction should show a stronger red line with transitions between facts.

The manuscript includes sufficient introduction and background and demonstrates how the work fits into the broader field of knowledge. Relevant prior literature has been appropriately referenced. The introduction has parts with excessive citations and the selection of the references cited is rather arbitrary. The discussion is excellent.

The structure of the article conforms to an acceptable format of ‘standard sections’.
Regarding the figures, I would suggest to exchange Figures 3 and S3 since Fig. S3 seems more important to a broader audience than Fig. 3.
Figures in the text are appropriately labelled. All appropriate raw data have been made available.
Figure S1 should, if possible, be included in the main text as it contains interesting and relevant information necessary to calculate the indices.
Figures S2 and S3 need a heading and a very short description. Likewise, Tables S1-S4 need a caption and/or a short description of what is shown. Specifically: Table S2: What has the Chi-square test been used for?

The submission is ‘self-contained,’ represents an appropriate ‘unit of publication’, and includes all results relevant to the hypothesis.
Experimental design: The submission is original primary research and clearly defined the research question, which is highly relevant and meaningful. The knowledge gap being investigated has been clearly identified, and statements has been made as to how the study contributes to filling that gap.

The investigation has been conducted rigorously and to a high technical standard. The research has been conducted in conformity with the prevailing ethical standards in the field. However, please see my concerns in parts of the statistical methods (described below).

Methods have been described with sufficient information to be reproducible by another investigator. All method descriptions are very comprehensive and allow a full understanding of the field and statistical methods. I am confident that the authors have a comprehensive dataset that is well suited to answer their questions
Validity of the findings: This study will have a high impact in the field and explores the novelty of examining several climatic indices on various scales at the same time.

The data on which the conclusions are based have been provided. The data seem to be robust, statistically sound, and controlled.

The conclusions have been appropriately stated, are connected to the original question investigated, and are be limited to those supported by the results.
Additional comments: General comments:
The authors tried to relate the arrival of the willow warbler to different local and distant climates. The topic is highly interesting and results will contribute substantially to the understanding of a widely observed phenomenon. I commend the authors for their extensive data set, compiled over many years of detailed fieldwork. I generally also like the idea of the calculation of the AA value, especially regarding the options of comparability among other regions or species.
However, I have some serious statistical concerns that I described in detail below. Main points include the model selection strategy, the way and time collinearity has been assessed, the absence of precipitation considerations, the relation of number of observations to number of parameters (n = 34, k = 14), and model reporting. I am giving examples and advices including literature for further read below.
Furthermore, the English language should be improved in several places to ensure that an international audience can clearly understand your text. Some examples where the language could be improved are given below. The current phrasing, particularly in the field methods section, makes comprehension difficult.
Abstract:
The abstract is well written, very informative and makes the reader curious. I would probably delete “(minimum AIC)” after the best model as I believe that this is common knowledge and if not, it can be read in the methods part. (see my concerns about the use of AIC)

Introduction:
While this section is very comprehensive, some parts rather read like a concatenation of facts than a story (in contrast to the discussion, which has a better storyline). The authors may want to consider better transitions among the facts to allow an improved story flow. Also, I would suggest to avoid excessive citations (see below).
Lines 50-52, 53-56 and 58-60:  Such excessive citations make it hard for readers; Moreover, there are many more papers investigating migratory birds and timing, or response to NAO; I would suggest to cite a few that deal with many species and write “e.g.” before; otherwise the selection of the paper cited would seem a bit arbitrary.
Line 57: not only winter, also annual indices have been used (e.g., Møller 2002, Grimm-Seyfarth et al. 2015)
Line 61: “explained” instead of “explains”
Lines 106-109: It seems that this formulation is a bit misleading. My suggestion would sth. like: “We aimed to examine whether the time of spring migration of the willow warbler at the Baltic Sea coast had responded to large-scale climate variables affecting the wide non-breeding grounds in the year before migration.”

Materials & Methods:
This section is again very comprehensive and allow a full understanding of the field and statistical methods. I am confident that the authors have a comprehensive dataset that is well suited to answer their questions. However, the English language should be improved in some parts of the section to ensure that an international audience can clearly understand your text. Some examples are given below. The current phrasing makes comprehension difficult.
The statistical part is particularly well described and not many language improvements are necessary here. It is written in clear and understandable language. However, I have a few serious questions and concerns regarding the statistics:
(1)	My first question is why the authors focused local climate on temperature only. First, the climate indices also represent various climatic factors and not just temperature. Second, rainfall, and even the interaction between temperature and rainfall, might have a strong influence on the appearance of the birds as they influence both their habitat and their food. If data are available for the weather station, I would encourage the authors to include rainfall and temperature-rainfall-interaction into the parameter set.

(2)	A second question that came to my mind is whether all those climate indices could be correlated with each other. A statement on correlation of the values of the indices used in the model would help here. In general, it can be quite critical to use a multiple regression model with several indices that could potentially affect each other (and also local temperature or the “year” variable), even if a correlation is not directly detectable. The authors should make clear that this does not violate any model assumptions. (NB: See my detailed comments below; I figured that come tests have been conducted, but AFTER model selection, but model assumptions need to be checked BEFORE model selection)

(3)	The authors only considered linear effects of the indices, while others have already shown that indices can have a quadratic influence (e.g., Møller 2002, Grimm-Seyfarth et al. 2015 for NAO). To my understanding, migration conditions might either become optimal toward one side of an index (linear relation) or around a specific index value and might get worse both above and below it (quadratic relation). A simple AICc comparison of AA against an index linearly or quadratically would solve this question.

(4)	I have some substantial remarks regarding the model selection, reporting and model fit sections which I describe below in details. Particularly, the confusion of the authors between “all-subset regressions” and “backward selection” need to be clarified. See below.

(5)	A LM with 34 observations and 14 explanatory parameters is extremely challenging and can easily overfit the model. I am not sure whether the use of “date of first capture per individual per year” as a response in a mixed model (using “Year” as random intercept) would not be more appropriate instead of using the AA value, even if I like the idea of the AA value as a nice single value that describes the behavior of the whole population. In addition, adding rainfall and temperature-rainfall interaction would add two more parameters. A possible alternative approach would be the following:

a.	Choose parameter subsets, for example regarding the season or regarding the index (e.g., all values from spring, all from summer, all from winter; or all NAOIs, all SOIs etc.; no index doubling among subsets)
b.	Conduct model selection on all possible parameter combinations per subset (NOT backward selection)
c.	Put the “best parameters” per subset into a final “global model” and perform model selection on all possible parameter combinations

Specific comments:
Lines 113-115: This sentence needs some clarifications: I guess the information is available at the Baltic Sea cost? So is the Baltic Sea the final breeding ground or another stopover area? If first, I would suggest to remove “to northern Europe”, if the latter, I would suggest to add “at the stopover site xxx”. (NB: I realized it is the latter when reading the text further, but the first sentence is confusing).
Line 119-120: This sentence is again confusing
L126: please add: in Africa
L128: replace “so we use” by “which is why we use”
Climate indices section: The climate indices are well described und understandable even when not working in the subject area. However, I would suggest to either mentioning them in the beginning (but this will add a bit of text – despite the abbreviations could be used when explaining their effects further on), or show them in a table (e.g., Name, Abbreviation, part of Africa or Europe they have an influence on). This could make it easier to follow (and to have a look-up when continuing in the text).
L 173: Could the authors please explain whether the temperatures from Leba represent temperatures in Bukowo? Has there ever been comparative measurements? Or does it experience the same geographic conditions? The distance of 95 km sounds rather far.
Line 174-176: Could the authors give a brief overview on the behavior of temperature across the 40 years? Where they increasing and if so, how much on average or how much per year?
Lines 182-185: Where the averaged indices NAOI April-May and NAOI November-March and NAOI August-October correlated with each other? It is a rather “slow responding” index so I could imagine it does not change much from summer to winter or from winter to spring. The same holds for other indices averaged across several seasons. A few words (if or if not, and if so, what have the authors done) would help here.
Lines 209-210: The method used is very valid and known, I believe that the two most important references are sufficient.
Line 233: The authors describe that the year and the 13 climate variables were used in the same LMs. Did the authors test for correlations of the indices and the year as I would assume that at least temperature could be related to the year, but even indices could advance or delay over time.
Line 237-238: Even if it is convincing to read that the authors know what they would need to do in the case of autocorrelation, if is not necessary to state this here, as the autocorrelations were not significant in your case.
Lines 245-246: This part is extremely important and I am waiting for it since the description of the climate data. I would suggest to move it to the end of the climatic section. That way, the question about potential collinearity is explained earlier. Moreover, I am missing the results for the collinearity analyses which are needed before heading on to the LM description.
Line 249: The authors claim to use “all subsets regressions”, which is not true if they also state that they used stepwise backward selection. I have had a look at the R code and figured that indeed backward selection has been used. One can do either all subsets or stepwise regression (such as backward or forward selection), but this describes two different approaches. Mundry 2011 and, more recently, Harrison et al. 2018 have reviewed different model comparison techniques and came to the same conclusion that any stepwise selection should be (and has been in the literature) “heavily critisised“ (Mundry 2011) and “ranking via AIC of all competing models is preferred” (Harrison et al. 2018). Therefore, I would strongly recommend the authors to redo the model selection part using all subset regressions (a personal hint: the R-package MuMIn has a function called “dredge” which should do a good model selection using all possible model combinations; different ICs are possible).
Line 250: with 34 observations only, the AIC value is not giving appropriate values and the use of AICc should be preferred.
Line 253: the R² value is a model fit value which can be calculated for LMs. However, as Harrison et al. 2018 summarised, even a high R² value does not necessarily tell us anything about the validity of the model. Further model fit measures are recommended (e.g., does the global model meet all model assumptions for an LM? Did the authors inspect residuals?). Another idea for the proportion of variance explained by each variable could be hierarchical partitioning (Lee and Nelder 1996, see package hier.part in R).
Lines 255-258: Multicollinearity should be assessed with the global model, not with the best model. Existing correlations already affect model selection not just the results and parameter estimates (I am citing Harrison et al. 2018 again, as this is a review and will lead you to further literature if needed). One can either test it with correlation tests (see my comments above to lines 245-246 for which results are missing) or with VIFs (but with all parameters, not just the ones in the best model). It is not necessary to do both.

Results:
The results are well presented. A figure showing the direct relation between AA and the best indices would improve the presentation of the results further. Model reporting including estimates is missing, preferably from the global model (Harrison et al. 2018). So far, readers get no idea on the direction of the effects.
Specific comments:
Line 272 and Fig. 1 suggest that 1989 has the lowest AA value. I do not understand this statement as both Fig. 2 and Table S1 suggest that the values of 2000 and 2012 are even lower (-5.28 compared to -6.02 and -5.94, respectively). Please clarify.
Line 276: please consider again that the analyses are not all-subset regressions
Line 279: multicollinearity should be checked before model selection and thus can be reported in the methods or in the beginning of the results
Line 281: It seems that the correlation coefficients have been reported (sorry for stating above that I did not find them), but again for the best model and not for the global model. This is confusing as I understood from the methods that correlation tests were done before model comparisons which is also why I was missing the results. Correlation tests of the final (“best”) model are meaningless as a correlation between two variables would violate model assumptions. Please note that a test for correlations should not only include the indices among each other, but also each index against year. Last, could the authors please explain why they retain the “year” in their model set (in the method section)?

Discussion:
The discussion is very comprehensive and discusses the different times and locations of the indices. The authors put a lot of effort in comparisons and explanations which I highly acknowledge. Some parts may even be a bit long, but I personally do not mind this too much. Some parts could also profit from slight language improvements.
Specific comments:
Lines 313-314: citation missing from other European studies mentioned
Line 376: I assume that the authors mean “a high abundance of insects”?
Line 494: this is the first time Fig. S3 is mentioned, while it would be worth mentioning every time the discussion or results describe one of these indices. I would suggest that this figure should best be included in the main text (results section) and is more important for readers than the current Fig. 3 which can be placed in the appendix instead.
Line 539: last letter, “t” – “the”?
Line 541: please insert “be” between would and easy
Line 543: “and to update annually” – it is not clear to me whether the AA index, the baseline or the database itself should be updated

Literature cited:
Grimm-Seyfarth, A. et al. 2015. Earlier breeding, lower success: does the spatial scale of climatic conditions matter in a migratory passerine bird? Ecol. Evol. 5: 5722–5734.
Harrison, X. et al. 2018. A brief introduction to mixed effects modelling and multi-model inference in ecology. PeerJ 6:e4794.
Lee, Y., and J. A. Nelder. 1996. Hierarchical generalized linear models. J. R. Stat. Soc. Series B (Methodol.) 58:619–678.
Møller, A. P. 2002. North Atlantic Oscillation (NAO) effects of climate on the relative importance of first and second clutches in a migratory passerine bird. J. Anim. Ecol. 71: 201–210.
Stephens, P. A., S. W. Buskirk, and C. Mart ınez del Rio. 2007. Inference in ecology and evolution. Trends Ecol. Evol. 22:192–197.


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: CLIMATIC VARIATION IN AFRICA AND EUROPE HAS COMBINED EFFECTS ON TIMING OF SPRING MIGRATION IN A LONG-DISTANCE MIGRANT WILLOW WARBLER PHYLLOSCOPUS TROCHILUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is clear, though the discussion is a bit tiresome and not very well organized (also within subsections).

Figures and tables lack headings and are not understandable without refering to manusctipt.

Bird raw data (subject of research) are not provided, but only some final statistics.
Experimental design: Problem of sample size which makes estimation of the lower part of the cumulative arrival curve unreliable. There were 21 years (out of 34) which had no more than 100 birds. This makes less than 5 birds (in some cases only 1 bird)  for estimation of the lowest 5% of arrivals.
I suggest to start the curve at a higher point, preferably at the lower quartile (25%).

The Adjusted-R squared value, rather than the overall R-squared, should be used when presenting the results of a multivariate regression model.
Validity of the findings: Conclusions regarding the effect of climate variables are mostly speculations. This should be stated and conclusions shoule be presented in a more cautious manner.
Additional comments: Nice innovative approach for estimating spring arrival patterns.


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: CLIMATIC VARIATION IN AFRICA AND EUROPE HAS COMBINED EFFECTS ON TIMING OF SPRING MIGRATION IN A LONG-DISTANCE MIGRANT WILLOW WARBLER PHYLLOSCOPUS TROCHILUS
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: No Comment
Validity of the findings: No Comment
Additional comments: The authors have used a 36 years data set of captured willow warblers at a banding station in northern Poland to investigate the annual variation of spring arrival dates in relation to a dozen of climatic variables potentially reflecting the conditions of the species breeding, migratory and wintering grounds. The manuscript is clearly presented and the analyses are straightforward. In addition to the commonly used ways to estimate arrival dates (percentiles of e.g. 5%, 50%, ect) they use a rather novel metric, Annual Anomaly (AA), based on the cumulative deviation from the mean distribution of the whole study period. As in many previous studies of willow warblers conducted over times periods overlapping the present study, the authors find that the spring arrival dates have advanced by 5.4 days. A substantial fraction (59%) of the inter-annual variation in arrival dates could be explained by a set of the climatic variables with fairly similar contribution (Table 1). Interestingly, these included conditions from throughout the annual cycle, including the climatic condition during the previous breeding season, autumn migration, winter and spring migration. That these quite general variables could explain such a high proportion of the annual variation in arrival date is quite remarkable. This might be due to the fact that the inter-annual variation in arrival data in this data set was quite substantial (late and early years occur throughout the study period) and that the explanatory variables themselves were mainly uncorrelated (Table 2) providing sufficient statistical power to disentangle the effect of the explanatory climatic variables. Overall, it is a nice study worth publishing.

Detailed comments.
My main question relates to the composition of willow warbler subspecies in the data set. The study site in Poland is located in the migratory divide between the subspecies trochilus (wintering in western Europe) and acredula (wintering in eastern and southern Africa), see e.g. Bensch et al 2009 (Molecular Ecology). The birds captured at the banding station is supposedly a mix of these populations. I would guess that their divergent migration routes and wintering areas will be quite differently affected by the analysed climatic variables, e.g. trochilus in West Africa should perhaps not be affected by the Indian Ocean Dipole. I understand that it will be impossible to disentangle these birds into their subspecies, but it would be good to get an idea of their relative proportions. For example, the banding recoveries from the study site (spring birds) could be used to say whether the data mainly consists of trochilus, acredula or both.  That you may have a mix of willow warblers with different migration routes and wintering areas should be mentioned in the introduction.

Several studies have examined variation in annual spring arrival dates of willow warblers in Europe, during time-periods overlapping the present study. The observed advancement of arrival dates are quite similar across the studies. It would however been interesting to see how well this local data set of annual arrival dates from Poland correlates with the arrival dates obtained from other places in Europe. For example, if your birds are mainly acredula, I would expect stronger correlations with arrival dates from e.g. Finland than from the UK.

Lines 424-425. Check species names, Pied flycatcher is Ficedula hypoleuca.

Line 490. Consider to replace “outstandingly” with e.g. the earliest.

Lines 534-535. I agree that AA seems to be a good way to measure annual arrival dates. However it would be useful to see how it correlates to the other measures, and whether its variance is smaller (assuming the others have more measurement errors).

It was indeed unfortunate that you had to exclude 2011 due to low sample size since this year showed remarkable delays in many migratory species wintering in eastern Africa (Tottrup et al 2012, Science).


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

Input:
Title: CLIMATIC VARIATION IN AFRICA AND EUROPE HAS COMBINED EFFECTS ON TIMING OF SPRING MIGRATION IN A LONG-DISTANCE MIGRANT WILLOW WARBLER PHYLLOSCOPUS TROCHILUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The article meets the standard, uses clear and professional English, cites appropriate litarature and shows excellent figures and tables. Raw data are shared.
Experimental design: No comment. Method is now described very well.
Very minor comments see below which might be added.
Validity of the findings: No comment
Additional comments: This is an excellent revision and the authors took over most concerns and implemented most suggestions. I particularly appreciate the testing of the many suggestions I gave.
I will first answer to the five specific points:

(1)
I particularly appreciate the test with local precipitation. I agree that these are too many variables. However, I would at least add in the discussion that NAO and local precipitation were positively correlated at the study site during the respective time, as this makes interpretation complicated whether the most important factor is NAO or local rainfall. That should at least be mentioned, now that the authors made all the effort.

(2)
I hope that the authors did not get me wrong – I highly appreciate the selection of the indicators by ecological meaning and not just by taking anything that is available. This was never questioned and, again, I am totally fine with the parameter selection. My only question was the collinearity, because I was missing it in a place where it should come. I highly appreciate the adaptations by the authors. Also, I am entirely fine with some collinearity which is to be expected in time series and ecological data, I was just wondering about the strength. The way it is presented now strongly improved the manuscript.

(3)
I also highly appreciate the test for linear versus quadratic terms and agree with the authors’ decisions. Only for one term, deltaAIC would be larger than 2, and I agree that this seems complicated to explain (through not impossible). However, as I believe that more people could question that, I would suggest to add a statement to the text that this has been tested and it did not lead to better AIC (I leave it to the authors how to describe the one exception – though it is only 2.49, so to be discussed whether the limit of 2 should be seen too strictly).

(4)
All subset regression: Great job! I highly appreciate it!

(5) I agree with the authors.

Further short comments:
Regarding the alternative approach I suggested: It is highly likely that this does not work for backward selection. Backward selection is highly sensitive to the order of the variables. If you change them (automatically through this approach), the result must differ (almost for sure) from whole model selections. If the authors decided to not touch precipitation issues, I am fine with the original approach.
Weather station: Great! Good luck with the local weather station.
I also highly appreciate the use of AICc, even if it shows identical results. For such a rather small subset, AICc just provides a better value (and sometime it indeed changes the order of the best models).
Figures and Tables are excellent.


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: CLIMATIC VARIATION IN AFRICA AND EUROPE HAS COMBINED EFFECTS ON TIMING OF SPRING MIGRATION IN A LONG-DISTANCE MIGRANT WILLOW WARBLER PHYLLOSCOPUS TROCHILUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Most comments were referred to and corrected and the statistical analysis has been modified and rerun. I find this manuscript innovative and important.

Some minor comments:

1. LL 386-388. You mention a change of 0.27 days a year of the first 5% of arrivals and of 0.17% of the first 50%. That is,  a 60% difference between the two precentiles. Although this might indicate a stronger effect of climate change on the lower edge/ more “adaptive”/ ”non-conformistic”birds, this may be an indication of the unreliability of measures based on a too small a sample for the estimation of the 5 prectile. Please, point that out. Please notice that this posibility is supported by the much smaller change for the 10th percentile (Table S2).
Additionally, I suspect that you got some mistake in this table, as the overall change of -7.9 days is identical for the 10th precentile and the median, but the slopes of these two precentiles are different: -0.17 versus -0.22. How come?

2. You exapnd quite a bit about checking for multicollinearity among explanatory variables. This is somewhat redundant because multicollinearity, if exists, causes inflation of the variance which may obscure possible relationships between the response and the explanatory variables. Therefore, any statistically significant results obtained, would be in fact conservative in case of multicollinearity. Eliminating a potential problem is, of course, desirable in order to receive a more complete picture of the statistical relationships. However, the elimination of multicollinearity could only enhance relationships already revealed in a model, not dismiss them.

3. Figures headings are long and difficult to follow. Figures in particular should be self-explanatory as words are in the manuscript’s text. Please add legends with images instead of the many words (e.g.  ”green arrows”, “thick lines”, etc. should be represented by an image).

Figure 1: Please simplify subheading (A) and divide the long sentence into 2-3 short ones. Additionally, please add a legend explaining the different lines/arrows, rather than writing it in the heading’s text.

Figure 2: It seems that numbers and words of headings got mixed up in your PDF file. Please correct headings to:
(A) Spring migration in 1997 in relation to the regression line of overall spring migration during 1982–2017;
(B) Spring migration in 1989 in relation to the regression line of overall spring migration during 1982–2017;
Please add a legend presenting the different lines/colors and shorten the worded explanation.
Please break the last sentence into two instead of using “which” (start with a picture of “light grey”, explain what it represents, and then turn to the dark grey.

Figure 3: Please add a feature legend with images (a line with circles, with triangles, etc.).

Figure 4: Please add the p-value to each of the regression’s graphs.

Tables 1 & 2 belong in the supplementary material. They are not necessary for the coherency of the manuscript.

Table 3: Please limit wording. Details regarding the statistical outcomes, such as F-value, Adj -R2, etc. are self-explanatory and the extra-wording is redundant. i.e., it would be enough to write:

Best model statistics:
Overall F  =…,    p-value =…, Adj-R2 = …


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: BIOCHEMICAL AND BIOPHYSICAL CHARACTERISATION OF IMMUNOGLOBULIN FREE LIGHT CHAINS DERIVED FROM AN INITIALLY UNBIASED POPULATION OF PATIENTS WITH LIGHT CHAIN DISEASE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript by Sternke-Hoffmann et al. characterizes the purity, thermal unfolding, tryptic digestion and aggregation kinetics of a set of light chain proteins from patients suffering from multiple myeloma (MM) and / or light chain (AL) amyloidosis. The study finds no correlation between protein stability, aggregation kinetics and the clinical phenotype of the disease, specifically the renal impairment. There was, however, an increased resistance to tryptic digestion in LC from patients with high renal impairment. Unfortunately, possible mechanistic explanations of this observation remain largely unexplored.

As the manuscript essentially  reports a data set, the reported data should be as complete as possible. I would strongly suggest putting the original data from AFM, aggregation assays and Western blotting from all 20 samples into the supplementary data set. This would enable the scientific community to mine the reported data set for future studies. The authors have already deposited SDS-PAGE and DSC data for all samples, which is commendable, but AFM data and ThT kinetics seem to be missing for most samples. I would also suggest adding a meta file to the supplements that lists explicitly, which data files contain which experiments and samples.
Experimental design: The main benefit of this paper to the scientific community is the thorough characterization of a LC protein sample set.  The data presented are solid and I see no flaws in experimental design. Therefore type of manuscript appears to be within the scope of PeerJ, even though it leaves the reader asking which, if any, hypothesis was being tested.

The main methodical criticism is that information about the criteria for patient selection is lacking. This is important, since all the LC samples in the study came from patients with a high ratio of LC to albumin in the urine. While this is common in MM, only a small subset of AL patients fulfills this criterion, as many patients present with massive proteinuria, leading to the excretion of large amounts of albumin and comparatively little LC, which would have prevented the purification strategy employed in this study. The samples in this study may therefore not be representative of MM and AL cases in general. This apparent and unstated bias needs to be resolved, especially since the title emphasizes the  ‘unbiased’ population of patients. The authors need to report whether the sample set simply consisted of a random set of MM patients, one of whom happened to be diagnosed with AL, or whether biochemical criteria about LC / albumin ratios were applied during patient selection and, if so, how their patient selection relates to the overall population of light chain disease patients.
Validity of the findings: The findings as reported are valid and the experimental design seems robust. Criticism and suggested improvements are stated in the previous two sections. It would be helpful to know if the data set in this manuscript will form the basis of further mechanistic or therapeutic studies or whether the authors are reporting a negative result based on a specific hypothesis.
Additional comments: Figure formatting should be improved before publication. Axis labels are uneven between panels. Many of them are much too small to be legible (Fig. 3 and 4). The AFM panel in Fig 3 lacks height scale.


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: BIOCHEMICAL AND BIOPHYSICAL CHARACTERISATION OF IMMUNOGLOBULIN FREE LIGHT CHAINS DERIVED FROM AN INITIALLY UNBIASED POPULATION OF PATIENTS WITH LIGHT CHAIN DISEASE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper “Biochemical and biophysical characterisation of 1 immunoglobulin free light chains derived from an unbiased population of patients with light chain disease” presents some findings on the biochemical properties of antibody light chains from patients with light chain disease, either diagnosed with MM or  AL
BASIC REPORTING
The paper is well written and very easy to understand. It gives a fair description of the work in the field and the references are sufficient. My only suggestion is to remove the acronym CNS since it is not defined elsewhere and only used once.
All the findings are also displayed through a few, quite clear pictures. In some cases the pictures could be improved: the dark green/light green boxes can be done in different colors. Also, the different properties are always displayed individually, and never combined in a single plot. For example, it should be expected, according to what stated in the paper, that the thermal stability and the tryptic digestion values might have some correlation. The paper never integrates or discusses the different features altogether – see later for more details
Also, no raw data is supplied
Experimental design: EXPERIMENTAL DESIGN
See the "validity of the findings" sections  about the experimental setup for digestibility.
All experiments are performed and described in a rigorous and replicable fashion
Validity of the findings: VALIDITY OF THE FINDINGS
Most of the results in this work are solid, even if negative or incremental. I would have liked to see if some of the features have a correlation, such as thermal stability and digestibility. Since the digestibility is primarily a way to measure the extent of dynamics of the LCs, it might be expected that these features correlate to a certain extent.

I am also very unsure that digestibility as presented is a very solid way to measure the extent of protein dynamics across different LCs. Trypsin has a very precise cleavage pattern, and the number of tryptic sites can vary hugely between different LCs. It would be extremely beneficial to also sequence the LCs from the patients’ B cells. This would have not only given an answer to e.g. the different number of tryptic sites, but also a valuable information on the precise differences among the patients’ LCs.
I would suggest that the authors comment on these points.

On the other hand, the digestibility is in some parts argued to be a possible starting point for fibrillation. This is true, but in my understanding the proteases that are involved in this process in vivo are completely different from trypsin, so these findings might not reflect to the actual digestibility of the protein in vivo. I would suggest that, if the authors want to study digestibility per se and not as a measure of protein dynamics, they replicate the experiment with the proteases that are actually involved in LC proteolysis.
Additional comments: The paper is clear and well written, and I believe that some of the findings are of interest in the field. I believe that some of the conclusions are not completely supported by the experiments, and they are mostly of speculative nature. I would therefore suggest to discuss these conclusions more thoroughly


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: BIOCHEMICAL AND BIOPHYSICAL CHARACTERISATION OF IMMUNOGLOBULIN FREE LIGHT CHAINS DERIVED FROM AN INITIALLY UNBIASED POPULATION OF PATIENTS WITH LIGHT CHAIN DISEASE
Review round: 2
Reviewer: 1

Output:
Basic reporting: In their revised manuscript, the authors have comprehensively addressed my comments and submitted a manuscript that is ready for publication.
Experimental design: no further comment.
Validity of the findings: The authors have expanded the data deposited at OSF to provide comprehensive access to their primary data.
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: BIOCHEMICAL AND BIOPHYSICAL CHARACTERISATION OF IMMUNOGLOBULIN FREE LIGHT CHAINS DERIVED FROM AN INITIALLY UNBIASED POPULATION OF PATIENTS WITH LIGHT CHAIN DISEASE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript in the current form is suitable for publication
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: ORB-WEAVING SPIDERS ARE FEWER BUT LARGER AND CATCH MORE PREY IN LIT BRIDGE PANELS FROM A NATURAL ARTIFICIAL LIGHT EXPERIMENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is well written and presented.
Experimental design: As detailed more fully in my general comments, I have some questions as to the independence of the panels/sites and thus the general validity of the statistical results.
Validity of the findings: As also detailed in my general comments, there is some over-speculation or over-generalizations, particularly with respect to the title and abstract.
Additional comments: The author exploits a natural experiment in the form of a bridge with alternating lit and unlit panels to explore how the lighting affects spiders living on those panels. The results appear to show more spiders in unlit panels and larger spiders in lit panels. The strongest result may be the larger number of captured prey in lit webs vs unlit webs, particularly after controlling for web size. I think these results are likely robust and could contribute a nice piece to the growing work on light and urban spiders. I do have a few major concerns however:

First, there is a real statistical issue with respect to independence. Each panel is treated as an “independent group” but this seems difficult to justify. They’re all right next to one another, right? I would guess that spatial autocorrelation could be an issue here and that other spatial issues might be apparent. Are there patterns with respect to whether a spider or panel is in the middle of the bridge vs at the end? I recommend further explanation and examination of these aspects in the methods. But most critically, there is one bridge and so one site really. In the conclusion it is noted that the study represents “one location” and one “snapshot”. So, I appreciate that this is recognized but I think that this should be better articulated; how might these results change if the study went on for longer than a week or if multiple bridges were used? Expansion of this in the discussion would be helpful.

Second, additional natural history details are needed. It’s not entirely obvious but it seems like all of the studied spiders were Larinioides sclopetarius. Can you provide more details about the species? There’s actually quite of bit work on this system within which it would be helpful to contextualize your results:
Kleinteich, A., Wilder, S. M., & Schneider, J. M. (2015) Contributions of juvenile and adult diet to the lifetime reproductive success and lifespan of a spider. Oikos, 124, 130-138. [this one is particularly relevant given the implications for food restriction]
Kleinteich, A., & Schneider, J. M. (2011) Developmental strategies in an invasive spider: constraints and plasticity. Ecological Entomology, 36, 82-93.
And also, the Heiling studies already cited in the paper. At present it’s hard to link the results to what this means for the species or ecology. Greater engagement in this regard would be helpful.

Third, particularly given the first point above, I urge greater caution and constraint in how the results are presented and interpreted. For example, the title and abstract are much too broad given the study (more detail on this below).

Additional comments:
Title – needs to be better constrained and described… at present it reads like a review which this is not, best to have a title that captures the essential result and in the proper context, e.g. “Orb-weaver spiders are fewer and smaller in unlit bridge panels from a natural artificial light experiment” (or something like this)
Abstract – at present, about half of the abstract is speculative… I would reduce this in favor of focusing more on the methods and results (there is essentially nothing in the abstract about the methods)
line 10 – the relationship between insects and light is complex, e.g.
Owens, A. C., & Lewis, S. M. (2018). The impact of artificial light at night on nocturnal insects: A review and synthesis. Ecology and Evolution, 8, 11337-11358.
I think this paragraph and the following two could be better developed
line 36 – is a week of data enough?
line 40 – what’s the light brightness? Is it fluorescent? More details needed here regarding the light source
line 42 – “unlit”
line 55 – so were all the species recorded (not just collected) Larinioides sclopetarius? And if so, why not make this clear in the abstract? If not, what else was observed?
Line 75 – what was the prey? And is number of prey most appropriate here instead of say, prey mass?
lines 106-108 – what’s the range of spiders in lit and unlit?
line 114 – I would interpret this as there not being effect (it isn’t a problem of the statistics)
line 120 – what family?
line 152 – I presume that the idea here is that lit webs are attracting more prey. This is discussed in the intro but should be made explicit here as well. But also, there are more webs in unlit conditions, thus it could just be that there are more webs competing for the same number of insect prey and webs in lit conditions take advantage of this (rather than there simply being more prey)
line 169 – I don’t think it’s very clear, particularly given that you didn’t measure prey. The main point of this sentence is fine but I would suggest being cautious about claims like this.

Figs 3-5: Increase font size of axes to improve readability


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: ORB-WEAVING SPIDERS ARE FEWER BUT LARGER AND CATCH MORE PREY IN LIT BRIDGE PANELS FROM A NATURAL ARTIFICIAL LIGHT EXPERIMENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well-written manuscript that clearly explains the experiment using appropriate language. The figures are relevant and easy to understand. The literature relating to spiders foraging under artificial light at night is well referenced. However, the introduction requires a lot more context for the effects of light pollution broadly, particularly for its physiological effects which have potential consequences for body condition and mortality, both of which are directly relevant to this experiment. More information is also needed for the basic biology of web building, and the importance of different lighting technologies to provide context to these results.
Experimental design: This is a well-designed and simple experiment that neatly tests a hypothesis, and these connections are clearly communicated. The introduction provides context for why investigating web building, abundance and body condition of an orb-weaver in the field is important. Some of the methods require more description, such as the choice of web for architecture measurements, and better justification is required for the use of body condition residuals. It would also be useful to explain why this paper is important given that a similar experiment was performed by Heiling & Herberstein  (1999).
Validity of the findings: The discussion provides a useful interpretation of the results, supported by the literature. This would be improved by expanding on explanations of results, given improved context in the introduction (e.g. physiological damage from ALAN), and providing better comparisons with cited literature (e.g. differences with Zygiella, similar result found for tetragnathids, effects of light type, etc.).
Additional comments: This is a very interesting study, and you have done a good job communicating your results and linking your results to your hypotheses. My main suggestions for improvement are to provide a more comprehensive introduction and a more cohesive discussion.


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

Input:
Title: ORB-WEAVING SPIDERS ARE FEWER BUT LARGER AND CATCH MORE PREY IN LIT BRIDGE PANELS FROM A NATURAL ARTIFICIAL LIGHT EXPERIMENT
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised version is clear and now well placed in the context of the literature and with respect to the implications of the results.
Experimental design: The additional detail provided in the revision is key and I'm satisfied with the justification and scope of the results.
Validity of the findings: Results are clear and well explained.
Additional comments: The revised version is much improved and the changes are well explained. In the revision the results are much clearer and the possible causes behind them more reasonable and complete. At this point I don’t have any further issues with the work and feel that it should serve as a useful contribution to the literature. I have a few suggestions and edits below – but there IS the important matter of Fig. 3 within which I think an unintentional error was introduced during revision.

Abstract – “not as active within these habitats” – this isn’t a landscape level effect is it?
Line 75 – any need for identifying body condition as a proxy for fitness? If not, I would delete this.
Line 92 – missed return for the subheading
Line 131 – microscope?
Line 183 – can remove “in them”
Fig 3 – something went wrong here, some of the asterisks were replaced by N.S.s


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: ORB-WEAVING SPIDERS ARE FEWER BUT LARGER AND CATCH MORE PREY IN LIT BRIDGE PANELS FROM A NATURAL ARTIFICIAL LIGHT EXPERIMENT
Review round: 2
Reviewer: 2

Output:
Basic reporting: I am happy with how the manuscript has been restructured
Experimental design: The experimental design is now easier to follow, and I am satisfied with the author's responses to my queries
Validity of the findings: The data have been better placed in the appropriate context, and the conclusions are now better supported by the rest of the manuscript
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: GENOME-WIDE IDENTIFICATION AND ANALYSIS OF CIRCULAR RNAS DIFFERENTIALLY EXPRESSED IN THE LONGISSIMUS DORSI BETWEEN KAZAKH CATTLE AND XINJIANG BROWN CATTLE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English language should be improved. Some examples where the language could be improved include lines 83-85 and the Conclusion section. Moreover, authors need to add a space between the word and the reference. Please, check line 67; 69; 76; 90; 100 and throughout the manuscript.
Experimental design: The study was performed using three samples of each cattle breed. While the sample numbers are on the lower side, this data could provide to research community interesting results about circRNA and the regulation of gene expression in skeletal muscle tissue.

Line 136. Authors need to add a reference for histological methods.

Line 140. These cattle groups were compared or not? Please, explain.

Line 207. Please, explain. Authors should specify which experiments were considered. Moreover, statistical analysis is poorly described.
Validity of the findings: The objectives and Conclusion need to be improved. The objective section should be more specific. Conclusion needs to be rewritten.

Line 314-315. What is the application of this results? Are those cricRNAs associated with meat quality traits or tissue development? Please, explain.

Line 338. This phenotype (longissimus muscle area) should be associated with circRNA data and the possible differences in gene expression. Thus, authors need to discuss how the circRNA regulate this muscle traits.
Additional comments: Lines 83-85. This sentence should be improved. Is this the objective of the current study (investigation of molecular mechanisms that control meat quality traits in Chinese brown cattle?) If this is the case, the Introduction section should be rewritten.


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: GENOME-WIDE IDENTIFICATION AND ANALYSIS OF CIRCULAR RNAS DIFFERENTIALLY EXPRESSED IN THE LONGISSIMUS DORSI BETWEEN KAZAKH CATTLE AND XINJIANG BROWN CATTLE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well reported, it is a topical work and there are very interesting results.
The paper is technically well presented and written. I suggest to carefully revise some paragraphs for English.
Experimental design: Materiel and methods are well explained but some modifications should be completed
I am wondering how the histological was performed. I suggest to the authors to carefully check the whole M&M part and provide all the necessary and detailed information of the protocols used. I also recommend to the authors, one the protocols are described elsewhere to just detail them as supplementary data.
Line 139: RNA library construction and sequencing
Please add sub-title to explain the different steps of the method and add reference to this method
Line 197: RT-qPCR analysis of circRNAs
Please add reference to this method.
The statistical method is poorly described. I ask the authors to carefully check this part and describe step by step all the statistical analyses conducted in this manuscript. Also, the packages uses are to be given in the supplementary data as recommended by the journal.
Results are welled presented, but there are some repetitions between methods and results (line 222-225) and (line 240-246)
To clarify the main message of the discussion section of this manuscript, I suggest to the authors to add sub-sections with informative titles and discuss accordingly.
Validity of the findings: The conclusion needs to be completed to give the take-home messages of this work. It is very poor and the authors are asked to highlight the novelty of their work and what are the future investigations.
Additional comments: This paper introduces interesting results. It needs substantial revision before I recommend it for PeerJ journal.


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: GENOME-WIDE IDENTIFICATION AND ANALYSIS OF CIRCULAR RNAS DIFFERENTIALLY EXPRESSED IN THE LONGISSIMUS DORSI BETWEEN KAZAKH CATTLE AND XINJIANG BROWN CATTLE
Review round: 1
Reviewer: 3

Output:
Basic reporting: First of all, I would like to remark the importance of the paper, to present novel information regarding circRNAs. I have some general comments to make before moving on to a number of more specific items:
:
1-	Tittle of the paper: it may need to be changed in order to fit better with the research results, which reveals significant difference in the expression of circRNA between two different cattle breeds.
2-	I suggest to condense the introduction, most of the text is repeated in the discussion. It will be very interesting to hypothesize about environmental rear conditions of these breeds, and how it modulate the expression of circRNA. Also, materials and methods must be specified.
The “state of the art” should be emphasized in cattle and muscle mechanism of regulations.
3-	Discussion should focus on results. It should propose an explanation about the differential expression of circRNA in the muscle of two different breeds. specially in myoblast mechanisms of regulations.

Specific points:
39-40 Muscle was the only tissue used, specific longisimus dorsi, that means only one sample, of 6 different animals (replicates) that need to be clarified, in the text and also in material and methods.
46- 48 Be specific about if the expression on paternal gene mean imprinted genes.
100-101 It is important to specify in which species circRNAs control the functions of vascular smooth muscle.
105- That asseveration need a reference.
Experimental design: Experimental are well design, was sequentially organized and responde to the main research aim. It has to be noted however, that the the researcher do no mention a control. Its is importante to have a values of reference about the circRNA expression in other tissue, or other species.
Validity of the findings: As the main result of the paper was to propose a possible role for two circRNA, which could be acting as a sponge of unknown miRNAs, and regulated  the IGF1R gene expression, authors should propose next experimental design that shed light on the real functions of these circRNAs.
Additional comments: Please check the lines: 72, 251, 252, 313, 318, 329 to separate words. Check the english redation in 42-44


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

Input:
Title: A MULTIPLEX CENTRALITY METRIC FOR COMPLEX SOCIAL NETWORKS: SEX, SOCIAL STATUS, AND FAMILY STRUCTURE PREDICT MULTIPLEX CENTRALITY IN RHESUS MACAQUES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors present an interesting new approach for estimating multilayer centrality that can handle common attributes of animal social networks: namely, network layers with different properties and functions. The authors then validate this approach by applying it to a well-understood social system, that of rhesus macaques. I found the paper to be clearly organized and well-written, with only occasional grammatical errors (noted under General comments). My main concerns are with the statistical approach, which I discuss further below.

The introduction does a nice job of introducing multilayer network approaches, describing the situations in which they may be helpful, and explaining how the currently available measures for describing multilayer centrality are often inadequate for animal social networks. I have only a few points where I feel additional clarification could be helpful:

L46, L63-64, L79-80: Is all social life complex? Are all animal social networks complex? I feel it would be helpful if the authors clearly state what attributes they believe make for a complex social system or social network.

L81-137: Following on from the above point, although the authors clearly present the rationale and potential advantages of using multilayer networks, are there instances in which the added complexity introduced by these approaches is not warranted?

L178-179: While this point becomes clearer later on (e.g. L330-339), a brief discussion or example here of what makes a particular centrality measure more or less appropriate for a given network would be helpful.

Table 2: Please define what network density is, and how it is calculated.

Figure 1: The caption should describe each portion of the figure (a, b, & c) separately.

Tables 3-6: Please provide standard errors and confidence intervals for model coefficients.

Figures 6: Can confidence intervals be included here?

Figure 8: The caption should indicate what the plotted line and grey regions represent.

In addition to the raw data that has been provided, the authors may wish to consider uploading the network data itself if it’s not already available.
Experimental design: L322-325: Was the severity of aggressive interactions (L290-293) included in the network, and if so, how was this done?

L326-328: Are grooming interactions generally asymmetric in rhesus macaques (e.g., A grooms B, but is not groomed by B)? If so, would it make sense to also treat this network layer as directed?

L335-339: Could more information be provided about how centrality was determined for the policing network? For example, assuming in-degree and out-degree are simply added together, one could envision peculiar situations such as individual A (policed 7 others, but was never policed itself) and individual B (never policed others, but was itself policed 7 times) having the same centrality.

L360-364: Although I appreciate the authors’ point regarding the difficulties of deciding the relative importance of different layers, I imagine that some researchers interested in using consensus rankings will have reason to suspect that particular network layers will be especially important. Are there potential modifications to this method that would allow such weightings to be incorporated?

L418-425: Burnham and Anderson (2002) caution against using arbitrary cut-offs, such as ΔAIC < 4 (see also Anderson, 2004, Model based inference in the life sciences; Burnham et al., 2011, Behav. Ecol. Sociobiol. 65: 23-35). This is particularly important for models with ΔAICc in the range of ~2 – 7; these still have some empirical support, and so should not be automatically discarded. If the authors wish to reduce their model set, perhaps the concept of a confidence set can be employed (Burnham & Anderson, 2002, pg. 196; Anderson, 2004, pg. 121).

With regards to removing more complex models with similar AIC scores to the top model, AIC already takes into account parsimony. As such, I think it would be better to leave those more complex models in the model set. That said, Burnham and Anderson (2002), pg. 131, do present a specific case where more complex models with ΔAIC in the range of 0 – 2 may be disregarded, which may be where the authors took their guidance for the pruning described here.

Including the more complex models (as well as models with ΔAICc > 4) may increase model selection uncertainty, but techniques for multi-model inference can be employed if this uncertainty turns out to be substantial.
Validity of the findings: L454-462: While I appreciate the authors’ justification for including both the aggression and status signalling layers when calculating consensus ranks, I think it is still important to test whether the main results change appreciably if one or the other of these two layers is excluded. If both layers are actually providing similar information about an individual’s social position, then including both in the consensus ranking risks inflating the importance of this information (especially since each layer contributes equally to those rankings).

L463-515: P-values obtained from GLMMs using network data generally cannot be trusted. These statistical models assume independent observations, but individuals’ network positions are not independent of one another (see Croft et al., 2011, TREE, 502-507; Farine, 2017, Methods Ecol. Evol., 1309-1320). To address this issues, a null network model can be constructed and incorporated into a GLMM (Farine & Whitehead, 2015, J. Anim. Ecol., 1144-1163). Please address this issue.

L473-474: Statistical information regarding the contrast between females from large families versus those from medium families is not presented here or in Table 3.

L503-515: The analysis of the grooming network provides a nice example where multi-model inference would be helpful. The model probabilities indicate substantial model selection uncertainty, with all five models receiving some empirical support.

L533-536: Earlier (L230-236), the authors reviewed literature indicating why females from large families were expected to be central, but was it predicted a priori that females from small families would also be central? Given that in L583-584 this finding is noted as surprising, perhaps only the former result should be included here in the list of expected results.

L536-539: I believe it would be good to acknowledge here that certain network layers (aggression, status signalling) provided a better match to the consensus rankings than others.

L613-614: Although the discussion immediately following this statement does a nice job of illustrating the potential of multilayer approaches to better characterize social patterns, I suggest tempering this first sentence somewhat. Consensus rankings certainly indicated differences in centrality compared to analysis of the single layer networks. However, whether those individuals with high consensus rankings are actually more important than individuals that are central within only a single network (i.e., in terms of their contribution to social functioning, group stability, transmission dynamics, etc.) remains to be experimentally tested.
Additional comments: L31-32: State the species here.

L40: Presentation of the statistical results here are somewhat confusing—e.g., females from the largest families were found to have higher centrality, yet the comparison between large and small matrilines is not significant and the comparison between larger and medium matrilines is not presented.

L128: “be a popular grooming partner”

L151: “node-level measures”. Also, should “network” follow “multiplex”?

L218-219: remove “are”

L269-270: “and the laws of the United States government.”

L467-510: Would it make more sense to discuss rankings as higher or lower (rather than better or worse)?


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

Input:
Title: A MULTIPLEX CENTRALITY METRIC FOR COMPLEX SOCIAL NETWORKS: SEX, SOCIAL STATUS, AND FAMILY STRUCTURE PREDICT MULTIPLEX CENTRALITY IN RHESUS MACAQUES
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the manuscript “A multiplex centrality metric for complex social networks: sex, social status, and family structure predict multiplex centrality in rhesus macaques (#38664)”,
the authors present an original and interesting method to measure multiplex centrality which allows using different centrality metrics to account for each layer depending on its dynamics and functionality.

Overall, the paper is very well written and organized, making it easy to follow and understand. It is a self-contained manuscript, well referenced and supported by tidy helpfull tables and figures. The introduction is divided in helpful subsections providing relevant background properly supported by accurate references. Enough raw data is provided to replicate the core analyses presented. The results directly respond to the objectives and hypotheses presented.
Experimental design: This is an orignal study is based on a solid data set including information from 5 interaction types between members of seven captive groups of Rhesus macaques, a well-known study species. The objective of the study is clearly defined and highly relevant to current demands for analytical tools to develop social network analyses that better respond to biological questions based on empirical data. The authors introduce a novel method to infer individual centrality based on multiple network layers (interaction types/contexts), and they also include validation of the method taking advantage of the known social organization and dynamics of the study species. The methods are well described and seem rigorous and carefully thought and carried out. The raw data provided presents the centrality ranks for each multiplex layer allowing for replication of the calculation of multiplex centralities and comparison with single-layer results.
Validity of the findings: Results are clearly presented and well supported by tables and high quality figures properly labelled (particular comments on figure captions are shown below).  Although it is not the first method to calculate multiplex centrality, it has characteristics that are absent in other known methodologies, thereby expanding the possibilities of analysis, particularly when using different centrality measures across layers may be a better way to address the problem or system of interest. I find it relevant and useful, not only for the field of primatology and for studies of social structure at large, but also as an interesting contribution to social network analysis in general. The results are nicely discussed and the conclusions are well stated and directly derived from the results.

I only have two concerns regarding the methodology which I would like the authors to discuss to some extent. First, is the use of GLMMs to analyze the centrality ranking data derived from interactions not violating independence assumptions (see Farine and Whitehead 2015 "Constructing, conducting and interpreting animal social network analysis")? If so, how could this affect the methodology proposed? Could it be better to consider methods like ERGM devised specifically for netwrk data? My second concern is related to the robustness of the centrality results. From what I understand, the analyses presented did not involve randomizations or any other method to estimate uncertainty about the centrality ranking results for each individual layer and for the multiplex centrality. If this is so, how could the method be complemented to account for effects resulting in small differences between centrality rankings? How do we know that the differences observed are not random?
Additional comments: The following are specific comments/suggested edits directly related to specific lines from the text or figure captions:

L82. I suggest avoiding the term network when referring to the layers of the multiplex network. Instead, use layers as you do further along the text.

L84-86. I suggest define the meaning of network layers (what they represent) before defining multiplex networks.

L118-119. Edit to: “…can further give insights into an individual’s social position/role within a society”

L128. Edit “partner” to “partners”

L129. Edit animal to animals

L218. Edit: remove “are”

L325-328. So grooming direction is not influenced by the dominance ranking? By defining the grooming layer as non-directional, this suggests that the information about directionality is not considered as relevant to centrality ranking as, for instance, aggression and dominance signaling. I this something well established in Rhesus macaques? Or why disregard directionality when the method devised allows for its inclusion and it may convey additional information? Please explain a bit more.

L334-335. Given that eigenvector centrality is less intuitive than other centrality measures, I suggest adding a reference to this statement or a bit more explanation on how it is better for finding positions in hierarchical systems.

L380. Edit to: “… how much of the variance of the untiered centrality values is explained by the tiered centrality values.”

Comments to figures.

Figure 1. Please add a bit more explanation to the caption, particularly referring to the three parts of the figure labeled a-c. Also, please mention what is indicated by bar color in 1b and make some mention of the y axis units in 1c (1-r2)

Figure 8. Please mention the confidence bands shown in the figures including confidence level.


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

Input:
Title: A MULTIPLEX CENTRALITY METRIC FOR COMPLEX SOCIAL NETWORKS: SEX, SOCIAL STATUS, AND FAMILY STRUCTURE PREDICT MULTIPLEX CENTRALITY IN RHESUS MACAQUES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is largely clear and well written. In places there are quite technical concepts that need to be better explained to make them accessible to the intended audience of the article (have detailed these in my line-by-line comments in the general comments box).

Use of literature is good. One paper that should probably be added in discussing the use of multilayer networks in animal behaviour is:
Finn et al. 2019. The use of multilayer network analysis in animal behaviour. Animal Behaviour, 149, 7-22.

Article structure is generally clear. I personally would prefer to see some of the initial sub-section of the Methods at the end of the introduction to help set up the hypotheses/predictions of the study at the end of the introduction. The discussion is a little repetitive at times (highlighted in my line-by-line comments below)

I would provide confidence intervals around model predictions rather than indicating significance in the Tables. Using p values and AIC together has some strong opponents and it is often best to use whether the 95% confidence interval crosses zero or not (in the model of interest or an averaged model) as a measure of the statistical significance of the result

The figures need considerable improvement - simply plotting model predictions without either the raw data points or an indication of the error around these predictions is unhelpful.
Experimental design: The research questions are well defined but it would be good to see hypotheses and predictions set out more clearly in the introduction.

Data collection methodology appears rigorous and has suitable ethical approval, and in general the methods are described in a good level of detail (with some minor exceptions detailed in my general line-by-line comments). The one general exception to this is that I would say that the Methods is very light on describing what software was used and how it was used to conduct various aspects of the data analysis.

I worry a little that different network metrics have been calculated for different layers - not so much for the calculation of the consensus rank (where it has been justified) but for the calculation of correlations between the ranks of layers (Fig 2), as betweenness centrality and eigenvector centrality might well be expected to not be correlated anyway creating a distinction between the correlation values calculated that does not depend on differences between the layers. I wonder whether a matrix correlation between different layers would also be of value.

I am concerned by the failure to account for the non-independence of observations in the network in statistical inference from the models fitted. In general animal social networks that fit LMs or GLMs use randomisations to test statistical significance (e.g. https://www.sciencedirect.com/science/article/pii/S0169534711001455) or use MCMC approaches to fit them (e.g. https://www.nature.com/articles/s41598-017-18104-4) to deal with the issue of non-independence, and I feel that using one of these alternative methods is important here unless the authors have a strong justification as to why they think the non-independence issue does not arise in this dataset.
Validity of the findings: Results are fairly well explained given that they are fairly complex. I would suggest being consistent with how you treat variables that are in the top model but with confidence intervals that cross zero (i.e. are statistically non-significant). I think the simplest and clearest way to do this is to state that they are in the top model but also say that they are non-significant universally (avoiding language like tended for example).

I would also suggest using higher rather than better when discussing consensus ranks (this comment applies elsewhere too)

For the results for separate network layers it would be worth reminding the reader which network metric was used as this might affect the results. This should also feature as a discussion point. Eigenvector centrality and betweenness centrality will indicate different social roles.

The discussion is rather long but very well written, I only have minor comments detailed below.
Additional comments: Some line-by-line comments:

Abstract
L22: "welfare" is a slightly odd choice here given you haven't yet specified between wild and captive animals
L28-32: Would suggest breaking up this sentence. Something along the lines of "Here we validate a new method for quantifying multiplex centrality called consensus ranking by applying this method to multiple social groups of a well-studied non-human primate, the rhesus macaque. Consensus ranking can suitably..."
L33: Suggest changing "predictive of" to "correlated with"
L37-42: I am not a huge fan of p values in abstracts. Your certainly need to make sure you are consistent here though if you do use them, some results here have p values and others don't

Introduction
L52: Suggest deleting "However, " to avoid having a however immediately followed by a yet, which reads strangely. Otherwise nice opening paragraph!
L84-88: I think it is best to start here with the technical definition here that a multiplex network can only contain inter-layer edges that connect the same actor in different layers. You can then go on to say that this normally equates to different layers representing different sets of behaviour interactions between the same or a similar set of individuals
L91-93: Here and elsewhere in the introduction you provide a good explanation of why you use multiplex networks versus single networks, but you also need to explain why multiplex networks are more informative than simply aggregating all of the layers to complete this motivation
L117: Here and elsewhere you need to make sure you are clear that "multiplex centrality" consists of multiple possible network metrics - too often it is sounding like a single measure in its own right.
L123: Another example where it is important to distinguish the advantage of multiplex to that of aggregating networks
L151: "node-level measureS of connectivity" and "in a multiplex NETWORK broadly"
L155: In my opinion you will have to provide a more accessible explanation of a tensor for a zoological/ecological audience or avoid using the terminology
L178-179: This needs a little more context/explanation
L184-188: First, I find it a little odd that the wording of this is almost identical to the abstract. I would suggest making a similar swap to that suggested earlier to make it easier to read.

Methods
L210: Would suggest linear rather than clear as you have used clear also in the previous sentence
L306-307: Not immediately clear what this means or whether that is deemed sufficient - a little more detail here would be helpful
L325-328: It seems strange to me that direction is deemed unimportant in grooming networks given the evidence in other study systems of asymmetry in these relationships - is this something particular to macaques? Potentially a more careful explanation would be of value here.
L333-334: It is not clear to me why betweenness makes a good measure of cohesion? Surely a measure such as closeness has a much clearer link to cohesion of groups. Individuals in some network structures can high betweenness when acting as bridges between communities despite having low cohesion to both. As such, I am struggling a little bit with this justification to use betweenness.
L336: Are in-degree and out-degree of the policing layer summed separately or together? It strikes me both have rather different meanings behavioural and summing them together could be problematic and also lose lots of information about the social role of an individual.
L360: On point b), it strikes me that a nice strength to this new measure when calculated this way is that by changing the weighting used when summing the ranks you can actually vary how much influence each layer has, which may be valuable in some contexts. Perhaps worth discussing somewhere?
L364: One potential weakness of this centrality measure in a multilayer (from what I can see) is that the ranking in each layer is done separately and so it doesn't incorporate the multiplexity of the network very well. Therefore an individual connected to the same 10 individuals in layer A and layer B will have a higher ranking than one connected to a different 7 individuals in A and B (and therefore 14 individuals overall). Other measures of multiplex centrality also have this issue but I think it is important to mention or caveat somewhere. If this could be factored into this measure too at some point down the line it would be great.
L365: This sub-section is one that I think I would struggle to replicate with the current level of detail. I think it particular it would be valuable to provide more information on the practicalities of how the clustering algorithm was applied and also how the output of the clustering algorithm is used.
L397-402: This is another approach that needs to be outlined more carefully to make it fully replicable. More help is needed in how the approach was applied and stronger links to the biology of the study system would help understand why it was used.
L411: Please make it more clear and intuitive why this transformation of the data is suitable for use in a negative binomial model.
L413-414: Please provide methodology for how dominance certainty was calculated and also how matrilines were defined to enable matriline size to be calculated. Dominance certainty is particularly important to understand how it fits in with aggression and status signalling - is it a separate measure or does the calculation of dominance certainty use these variables?
L415: What do you mean by all interactions? Up 3-way? Or were up to 6-way interactions fitted? This is currently very unclear.
Would be helpful to define the alpha/significance level somewhere in the analysis subsection of the methods

Results:
L443: Suggest changing "highest" to "strongest positive" to be clearer with direction
L446: Suggest "more variable POSITIVE correlation" to ne clear with direction
L449-451: Suggest adding some numbers/model predictions for this result
L461: Suggest changing to "in the CALCULATION OF consensus"
L467-468: This result is not immediately apparent from the model results (main effect term is NS + there is an interaction anyway) so you need to be clear with where it comes from
L484-485: Avoid this (see comments in Box 3)
L495-501: A supplementary figure or some mode estimates/standard errors to support this verbal description of the results would be helpful

Discussion:
L533-536: I feel more careful wording here to avoid equating general effect with characteristics of "the most connected individuals"
L573: I would suggest editing to "In fact, kinship among females contributeS to key..."
L586: Would suggest adding a qualifier at the end of this sentence e.g. "...for being well-connected for females in small families". Would also suggesting adding a "can"  at the start of the next sentence "Female macaques CAN also form"
L613-614: More careful wording is needed here. You have shown you get different results, but succeed implis there is a right/wrong which I would disagree exists. I think you can say that the multiplex provides a more holistic overview without claiming it is the correct approach.
L617-618: This subadult result didn't really come through clearly in the results section - be more clear linking age to subadult/adult in the results too for consistency.
L620-621: Again, this comparison isn't entirely fair - I imagine the multiplex doesn't reveal everything we know either, perhaps again temper this a little to say that the multiplex has provided a more integrated/holistic view of social structure etc.
L623-634: I find a lot of the ideas in this paragraph rather repetitive of things that have come before, especially in this latter section - it loses the flow of the discussion somewhat.
L638-639: I would suggest avoiding this
L662-663: This seems rather repetitive from earlier in the paragraph
L668-671: This seems a rather weak ending to the paragraph and I am unsure what is meant by talent in this context? I I wonder whether this sentence could be deleted.

Tables 3-6: Would suggest providing an indication of confidence intervals around model estimates (perhaps instead of p values as highlighted in Box 1)

Figure 1: Please provide more helpful and detailed figure legend
Figure 2: Any reason why this couldn't be multi-panelled to provide equivalent data on all of the groups?
Figure 3: Please provide more helpful and detailed figure legend
Figure 4-7: I would strongly suggest you add confidence intervals and preferably raw data to these plots. They also require more helpful and detailed figure legends
Figure 8: Would be good to see a version of this showing all 7 groups. The figure legend also needs to be more detailed e.g. what are the lines/polygons plotted here and why have they been plotted? Why is dominance rank on a different scale to the other figures?

I hope my comments are useful in improving the manuscript.
Matthew Silk