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

Input:
Title: EFFECTS OF DIVERSITY AND COALESCENCE OF SPECIES ASSEMBLAGES ON ECOSYSTEM FUNCTION AT THE MARGINS OF AN ENVIRONMENTAL SHIFT
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, the manuscript is written with clear and unambiguous language. The study is on a topic broadly interesting to many people in various fields and the general PeerJ readership. I believe with some major revisions, this study can be published in PeerJ. However, as written, the manuscript lacks many of the appropriate literature references and background needed to give the readers appropriate context. I have detailed in this in the "general comments to the authors" section.
Experimental design: The general experimental design and research question is sufficient. The authors should revise the mesocosm descriptions to be more clear. I have detailed this and other edits in the "general comments to the authors" section.
Validity of the findings: I have some concerns in regards to this section. Overall, the data is interesting, however, the authors could expand upon the results they have with data they have at hand. This manuscript would benefit from an increased analysis of the OTUs present and how they correlated to the factors measured beyond salinity. Do the authors see any changes in abundances of an OTU or OTUs that relate to changes in carbon mineralization at the mid species richness? Were those isolates native or brought in with mixing? Or, if salinity negatively impacted thse functions what OTU changes could have influenced that? What insights can be garnered from those OTUs in their potential function? While richness can tell you about the diversity in the community it doesn't account for potential fluctuations in an organism or organisms that may relate to the loss of an ecosystem function. Further, while richness can increase, it may not be the immigration of organisms but rather the change in native taxa that resulted in the correlation. Conversely, increased richness may result in communities that are more resilient because of the functional redundancy provided. I think more detailed analyses of this data placed in context with other work on community resilience and salinity impacts could help shed some light on this and add to the overall manuscript.
Additional comments: Overall, the manuscript is well written and uses unambiguous language. A study on how salinity impacts ecosystem function and community composition is very interesting to broad fields and to PeerJ readers.  However, the manuscript needs major revisions (discussed below) before it is ready to be published. The authors should focus on adding more context to the introduction, clearing up the mesocosm setup in the methods, and adding more details on OTU abundance and their potential relationship to the measured ecosystem functions.  I want to stress I believe this manuscript is publishable and the data is interesting. I believe more context in the introduction with a better set up to the hypotheses and questions being tested and asked, respectively, will help considerably.

Introduction

The introduction is lacking a lot of literature, a proper review of the current knowledge, and many details on how salinity may impact ecosystem functions in aquatic systems. As written, the introduction felt more of a review of the study and methods done in it. The only introduction to the current field is lines 29-32 and paragraph two (lines 38-48). This made it hard to connect the importance of this study to what was being argued in the discussion and, most importantly, why this study was done in the first place. Moreover, the introduction would benefit from the addition of literature related to zooplankton/bacteria communities and salinity. The only literature in the introduction discussing aquatic communities of zooplankton or bacteria was Paver et al. (2018), an interesting study but was focused on the evolutionary transitions rather than the impact of salinity on community composition and ecological function. The rest of the studies focused on plants, insects, salmoids, and amphibians. A few pieces of literature that could help shape this introduction to focus more on the organisms being studied are:
-Langenheder, S., Kisand, V., Wikner, J., & Tranvik, L. J. (2003). Salinity as a structuring factor for the composition and performance of bacterioplankton degrading riverine DOC. FEMS Microbiology Ecology, 45(2), 189-202.
-Dupont, Chris L., John Larsson, Shibu Yooseph, Karolina Ininbergs, Johannes Goll, Johannes Asplund-Samuelsson, John P. McCrow et al. "Functional tradeoffs underpin salinity-driven divergence in microbial community composition." PloS one 9, no. 2 (2014): e89549.
-Lozupone, Catherine A., and Rob Knight. "Global patterns in bacterial diversity." Proceedings of the National Academy of Sciences 104.27 (2007): 11436-11440.
-Eiler, A. et al. Productivity and salinity structuring of the microplankton revealed by comparative freshwater metagenomics. Environ. Microbiol. 16, 2682–2698 (2014).
-Logares, R. et al. Infrequent marine-freshwater transitions in the microbial world. Trends in Microbiology 17, 414–422 (2009)

The introduction must set up the reader understand the problem that was being addressed, what other researchers have learned from their research into the problem, and how this manuscript is going to compliment and add new data to the previous research.  Some topics I would like to see discussed are: 1) how are zooplankton and bacteria communities broadly influenced by salinity changes (e.g. fluxes in richness or shifts in structure) or other factors, 2) how do the change to (1) influence the functional genes present (e.g. genes related to decomposition or other important cycles) or ecological processes (e.g. nutrient cycling) occurring in these systems, 3) What has been missing and how does this study complement or improve upon that.

Specifics:
 Lines 30-32: None of the citations used in these are examples of zooplankton or bacteria being impacted. While it is helpful to show how other communities are impacted, I am not sure how insects or angiosperms studied in Gutierrez-Canovas et al. and Zhang et al., respectively, give a good indication of how zooplankton or bacteria are impacted by salinity. Further, Mayfield et al. does not discussion salinity at all and is not appropriate to be used in this case.
Lines 34-36: This should be moved to the last paragraph as an introduction to what you will discuss later on and why you did this study.  In this spot, it is confusing since there has not been much discussion about any of the important literature.
Lines 37-48: I think this is a good start to the introduction and should be combined with lines 30-32 and then greatly expanded upon. Limit or add more literature review of how the organisms being examined in this study (zooplankton and bacteria) are impacted by salinity changes or intrusions. A few studies to examine can be found referenced above.
Lines 56-58: Salinity is also an important determinant of bacterial communities as well. This should be emphasized.
Line 58: Stagg et al. is not an appropriate reference. The focus is on soil environments and on plant communities and does not measure bacteria richness at all.
Lines 62-75: The authors would be better served by not focusing on a review of the study and what you did. Shorten this down to two-three lines of a review of the methods, the take-home results, and why this is interesting data.

Methods

The general overview of the methods I understand; however, I found the specifics on how the mesocosms were made and maintained a bit confusing.  I would like to see that section of the methods cleared up.  See below for the details on what was confusing.

Specifics:

Lines 76-84: How were these mesocosms put together? What water was used to fill the experimental ponds? Was that water sterile or from the tap?  If it was tap water, could that community present (usually as a biofilm) influence the microbial community you were examining?
Lines 81-82: How were the five different source water used?  As written, I am assuming that initially all five were dumped into each tank; however, it is unclear if that was the case. If each treatment was seeded with a different pond how might that influence how the communities respond over the duration of the experiment? For instance, if you seeded one with a starting community that was at a salinity at 5 then it most likely all ready had a starting community more resistant to salinity fluctuations (fresh to brackish) vs. a community you seeded from a pond at a salinity of 0.  This is important since you are comparing all the different treatments as if you began with a similar starting community. Further, for the source tanks, where were these communities from?
Line 81: The use of bacterioplankton is incorrect here and throughout the manuscript. Since the water was not filtered to remove particle-associated organisms this study is looking at whole bacterial communities rather than only the plankton portion.
Lines 133: delete “concentrated from” and replace with “extracted from”.
Lines 137-138: redundant to the line above.
Line 139: Since the water sample was not size-fractionated, bacterioplankton were not focused on. The water samples most likely represent both particle-associated and free-living organisms.
Lines 139-141: What chemistry was used?
Lines 142: The raw sequences would contain both archaea and bacteria unless there was a pre-step filtering process. If a filtering process was done prior to analysis it would need to be stated. Otherwise, the sentence should be corrected to “raw sequences”.
Line 144: Silva database should be cited
Line 146: Terminology: Sequences aren’t binned, a term often used in metagenomics, but most likely clustered. If they were clustered in MOTHUR which program was used (e.g. cluster_split() or?).
Lines 161-162: How was “and the interactions between time and salinity and salinity and mixing” incorporated into the model? Further, can the authors expand how “… random effect of replicate over time to account for repeated measure” was calculated and incorporated? It may be helpful by putting this all in a equation form.
Lines 178-179: Since you are using these two as proxies, it would be helpful to describe why in the introduction? Why use these two over primary production or other nutrient cycles.

Results

Lines 229-238: There is a ton of noise in this data between and within treatments. For instance, by eye, it would seem that the decrease in richness was largely driven by the increase in mescosm salinity 0 and decrease in the mesocosm salinity 9. The other two mesocosms (salinity 5 and 13) would seem to have almost no change on average. I would be curious if there was a statistical difference between mesocosm salinity 0 and mesocosm salinity 13 at day 45 or a statistical difference between salinity 5 or salinity 13 at day 0 and day 45, respectively. For instance, if you follow salinity 5 over time it would appear to increase in richness compared to day 18, but be more similar to day 0. Moreover, while there is a lot of fluctuation in richness for salinity 13, it seems it stayed pretty consistent with the exception of one point that saw an extreme drop in richness. The only system that appears to have a dramatic decrease in richness is mesocosm salinity 9. For that reason, I think it would be important to analyze these different mesocosms individually to see how the community and richness change over time rather than all together. The individual trends could then be used to help facilitate downstream analyses for comparing how salinity impacts.
Figure 3: Why on day 45 do the dots appear to shift over from their designated salinities? Did the mesocosms overall salinity?

Section 0.5.2: For the PCoA done, how was this created? What distance was used? Since PCoAs don’t take abundance counts, did the authors use UniFrac to calculate distance matrixes? If so, how was this done (e.g. MOTHUR)?

Section 0.6.2: The general trend is to increase, however, a look at the data would show that mid-level richness there were massive spikes in carbon remineralization that then goes back down. Why do the authors believe this happened? Are there any OTUs that the authors can tie to these spikes (e.g. specifically correlated)? Why are the authors only using richness and not the OTUs? Like indicator species, correlations of OTUs to the environmental data collect (e.g. carbon remineralization or decomposition) would massively improve this manuscript. It would help put into context what organisms were involved in it? Were the organisms that were not really abundant and then spiked? Were they organisms that potentially weren’t there but then introduced through mixing?  These type of questions help put context to the increase, decrease or no change in richness since abundance is not considered in richness calculations. For instance, over time richness may not change, but the OTUs present may fluctuate. Therefore, the authors may miss relationships between fluctuations of an organism and decrease/increase in decomposition or remineralization.

Discussion
Much of the literature used in the discussion is on zooplankton or higher-level organisms, yet the majority of correlations and trends were found with bacteria. The literature should reflect that to help put your positive results into context of what has previously been found with bacteria and abiotic changes and their impact on ecosystem function.
Line 301: This hypothesis was not introduced anywhere else in the manuscript. If this is something you want to discuss it should be at the end of the introduction so that we know why you are doing the methods you are.
Lines 324-325: Is it the change in richness (e.g. more OTUs) or the increase in abundance of an individual OTU or OTUs that led to this correlation. By looking at abundances increase richness would mean the importance of the introduction of new OTUs from other sources (e.g. immigration) rather than the local community. If the latter is the case then this should be discussed.
Lines 333-335: If this is the case then how would you get an increase in richness? Increased richness is the result of increased immigration from outside sources. Therefore, if mixing was not where the increased richness was from, where were the new OTUs from (the moss?).
Lines 340-341: Stagg et al. did not measure bacterial richness. They inferred some about salinity impacts on microbial community structure and decomposition but they provide no direct data of richness and decomposition as suggested by these lines.


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

Input:
Title: EFFECTS OF DIVERSITY AND COALESCENCE OF SPECIES ASSEMBLAGES ON ECOSYSTEM FUNCTION AT THE MARGINS OF AN ENVIRONMENTAL SHIFT
Review round: 2
Reviewer: 1

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: The authors answered all of my questions and concerns from the first review. I believe this has greatly increased the focus and reproducibility of the experiment. I have no further revisions for this manuscript. My only suggestion to the authors would be a potential rephrasing of their 3rd intro paragraph (Lines 53-65). I completely understand the authors are trying to unpack the effects salinity has on biological communities. However, the claims about microbial communities could be adjusted. For example they end the paragraph by saying there will be a decrease in bacterial functional processes with increasing salinity. While some processes might be suppressed (e.g. methanogenesis, nitrification), other processes would be enriched for ( e.g. sulfur oxidation and reduction). Therefore, I would suggest the authors adjust this paragraph to say that salinity is known a known driver of microbial communities and the biochemical cycles they mediate. This claim is widely accepted, whereas I would not be surprised to see papers that find moderate increases in salinity increase the abundance/functional potential of certain freshwater communities. However, this is only a recommendation, and I do not this it is a required edit.


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

Input:
Title: EFFECTS OF AUXIN DERIVATIVES ON PHENOTYPIC PLASTICITY AND STRESS TOLERANCE IN FIVE SPECIES OF THE GREEN ALGA DESMODESMUS (CHLOROPHYCEAE, CHLOROPHYTA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The structure and language are clear and have publication quality, except for minor corrections indicated below and very minor ones directly in the annotated PDF.

General linguistic matters
A.	I strongly recommend improving the title since a genus as a merely taxonomic unit cannot have stress tolerance or something like that, but only its species or strains. Although the title would become longer, it is suggested to change the end of the title into ….in five species of the green alga Desmodesmus.
B.	For the citations in the Introduction Section, I recommend only providing the citation in brackets at the end of the sentence. The present form of “XX says that…(XX + year) is redundant and puts the main message into the dependent clause and the less important information about the author into the main clause. In the Discussion Section this style appears to be ok for stressing the conclusion of the cited authors which is discussed in the light of the new findings. But here the year should be mentioned directly behind the author name: XX (year) says that… This format may be more troublesome for the Editorial Office, but given the high publication costs the Editorial Office should provide every possible service to the authors!
C.	The references are ok in my random checks, but all scientific names should be given in italics!
D.	In Fig. 1, writing the concentrations directly as 100, 200, and 300 “uM”(!) should be deleted, since this information is given in the bar as well as the legend, and the writing error of u for micro can be avoided.
Experimental design: The effect of plant hormones on plankton responses is investigated exemplarily experimentally with IAA and derivates for the plant hormones and different species and strains of the fresh water green alga Desmodesmus. The responses of the algae include total increase of cell numbers and numbers of cells per colony and by this also size of cells and colonies. The number of cells is important in potential interaction with other aquatic organisms. The sizes of cells and colonies additionally influences buoyancy of planktonic organisms.

The present study is one of the few experimental contributions in this field and provides important clues for interpreting field observation of plankton ecology.

I am sure that the authors have applied the correct methodology, but they need to explain several methods not described in the text as I suggested in the validity box.

The above comments are also sent to the Editor.
Validity of the findings: I am convinced that the experimental design and conclusions are all valid, but the Materials & Methods Section requires some fundamental complementation and some conclusions should be discussed more carefully:
1.	Deposit of vouchers: Physical voucher strains or specimens are a basic requirement for reproducibility of the identification; lack of such vouchers in responsible journals leads to rejection. It is a particular strength of this study that the authors isolated and identified their algae themselves instead of simply ordering well-identified, but perhaps physiologically degenerated strains from a collection. In contrast to some other publications dealing with identified species, here species were identified. These new and well characterized biological resources are too important for not depositing them in a publicly accessible collection.
2.	The methods for identification well described in the Materials & Methods are not mirrored in a paragraph in the Results. Please, provide the results of your species identification explicitly by briefly listing the species and numbers of strains per species. Please specify the range of bp identity in the BLAST search and the also the gap of how many bp which are different to the next closely related species.
3.	The methods for measuring “growth” are not explained, but can only be concluded from Fig. 1 where OD is indicated. Please, explain how OD was used in the Materials & Methods and whether cell density is linearly correlated with the number of living cells. If chlorophyll content was used for measuring the OD, it is possible that chlorophyll content is changed under different conditions without parallel change of the cell numbers?
4.	Was or how was the initial amount of algae defined for the experiments?
5.	How were the concentrations of IAA and other compounds selected for the experiments? Are these concentrations similar to those in plants or in the freshwater environment? This should also be mentioned in the Discussion Section for indicating the ecological significance of the experimental findings.
6.	In the use of auxin-inhibitors and other experiments derived from the Arabidopsis methodology, please, be more careful in making conclusions, if it is not been carefully tested whether the mechanisms in Arabidopsis are really the same as in the green alga. The presence of a pyrenoid is a clear evidence that physiology of algae is not just the same as in angiosperms.
7.	What was the agar concentrations in the agar plates?
8.	Was the CA medium autoclaved? (some reviewers/journals even require providing the brand name of each compound! I do not think that this would be important for this experiment)
9.	What kind of grids and coating were used for electron microscopy?
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: EFFECTS OF AUXIN DERIVATIVES ON PHENOTYPIC PLASTICITY AND STRESS TOLERANCE IN FIVE SPECIES OF THE GREEN ALGA DESMODESMUS (CHLOROPHYCEAE, CHLOROPHYTA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this manuscript, the effect of indole-3-acetic acid (IAA), an auxin constituting a class of plant hormones, on the phenotypic plasticity of different Desmodesmus species was investigated based on the previous findings on Desmodesmus opoliensis and Desmodesmus komarekii. The results were found to be strain-dependent in other Desmodesmus species, namely, D. armatus, D. communis, D. apoliensis and D. intermedius and discussed in terms of the advantages of individual-level heterogeneity among planktonic microorganisms.  Exposure of D. komarekii to IAA lead to an increased resistance to various stress conditions similar to earlier findings on bacteria. In addition to IAA, structurally related auxin analogs, naphtalene-1-acetic acid (NAA) and 2,4-dichlorophenoxyacetic acid (2,4-D), and auxin-related inhibitor compounds (4-biphenylboronic acid and 2,3,5-triiodobenzoic acid) were also used and they were shown to inhibit the growth of Desmodesmus.
4-biphenylboronic acid (BBo) and 2,3,5-triiodobenzoic acid (TIBA) are not included in the final paragraph of introduction describing the general experimental procedure. The fact that they are types of auxin inhibitors is mentioned first in Fig 1 legend and is not understood well from the legend. They are explained later in results line 216. If an explaination is given in the introduction final paragraph, it would be easier to understand. Also the figure legend should be more explanatory.
Results starts with the title Effect of auxin analogs… However, inhibitors of auxin biosynthesis or transport was also given in this section. Therefore, it would be good to change the name of the section accordingly. Line 220 states the inhibition of D. komarekii growth with TIBA and BBo and later it is speculated that auxin transport and inhibition of YUCCA function could be the reason. It could be discussed in more detail in the Discussion section.
In the results part, line 227 says indole derivatives had divergent effects... and refers to Fig 4-11. Later in the next paragraph, Fig 4-6 are mentioned (line 240) and Figure 4 results are described later (line 241). Then it is jumped to Fig 8 (line 252). It makes confusion and breaks the coherence. I think it would be better to arrange the figure numbering in a more clear way.
Figures 4, 5, and 6 gives the results of different compounds (Fig 4 IAA, Fig 5 2,4-D and Fig 6 NAA) on three strains of D. armatus. However, Figure 7 gives the result of three compounds on the fourth strain. Why giving Figure 7 with a different version than 4, 5, and 6? Figure 7 could be deleted and the data can be presented to be a part of Fig 4, 5, and 6 as the fourth strain.

The manuscript might benefit from English editing. Several grammar errors are:
line 59 a numerous, erase “a”,
line 73 a selection pressures,
line 92 role “of” plant hormones,
line 120 instead of provided: yielded,
line 121 instead of are: were
Line 215-215 an auxin biosynthesis inhibitor”s“ erase s
Line 235 …derivatives, four strains…
Line 235 four strain”s”
Line 236 erase each
Line 239 chemically synthesized?
Line 240-241 Sentece starting with moreover needs revision
Line 572 Figure 1 legend first sentence needs revision such as: …several auxins and ihibitors of …
Line 302-305 Please restate the sentence.
Line 318-319 repeat of the same phrase
Line 359 Instead of “these”, Microalgae
Line 403 erase responses

Minor editing errors:
line 111: 3000xg,
line 118: ITS1-5.8S-ITS2,
line 124: Inc”.”
Line 344: lateral organ boundaries-domain harboring transcription factor?

References: Please go through the references to make them uniform
-	Some are written long (Bianco et al., 2006), some as abbreviation (Chung et al., 2018), some with capital letter in each word, some not…
-	De-Bashan et al, 2008 was written as upper case
-	Microorganism names should be written in italic, a couple of examples: Donati et al., 2013, Bianco et al., 2006, … etc.
Experimental design: Original primary research within the scope of the journal, research question is well defined and relevant. How the research fills an identified gap is indicated.

Other comments are indicated in part 1
Validity of the findings: Comments are indicated in part 1.
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: EFFECTS OF AUXIN DERIVATIVES ON PHENOTYPIC PLASTICITY AND STRESS TOLERANCE IN FIVE SPECIES OF THE GREEN ALGA DESMODESMUS (CHLOROPHYCEAE, CHLOROPHYTA)
Review round: 2
Reviewer: 1

Output:
Basic reporting: All my previous suggestions have been satisfactorily considered in the revised version. I only made some corrections of minor writing errors.
Experimental design: All my previous questions concerning methodology have been satisfactorily answered in the revised version.
Validity of the findings: The authors have clarified all the open questions addressed in my previous review.
Additional comments: Please, check a few writing errors. You did a great job with this study!


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

Input:
Title: EFFECTS OF AUXIN DERIVATIVES ON PHENOTYPIC PLASTICITY AND STRESS TOLERANCE IN FIVE SPECIES OF THE GREEN ALGA DESMODESMUS (CHLOROPHYCEAE, CHLOROPHYTA)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript is a revised manuscript and I see that the authors have improved the manuscript during revision. The coherence is better and the figures are easier to follow upon revision, but I still have some suggestions:

-	Please take the sentence (line 231) “By contrast, we found that the auxin-related compounds NAA and 2,4-D both inhibited the growth of D. komarekii in a dose-dependent manner, but they did not influence their number of cells per coenobium/individual colony (Fig. 2d, e).” to the previous paragraph where you are explaining Figure 2.
-	Please take the sentences (line 234-238) to the first paragraph of Results where you are explaining Figure 1.
-	Please provide legends for supplementary figure 1 and 2.
-	Figure 2 legend: please refer to a, b, c, d, and e parts of the figure for clarity
-	Figure 5: I think D. armatus JYCA039 (part of Figure 5) should be transferred to Figure 4, because Figure 4 has the results of the other three D. armatus strains.

Minor points:
-	Abstract, first sentence: algae
-	Introduction, line 92: instead of Therefore, In addition.
-	Line 94: an Arabidopsis…
-	Line 98: elucidating
-	Line 107: please transfer “for more details see Supplementary Materials” to line 105 after “with 0.8% w/v agar”
-	Materials and Methods, line 187: In the abovementioned experiments
-	Results, line 191, title: the inserted phrase, make the first letters capital
-	Dicussion, line 358: please erase one of the a’s and use small letters
-	Discussion, line 371: instead of if, because?
-	Discussion, line 433: amounts…were
-	Discussion, line 436: IAA that many… can secrete
-	Discussion, line 436: similar to…
-	Discussion, line 438: can even secrete
-	Discussion, line 439: ug->μg
-	Figure legends, line 619: inhibitors
-	Figure legends, line 622:and a potent
-	Please add Table S1 to the title of Supplementary table.
Experimental design: No additional comment
Validity of the findings: No additional 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: SEASONAL PATTERN OF INFLUENZA AND THE ASSOCIATION WITH METEOROLOGICAL FACTORS BASED ON WAVELET ANALYSIS IN JINAN CITY, EASTERN CHINA, 2013–2016
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, the English language should be improved. The current phrasing makes comprehension very difficult. Some examples where the writing needs to be developed include lines 72, 184, 248, 251, 258, 265, and 299-304.

The article aims to explore the association between several meteorological factors and influenza spread and infection. There are some suggestions spread in the discussion about the mechanisms by which these factors could lead to particular influenza patterns, but since it is a central issue in the manuscript, there should be a separate section in the introduction as a context.

The structure of the article seems to conform to an acceptable format of ‘standard sections.’ The submission appears ‘self-contained.’
Experimental design: The knowledge gap that is intended to fulfill in this analysis is not clearly defined in the manuscript. It is not clear whether the main aim was to describe the synchrony in the timing of influenza epidemics and meteorological factors or to find causal relations between them. Both intentions are stated.

My main concern regarding the analysis strategy is that the study makes explanatory conclusions from bivariate analyses, comparing meteorological variables that are highly correlated, and omitting several pertinent variables. Meteorology is not my specialty, but intuitively and looking at the provided data (Fig. 1), the correlation factors in Table 1, and at some basic literature, meteorological factors as humidity, temperature, atmospheric pressure, wind speed, rainfall, and sunshine duration are highly interdependent. Any separate analysis would mask mediation and confounding mechanisms.
Furthermore, influenza virus subtype (e.g., H1N1, H3N2, B, etc.), that have shown to have considerable influence on the spread and severity of influenza epidemics are omitted from the analysis. This omission is surprising since the analyses are done using laboratory-confirmed influenza information. It is possible that the information at the local level is not available (something that is not mentioned in the paper), in which case other geographical scales could have been used as proxies for virus subtype circulation.
The analyses using the cross wavelet transform and wavelet coherence have the same problem as the bivariate correlation analyses also employed. Since most meteorological phenomena are interdependent, there is no way to identify the real association by restricting the analysis exclusively to bivariate comparisons of seasonal patterns. My thought on this is that these are only measures of synchrony in timing, but they are not able to establish causal relationships.
Although statistical measures and sensitivity analyses can justify such bivariate analyses, there is no justification for the study design employed in this case. As an example, other studies cited by the authors (Yu et al. 2013 and Tamerius et al. 2019) use more robust multivariate analyses, including meteorological variables, as well as influenza virus subtype circulation measures to identify associations between meteorological factors and influenza patterns.

The description in the method section is confusing in several parts. For instance, the description of the construction of the arrows is not well described (lines 139-140). It is not clear about which arrows are being described.

The description, labeled, and aesthetic of the Figures should be substantially improved to conform to an acceptable standard. Some examples where the Figures need to be improved include:
In Figure 1, several kinds of plots are used (bars and lines), and some of the measures are combined without apparent reason (atmospheric pressure and wind speed). I suggest unifying the plot aesthetic when possible and combine measures that are more related, as mean and minimum temperature, for instance. Also, units for the Y-axis should be added.
Captions in Figures 2 and 3 are switched.
X- and Y-axis in wavelet plots (Figures 2 and 3) are not correctly labeled. The x-axis should be something like “time-period (weeks)” and Y-axis something like “frequencies or scale (weeks),” as stated in the captions.
Less imperative but still relevant, I suggest using another palette of colors than rainbow for a continuous scale, as in the case of wavelets. The rainbow colors palette has several drawbacks that have been pointed out elsewhere. For instance, it can induce the perception of ruptures where there is continuity and can make real ruptures appear as a continuous gradient. Some further details: https://www.scientificamerican.com/article/end-of-the-rainbow-new-map-scale-is-more-readable-by-people-who-are-color-blind/?redirect=1
https://www.mathworks.com/tagteam/81137_92238v00_RainbowColorMap_57312.pdf
Validity of the findings: The data on which the conclusions are based is provided.

As mentioned above, the analysis design performed does not allow inferring causality between climatic factors and influenza infection. In consequence, several statements suggesting this kind of relation throughout the text should be avoided and nuanced. Some examples of these expressions are: “We found weekly change in climate variables significantly contributed to dynamic variation of influenza virus” (line 244), “we also found that the influenza seasonality was determined by some of the relative climatic factors” (line 297), “[climatic factors] played important role in shaping influenza seasonality” (line 309-310), “led to” (line 311), and “[we] exploited the impacts of climatic parameters on influenza virus”.
As stated in the guidelines of the journal, “Speculation is welcome, but should be identified as such.”
Additional comments: Besides the points highlighted above, some minor issues:
In the data section, it is stated that influenza-like illness is used in the analysis, but the only influenza information used is laboratory-confirmed influenza.
Maybe I am reading badly the statistical significance in the wavelet plots, but in lines 169 and 175 it is said that the frequencies in the 32-64 week band are not statistically significant, but the black line indicates the opposite.
Line 198, it is written 214 but is 2014.
In line 216 it should be Fig. 3F, not 3G.
In line 216 it should be Fig. 3F, not 3G.


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: SEASONAL PATTERN OF INFLUENZA AND THE ASSOCIATION WITH METEOROLOGICAL FACTORS BASED ON WAVELET ANALYSIS IN JINAN CITY, EASTERN CHINA, 2013–2016
Review round: 1
Reviewer: 2

Output:
Basic reporting: •	English language: the paper has a lot of mistakes and definitely need to be reviewed. I tried to help by making notes about things that need to be changed and I will send the scanned version with my notes. The transcription here following the guidelines in impossible, because would require to re-write almost the full paper. I strongly recommend the use of Grammarly or a similar app to help with the grammar and phrasing.
•	Literature references: I missed the results from China in the literature review. As the paper is from a specific Chinese city, it would be important to look at findings from other places.
•	References: Please check the references. The webpage cited is in incorrect format (page 85). Some other citations are also wrong. For example: please use Tamerius et al (YEAR).
•	Figures:
o	Figure 1. Please, use graphs of one vertical axis. AH has a different scale than Wind speed, please create 1 graph to each variable. Specify in the figure’s legend the frequency of the data.
o	Figure 2: It would be better if we have more dates on the horizontal axis.
Experimental design: It is not an experimental design study.
Validity of the findings: Specific commentaries:
LINES 78-82:
•    The outcome needs to be described more clearly. What does it contemplate? The reading of these lines makes me feel that the outcome is ILI + confirmed cases. But in posterior sections, it was not confirmed.
•    Why the outcome is measured weekly and annually? If we have weekly data, and it is the most frequent date you have, we have also annual data right?
•    It is not clear the frequency of the data you are using
•    Do you have missing data? How did you treat it? Imputation? If yes, please refer to that here.
•    Please cite reference for the Jinan CDC at the first time you mention it
•    You are here presenting your data, so please specify here the type of data you will analyze (positive rate).
•    It is important to mention the coverage of the 3 sentinels. Are they all the possible health facility to people looking for care? If it isn’t please specify its coverage.
LINE 87: is the rainfall accumulated? If all meteorological variables are average, please suppress this information, not repeating it each variable is presented. You can say: “we used average measures of…”
LINE 83-89: What was the procedure used to match up the climatic to the influenza data? Both data sets are in different frequencies. Please, let it clear.
Moreover, where is located the meteorological station? Capital? Did you use data from the one closest to the sentinels?
LINES 91-96: Please, be more clear to the chronological analysis: 1) Outcome, 2) Descriptive (include correlation and normality test here), 3) Wavelet analysis.
Important: you didn’t explain to the reader why are you looking to correlation, normality test, and wavelet decomposition. It is important to briefly explain why you are using these methods.
LINES 103-117: I don’t think you have a section here. In general, researched introduce the continuous wavelet in the wavelet analysis. So, I recommend to summarize and join this section with the previous one (Wavelet analysis). Here, the most important information are the “continuous decomposition”, the wavelet mother used and the coherence statistic. In my opinion, all formula could be suppressed, but the concept of the mother wavelet and coherence should be well described.
LINE 113: you have here a citation in another format (no 28).
LINES 118-145: Again, I would suppress the formulas, and explain clearly the coherence and what the reader would expect to find in the power spectrum graphs: the area where the entropy is high, the meaning of the arrows direction and the edge. It is important also to mention the null and alternative hypotheses used to build the confidence intervals: ARIMA? IID? Seasonal and stationary?
LINE 157: Why are you testing for normality? Please explain.
LINE167: “Influenza virus presented an annual epidemic cycle…”
ALL TEXT: please, use: climate factors, not climatic factors
LINES 173-179: I would recommend you to compare the average spectrum power in the periods you are inside the edge. The average power as a whole can be diminished by insignificance from the area outside the edge. Figure 2 seems to corroborate the hypothesis that you have similar annual seasonality in all climate variables and influenza.
LINES 180-218: Please, be specific. More than tell the reader if a climate variable is leading, you should say in how many weeks the peak or minimum values are leading the influenza peak or minimum values. Without this information, you can’t establish a connection between the variables. The fact that (for example) a peak of a climate variable is not leading influenza’s peak does not mean that they are not related. To talk about a lack of relationship we should have no explanation by incubation time, virus spread time, etc.
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: SEASONAL PATTERN OF INFLUENZA AND THE ASSOCIATION WITH METEOROLOGICAL FACTORS BASED ON WAVELET ANALYSIS IN JINAN CITY, EASTERN CHINA, 2013–2016
Review round: 2
Reviewer: 1

Output:
Basic reporting: The text is clear and unambiguous.

There are some small typos, for instance, in lines 294, 319, 321, 328.

There are problems with the captions of Figures 8 and 9. The virus subtype mentioned in the description is not the correct one.

The link provided for the Mathlab package in line 142 does not work. I also think that besides the link, the authorship of the package (Grinsted) should be better cited in the manuscript as a reference

The color scale in the wavelet plots is not pink to white. It seems more like dark-brown to white.

Change "atmosphere pressure" for "atmospheric pressure" in lines 352-353.
Experimental design: It would be very informative to include analyses of all-subtype influenza and compare them with the analyses by subtype. Since subtypes are competing with each other, this could affect the seasonal pattern of each subtype.
Validity of the findings: no comment
Additional comments: The quality of the paper improved considerably since the first version. Most of the issues signaled in the previous review were adjusted.

I highlight two aspects that I consider need to be addressed:

The differences across virus subtypes in the associations between climate factors and seasonality are an interesting finding. In addition to the suggestion made earlier about including analyses of all-subtype influenza, I find that it is imperative to mention if there is a possible interpretation of these differences across subtypes. Its is not clear for me whether these differences were already noticed in previous work, or this is the first study to report them.

My main concern with the previous version of the manuscript was the fact that statistically significant associations and co-movements were interpreted as causal relationships. I find that this issue is very well addressed in the discussion of the new version of the paper, by clarifying that these are potential relationships suggested by the theory and results. However, at the end of the discussion (lines 339-342) and in the conclusions, there are still strong sentences indicating causality, by using verbs such as “influenced” and “shaped.” I suggest employing more cautious statements for interpreting the findings, as it was done in most of the discussion section.


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: SEASONAL PATTERN OF INFLUENZA AND THE ASSOCIATION WITH METEOROLOGICAL FACTORS BASED ON WAVELET ANALYSIS IN JINAN CITY, EASTERN CHINA, 2013–2016
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript has improved a lot since the last version.

Basic Reporting
·      English language & formating: the language improved a lot, but we still can find some grammar mistakes. I am sending my notes scanned, in case it helps.
·      Figures: all problems were solved, and the pictures have improved a lot.
Specific commentaries:
·      Methods – Influenza surveillance data: How much the three sentinels represent in terms of influenza offer of care? Please specify its coverage.
·      LINES 262-263: please make it clear what combination are you referring to.
·      LINES 340-343: all the linear correlations obtained are very small. I wouldn’t attribute to influenza B a relationship with temperature if the wavelets didn’t point out to that.
·      LINES 364-365: same commentary above.
Experimental design: The research question is original and challenging, but it could have its epidemiological implications better explored in the discussions.
The methods description improved a lot!
Now, it is clear what data they have used, the frequency and statistical procedures throughout the analysis.
Validity of the findings: The authors relied in a lot of methods, and it makes it difficult to have a clear and objective conclusion.
The data and all graphs have been provided, and they are in line with the results and conclusion sessions.
Additional comments: It lacks and explanation to the different sets os variables found as associated with the influenza subtypes. I would invest a little more on that to move the quality of your work one step ahead.


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: SEASONAL PATTERN OF INFLUENZA AND THE ASSOCIATION WITH METEOROLOGICAL FACTORS BASED ON WAVELET ANALYSIS IN JINAN CITY, EASTERN CHINA, 2013–2016
Review round: 3
Reviewer: 1

Output:
Basic reporting: In general, the quality of the text is unambiguous and professional.
However, there are still several aspects that should be adjusted to reach publishable quality. Some examples (not the only ones):
- Through the text, it is used both “climate factors” and “climatic factors” (lines 212, 353).
- Lines 219-220: “In terms of temperature, in the 26-week band 220 (2013–2014), influenza virus A (H1N1) pdm09 was negatively correlated with the left arrows.” This could lead to misinterpretation because there is no correlation “with the left arrows”, but the arrows indicate the negative correlation.
- The word “virus” is overused in some sections. e.g., it is repeated 13 times in lines 269-275.
- Line 164: "Figure 2D", but it actually refers to Figure 2E.
- Lines 215-235: The results described correspond to Figures 5 and 6, but there is no explicit reference to these plots in the text.
- Lines 266 and 341: "in which" instead of "that"
- Line 294: "obtained" is not the appropriate term here.
- Line 297: "lags" instead of "lag"
- Lines 331, 339, 345, should be "a" instead of "the"
- Line 361: not clear what the expression "and people" means.
- Lines 325 and 368: "illuminated" might not be the appropriate term.
- Lines 373: "elaborated" might not be the appropriate term.
- There are several typos in the main text, e.g., spaces lacking in lines 154, 160, 161, 164, 173; other typos in lines 362, 366...
Experimental design: Most of the findings were obtained using wavelet plots, but the components of these plots are not described in the method section. There is no reference to the meaning of the arrows, their direction, the colors, the thick black curves, or the cone of influence in this section.
Part of this information is written in the results section, but it is spread here and there, and part of it seems incorrect, as will be detailed below. The caption of the figures is the only place where this description is done. this description should be better organized and has some substantial contradictions with the information consigned in the results section.
More precisely, in the results section (lines 193-194) is written: “The cone of influence separates the reliable (white colors) and less reliable (pink colors) regions.” In contrast, in the caption of Figure 1 is written "The cone of inﬂuence separating the regions with reliable and less reliable estimates is represented by the lighter pale colors.  […] The region outside the black-curved cone indicates the presence of edge eﬀects.” Both descriptions are contradictory, and it seems that the latter is the correct one.
As stated in the caption, the scale white-pink is not related to the cone of influence (edge effects) but to the “power” of the correlation (“The color code for power ranges from pink (low power) to white (high power)”).
Validity of the findings: Some expressions are not supported by the results.
- Line 294: "atmospheric pressure influenced the variations in different influenza virus types".
- Line 297: "Furthermore, during some time periods, the prevalence of influenza virus 'lag' the changes in atmospheric pressure, which can predict the occurrence of influenza virus A(H3N2)epidemics."
The study does not provide support to affirm that atmospheric pressure "influence" or "can predict" variations in virus subtype.
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: CHANGES OF CELLULAR STRESS RESPONSE RELATED HSP70 AND ABCB1 TRANSCRIPT AND HSP70 PROTEIN LEVELS IN SIBERIAN FRESHWATER AMPHIPODS UPON EXPOSURE TO CADMIUM CHLORIDE IN THE LETHAL CONCENTRATION RANGE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Remarks to Protopopova et al. : Investigation of cellullar stress response … in Siberian freshwatwer amphipods upon cadmium exposure.

This ms addresses an important aspect of stress ecology, the stress tolerance of endemic species from remote areas. The topic itself therefore warrants publication but the manuscript needs considerable revision.
The authors just describe their results in a rather simple way and solely conclude that molecular stress responses in amphipods from the Baikal follow ˈdifferent adaptation strategiesˈ and are rather ˈinsensitiveˈ. This, however is, to my opinion, just part of a much more interesting story. In fact, most of the amphipods died from Cd contamination before they could counteract stress symptoms biochemically. How come? Usually protective biochemical responses such as hsp70 induction (but also MDR-related gene activation) increase at lower concentrations than the LC50. There are many examples in the literature for this phenomenon (e.g., Brulle et al. 2006: Environ Sci Technol. 40, 2844-2850; Werner & Nagel 1997: already cited in the ms). In species from extreme habitats, however, this rule does not always apply, e.g. in ice fish which apparently do not express hsps at all. So, also in the Baikal, with its pristine water, its location in a remote area and without experiencing challenges by heat due to Siberian climate, the lack of strong selection pressure for an effective biochemical stress response system apparently has left abundant biota non-adapted to stressors, including the artificial stressor cadmium. Such argumentation would put the results of the authors in an evolutionary context and, additionally, has implications for a presumed vulnerability of these endemic species to pollution.

In the para lines 63-67, the authors simply state that, quite often, molecular effect data are generally not related to cadmium stress. This is only true, if linear or, generally, monotonous concentration-response relationships are anticipated. However, it is long known for stress proteins, including hsp70, but also other biochemical stress responses that quite often the molecular stress response collapses at concentrations lower than the LC50, due to down-regulation, pathologies etc. So, as a rule, molecular stress responses follow non-monotonous response curves with a maximum response at a given concentration and declining levels at further increasing pollutant concentration. Consequently, the statement of the authors in lines 63-67 is imprecise – already 20 years ago, the relationship between stress gene transcription, stress protein formation and demographic parameters such as mortality and reproduction has been exemplarily documented in a model snail species (Kohler et al. 1998: Environ. Toxicol. Chem. 17(11), 2246-2253).

The authors have kept and exposed all amphipods at a constant temperature of 6.5 – 7.0 °C. While this corresponds to the habitat temperatures of most tested amphipod species, it was probably too cold for E. vittatus (2 – 6°C colder that in its natural habitat). So, can the authors exclude the high mortality (line 244) in this species to result from non-physiological, low temperatures? In fact, Fig 1 does not really support the interpretation of the authors for a gradual increase in mortality in the species´ order given in lines 243 and 244, as confidence intervals for the species-specific mortality curves largely overlap, and only the one for E. vittatus differs from all the others – eventually due to the artificially low temperature which may have resulted in a metabolic depression (in contrast to the interpretation given in line 312).

A main point that necessarily has to be addressed in a revised ms is the non-justified pooling of data deriving from different LCx exposure across different species in single datasets and figures, and ˈconclusionsˈ drawn from such approach. For example, in Fig 4 each data point is defined by a specific LCx value and a – strongly covariate – specific species. It is impossible to tell LCx from species and, thus, the calculation of a regression curve on the basis of solely LCx is scientifically incorrect. The same applies to figures 2, 3, and 5. Should the significance in the data of the rightmost column in Fig 5 really be attributed to the LC90 or rather the species G. lacustris? In a revised ms, all data necessarily need to be separated according to the respective test species!

Lines 265/266: This function is definitely not Gaussian but non-monotonous with a local maximum.

Lines 360-362: The mechanistic interpretation proposed here (concomitanly high levels of hsps and metal-binding proteins) is in contrast to the results of Haap & Kohler 2009 (cited in this ms) who showed a trade-off between metal-binding proteins and hsps.

Why did the authors quantify the level of an MDR-related gene, abcb1? The MDR transporters are able to confer tolerance to organic compounds, but not cadmium. Inclusion of metallothioneins in this study would have been much more relevant in this context.

Even though the English is readable, the text, particularly in the Discussion, follows some foreign syntax and style. The authors are strongly recommended to have a revised ms pre-checked by a professional prior to submission.
Experimental design: see above
Validity of the findings: see above
Additional comments: Ms should be largely re-written. This seems to be possible but will require consideable input.


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: CHANGES OF CELLULAR STRESS RESPONSE RELATED HSP70 AND ABCB1 TRANSCRIPT AND HSP70 PROTEIN LEVELS IN SIBERIAN FRESHWATER AMPHIPODS UPON EXPOSURE TO CADMIUM CHLORIDE IN THE LETHAL CONCENTRATION RANGE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please see comment below - in general the language needs some improvement. The structure, background and referencing is according to standards in the field . The results are relevant but discussion would benefit from linking the finding more with their meaning in the context fo the work or beyond.
Experimental design: Design is rather clear, with a research question being clear to me and well addressed. some more detailed comments are below:
L108	please specify the waters nutrient levels and other quality parameters.
L114ff	How did the difference in Biomass for each of the species influence the bioavailability of Cd over time? 2 L is a high volume but also amphipods of a mass around 10 g would not be considered low. As this biomass varied among species, could this have any impact on the effects that one observed?
Validity of the findings: The replication seems partly relatively low but this is balanced by a repetition of the experiments. The data are provided - more detailed comments are provided in the following lines

Results
General: it is realized in some cases, but a more general consideration of effect sizes and not statistical significances is, given the heavy criticism of the latter approach, more favorable and should be prefer. Moreover exact p-values should be reported, ideally with the clear information on the replication (if possible)
L241	I assume “varied over an order of magnitude” was meant here?
L243	It is generally confusing to refer to CdCl2 as toxicant and based on this it is unclear to me whether the LCx values refer to Cd or CdCl2. I would suggest to provide information in Cd. Irrespective of this, the point needs clarification.
L276	What kind of increases is referred to here? The increases based on statistical significance? Please be specific.

Table 1 and figure 1 do largely represent the same thing – duplication of information should be avoided. Moreover, in the table, the CIs should be reported at all levels for full transparency.
Figures: I would suggest to provide instead of LC values in all the figure son the x-axes the actual concentration. The LC values are a kind of confusing and not intuitive for a reader who is not willing to read the full paper. Also the figure captions should help to explain why those concentrations have been chosen.

Discussion
The chapter would also clearly improve from some language polishing taking advantage of an expert in the field. For instance, “toxicological sensitivity” would just be “sensitivity” or “cause of toxic action” – “mode of toxic action”. Seems there are some technical terms lacking which would greatly improve readability. Moreover, it seems that some data are “just” repeated but not put into context (see L313ff but also L336f and elsewhere).
L290	Please rephrase sentence – the message is not 100% clear to me.
L297	Why only to a certain extend? Some references would be helpful as would a more clear explanation for this point.
L321f	I cannot fully follow in this paragraph – I do see graphs assessing the protein levels in different species each exposed to different levels of Cd (od CdCl2) at 3 points in time. With this design, it is difficult to say something about different phases of the biological reaction as there are basically 3 points in time, which is not an overwhelming dataset and neither trend can be well support.
Additional comments: interesting work, which would benefit from the involvement of a native speaker for an English language check and also check for references and other formatting issues (see for instance L104 or 195 but also at many other occasions.).
Some other aspects are:
Abstract
The document seems to carry information on the sensitivity of amphipods towards cadmium including some gene expression data and protein production data. Although, I think I can follow the message, I would suggest to double check the language of the whole document since there are a multitude of grammatical issues (including lengthy sentences) which, if solved, would greatly increase the readability of the document for the target audience. What I found a little striking is that no information is provided on the response of Hsp70 proteins in the organisms. Also, the conclusion seems a little broad, considering that – according to the authors – only organisms from one region are used. I suggest to soften this statement.

Introduction
L34	An example of a unnecessarily lengthy sentence. It could be split in two, with the second half of the sentence representing a stand along one.
L39ff	The linkage between the last sentence of the paragraph and the second last sentence is unclear to me. It should be explained why these genes are expressed and what the response entails. This might be clear for the authors but might not so for the readership in more general. Also I would suggest to limit the number of references that are cited to support one statement to a max of 3-4; exceeding this number seems not necessary to make the point, that there is support for the statement in literature.
L63ff	Sadly the message of the whole paragraph is not very clear to me. Please calrify.
L68ff	Although it is likely that any set of species defers in its stress response capacities, I do not see much evidence presented until now that supports this claim for the set pf species selected – there rewording and softening the statement is advised.
L76ff	Also here I would suggest to revise as the data as presented until now does not support this claim. It is also recommended to add references that are in support of this statement.


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: CHANGES OF CELLULAR STRESS RESPONSE RELATED HSP70 AND ABCB1 TRANSCRIPT AND HSP70 PROTEIN LEVELS IN SIBERIAN FRESHWATER AMPHIPODS UPON EXPOSURE TO CADMIUM CHLORIDE IN THE LETHAL CONCENTRATION RANGE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript uses professional English; most of the used terms are similar to those in the cited bibliography.

The cited works in general help to introduce the hypothesis and to discuss this hypothesis according to the results. However, the rechecked of the cited papers such as Werner & Nagel (1997) or the inclusion of more articles can change the following sentence.

Line 63. "It is stated in many studies on the effects of cadmium on hsp70/Hsp70 levels that the test organisms were exposed to sublethal cadmium levels but the published molecular effect data are generally not related to the general level of stress caused by the cadmium concentration applied, such as lethal cadmium concentrations. It is thus unclear how sensitive the observed gene response to cadmium is."

However, Safari et al. (2014) describe the hsp70/Hsp70 genes induction using qPCR after exposure to LC50 fractions of cadmium. Also, Jung & Lee (2012) shows lethal cadmium concentration and the concentration that induced hsp70/Hsp70 gene expression also by qPCR. Mlambo et al. (2010) measured hsp70/Hsp70 proteins levels after exposure to LC05, LC10, and LC20 of three metals, including cadmium. Werner & Nagel 1997, already cited in the manuscript, shows LCx and the cadmium concentration that increased hsp70/Hsp70 proteins levels. The authors should check the findings of these manuscripts.

The manuscript has a standard structure. It describes mortality, induction of the heat shock protein hsp70/Hsp70 and the multixenobiotic transporter abcb1; and conjugated diene levels in four species of Siberian freshwater amphipods exposed to cadmium for  1, 6 and 24h.

In the abstract of the present describes a significant increase in the induction of the heat shock protein hsp70/Hsp70 and the multixenobiotic transporter abcb1 at CdCl2 concentrations similar to or higher than LC50 after 24h exposure. However, Jung & Lee 2012 and Safari et al., 2014 found induction at lower cadmium concentrations. Park & Kwak (2013) found that hsp70/Hsp70 genes were induced at very lower concentrations compared with LCx also using qPCR but after exposure to organic chemicals.

Line 25. "Induction of stress gene responses by lethal CdCl2 concentrations indicates that in the amphipods they are rather insensitive."
The pronoun "they" is OK only if the genes are insensitive.

The findings of the present manuscript could describe a particularity for amphipods, but Werner & Nagel (1997) also worked with amphipods and found an increase in hsp70/Hsp70 protein levels at very lower cadmium concentration compared with LC50

In the present manuscript, the LC50 after 24h for CdCl2 was in 1.7 mg/L in Gammarus lacustris, 2.9 mg/L in Eulimnogammarus cyaneus, 8.3 mg/L in E. verrucosus, and 18.2 mg/L in E. vittatus. However, Jakob et al. (2017) found that the LC50 after four weeks at 6°C for CdCl2 was 2 µg/L in E. cyaneus and 12.9 µg/L in E. verrucosus. Exposure duration increase sensitivity in the orders of magnitude, but this increase is species-specific. This last may help to understand the differences among the species observed in Fig. 3 over time.

Fig. 3 and Fig 4. do not show the responses for all species at the same LCx, which question the meaning of Fig. 3B and Fig 5.

References

Jakob, L., Bedulina, D. S., Axenov-Gribanov, D. V., Ginzburg, M., Shatilina, Z. M., Lubyaga, Y. A., ... & Sartoris, F. J. (2017). Uptake kinetics and subcellular compartmentalization explain lethal but not sublethal effects of cadmium in two closely related amphipod species. Environmental science & technology, 51(12), 7208-7218.

 Jung, M. Y., & Lee, Y. M. (2012). Expression profiles of heat shock protein gene families in the monogonont rotifer Brachionus koreanus—exposed to copper and cadmium. Toxicology and Environmental Health Sciences, 4(4), 235-242.

Mlambo, S. S., van Vuren, J. H. J., Basson, R., & Grant, B. (2010). Accumulation of hepatic Hsp70 and plasma cortisol in Oreochromis mossambicus following sublethal metal and DDT exposure. African Journal of Aquatic Science, 35(1), 47-53.

Park, K., & Kwak, I. S. (2013). Expression of stress response HSP70 gene in Asian paddle crabs, Charybdis japonica, exposure to endocrine disrupting chemicals, bisphenol A (BPA) and 4-nonylphenol (NP). Ocean Science Journal, 48(2), 207-214.

Safari, R., Shabani, A., Ramezanpour, S., Imanpour, M. R., & Rezvani, S. (2014). Alternations of heat shock proteins (hsp70) gene expression in liver and gill of Persian sturgeon (Acipenser persicus Borodin, 1987) exposed to cadmium chloride. Iranian Journal of Fisheries Sciences, 13(4), 979-997.

Werner, I., & Nagel, R. (1997). Stress proteins HSP60 and HSP70 in three species of amphipods exposed to cadmium, diazinon, dieldrin and fluoranthene. Environmental Toxicology and Chemistry, 16(11), 2393-2403.
Experimental design: I have no questions for the experimental design or the methodology.
Validity of the findings: The hypothesis about the insensitivity of stress genes induction to cadmium exposure should be reformulated, including previous works that have already compared LCx with hsp70/Hsp70 responses.

A high level of speculation supports the discussion about a direct relationship between internal cadmium concentration and gene expression responses because the internal concentration was not measured in the present work.  The debate about a relationship between size and cadmium sensitivity, should consider the size and the sensitivity of all species at the current work and include the species in others works with amphipods such as Werner & Nagel (1997).

The conclusions should take a dimension from the works that related gene stress responses and LCx previously.
Additional comments: I could not see the results of the Western-blotting, and the gene expression response for each combination between LCx and amphipod species.


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: CHANGES OF CELLULAR STRESS RESPONSE RELATED HSP70 AND ABCB1 TRANSCRIPT AND HSP70 PROTEIN LEVELS IN SIBERIAN FRESHWATER AMPHIPODS UPON EXPOSURE TO CADMIUM CHLORIDE IN THE LETHAL CONCENTRATION RANGE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors did consider all of my previous comments and largely re-wrote the ms in a way that addressed them. I am fine with the new version.
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: CHANGES OF CELLULAR STRESS RESPONSE RELATED HSP70 AND ABCB1 TRANSCRIPT AND HSP70 PROTEIN LEVELS IN SIBERIAN FRESHWATER AMPHIPODS UPON EXPOSURE TO CADMIUM CHLORIDE IN THE LETHAL CONCENTRATION RANGE
Review round: 2
Reviewer: 2

Output:
Basic reporting: General description.
This manuscript tests the hypothesis that cadmium exposure causes molecular responses in a direct form. The alternative hypothesis is that the molecular responses are an indirect consequence of cadmium effects.

The process of rejecting the hypothesis consists of comparing the lethal concentration of Cd with the concentration of Cd that induced molecular responses (effective concentration).

According to the abstract (page 1, line 30), The decision rule is the following:
An effective concentration lower than the LC50 indicates a direct response to cadmium.

Specific points

1-Figure 2.

The text in axis x is not precise and leads to a misunderstanding.

Page 8, line 157, two concentrations were tested in all species,
0 and 5 mg/L.

The x-axis does not distinguish between 5 mg/L and 0 mg/L, and among the species.
In the discussion, the authors can compare the of 5 mg/L with different LCx.

2-Figure 3
Similar to the previous figure, the text of the x-axis is not an accurate description of the experiment.

Page 8, line 172. the tested concentrations were the LC10 and the LC50; and 0, 1.7mg/L (LC50 for G. lacustris), and 5 mg/L.

3-Figure 4

Similar to the previous figures. Information is mixed with interpretations.
In the raw data archive, the tested concentrations were 0, and 5 mg/L.

The figure also does not clearly show the differences in the response of each species.
The reason for the adjustment is not apparent, because no interpolation took place.

4-Figure 5

Similar to the previous figures. For clarity, tested concentrations should be on the text of the x-axis.

The authors' interpretation can take place in the discussion.

5- Conclusion (Page 23, line 493)

Which would be the results for a not phenotiícally characteristic?
Experimental design: No comments about it
Validity of the findings: No comments about it
Additional comments: The authors obtained precise experimental results, but its description is confusing. This confusion can quickly solve by correcting the x-axis of the figures. Several previous works compare molecular and lethal responses to contaminants, only very little of this prior information was considered in the discussion.  In the present manuscript, the mortality curve is monotonic, but the molecular-responses curve seems to be non-monotonic. This difference should be discussed.


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: PREDICTIVE MODELLING OF THE DISTRIBUTION OF CLEMATIS SECT. FRUTICELLA S. STR. UNDER CLIMATE CHANGE REVEALS A RANGE EXPANSION DURING THE LAST GLACIAL MAXIMUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript titled “Predictive modelling of the distribution of Clematis
sect. Fruticella s. str. under climate change reveals a range expansion during the Last Glacial Maximum” coauthored by Mingyu Li, Jian He, Zhe Zhao, Rudan Lyu, Min Yao, Jin Cheng, Lei Xie is a well-written manuscript. The manuscript has good enough references and some of them relevant in the field of the study, and the aim of the manuscript is well presented.
Experimental design: The methods used to support the aims are good, but they can be better.  For example, I encourage following the GBIF citation recommendation. The variables used for the analyses are good as well as the multicollinearity analysis among variables. The present and past scenarios are good. But the authors need to explain in detail why they are using the RCPs CCSM4 among many others that exist.

The critical part of the study is to combine the five Clematis species to do all the SDM analyses. I think every species must be modeled separately and then the sum of models, for the present, past, and future will be done. Because the ecological niche is a particular and unique for each species, not for section Fruticella.
The historical aspects of the models relating to species distribution (hypothetical ‘M’ region; Barve et al., 2011) must be used for every single species.
To evaluate the performance of the models I recommend calculating the true skill statistic (TSS), a threshold-dependent measure of model performance that evaluates the accuracy of predictive maps generated by presence-only data (Allouche et al., 2006; Liu et al., 2013).
The centroid of a suitable habitat
must be evaluated for every single species.
Validity of the findings: Because the authors apply all the analyses to section Fruticella, not for every single species, it is possible that the results change and they need to discuss the new results.
Additional comments: I think your study is interesting for so many readers, but you need to apply the analyses for every single species and then discuss your findings.


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

Input:
Title: PREDICTIVE MODELLING OF THE DISTRIBUTION OF CLEMATIS SECT. FRUTICELLA S. STR. UNDER CLIMATE CHANGE REVEALS A RANGE EXPANSION DURING THE LAST GLACIAL MAXIMUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: I appreciate very much that you have thought of me for the review of the manuscript entitled “Predictive modelling of the distribution of Clematis sect. Fruticella s. str. under climate change reveals a range expansion during the Last Glacial Maximum”.

I have read the manuscript carefully, and I found if very interesting. The manuscript is written clearly and uses a good English language. The literature is useful and well referenced at the end of the manuscript. The figures show high quality and they are well labelled to help the reader. Most interesting contribution of this study is shown in the research about the effects of climate change on distribution and response mechanisms of plants.  This paper addresses a relevant question regarding climate change context where organisms are displaying different responses to future shifts that will occur.
Experimental design: I would like to enhance that the methods sound very interesting for me, and I am mostly related with them. They are reasonable and generally well justified. It is appreciated that the authors use some novel approaches. I would like to value the inclusion of 35 environmental variables, not only 19 from WorldClim database, which is the most common option on these studies. I would also like to thank you for teaching me an unknown method to test the multicollinearity, in this case using ArcGIS software. Related to this Multicollinearity Analysis test among all variables (paragraph starts line 175) finally were kept the most ecologically meaningful. I would like to recommend to the authors the Variance Inflation Factor (VIF), a measure of how much collinearity increases variance in a model implemented in HH package (Heiberger, 2017) in R.
However, below I refer to some aspects which are unclear and require a justification in my opinion.

(1)	I have a doubt relating the idea reflected in the introduction about those methods of species distribution modelling which use only presence data (Maxent) vs. others which use both presence and absence (GLM, GAM, and Random Forest). I think that the distribution of Clematis sect. Fruticella s. str. is well-known, such as is shown in the first paragraph of M&M (lines 130-149). In case that you cannot use real absence because you disown the accurate distribution of species in some region you could also use these algorithms implementing a binary response with presence and artificial absence data (pseudoabsence/background). I recommend you read the following article about this: “Selecting pseudo-absences for species distribution models: how, where and how many?” (Barbet-Massing et al., 2012 in Methods in Ecology and Evolution). If you use background you will have more points of this instead of presence. However, you could weigh given a determined value. I would like to compare the results obtained from Maxent with other algorithms. I would recommend you to use the package implemented in R “biomod2” which is used for ensemble platform for Species Distribution Modelling. Depends on your data, presences are considered as presences, absences as absences and pseudo-absences as background (recommendation is to use a large amount of random sampled pseudo-absences to be close to the background concept). With this package you could select the best model using Akaike Information Criteria (AIC).  You can use the function “background_data_dir” from BIOMOD_ModellingOptions() or some random pseudo-absence sampling at BIOMOD_FormattingData() in case that you don’t feel reliability to obtain absence data as you said in the Introduction (line 65). If this is so, I suggest that you provide a more detailed explanation in the Methods paragraph. Thus, I would like to see the estimated results but including other species distribution modelling algorithms. I think that in this study could be very important to compare the potential suitable distribution areas predicted using not only Maxent modeling scenarios.

(2)	In the Table 1 the authors show different resolution per each environmental variables. I would like to remember them the importance of use the same resolution for all variables used to predict a model within the same period of time (LGM, LIG, current, future).
Validity of the findings: I think that the results according to the model tested are very exciting for the study of the possible plant response mechanisms involved in the development of conservation of biodiversity under the effects of the current climate change. The results are very clear, although I would like to compare the same scenarios using other methodological algorithms in order to provide a more robust and reliable scientific contribution. It is very interesting to see how there are species which are suffering adaptations, whose distribution will not show drastic shifts in spite of the increasing of the global temperature. Conclusions are well linked to the original aim of this study.
Additional comments: I have read the manuscript carefully, and I found it very interesting. The manuscript is written clearly and uses an interesting and detailed bibliography with new and highly demanded approaches. However, to make this contribution more reliable I think that authors should carry out other methodological algorithms related to species distribution modeling.
I hope my suggestions and comments to the authors will contribute to improve the quality of the manuscript.
In any case I congratulate you for the excellent work!


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

Input:
Title: PREDICTIVE MODELLING OF THE DISTRIBUTION OF CLEMATIS SECT. FRUTICELLA S. STR. UNDER CLIMATE CHANGE REVEALS A RANGE EXPANSION DURING THE LAST GLACIAL MAXIMUM
Review round: 2
Reviewer: 1

Output:
Basic reporting: In this new R1 version of the manuscript titled “Predictive modelling of the distribution of Clematis sect. Fruticella s. str. under climate change reveals a range expansion during the Last Glacial Maximum,” the authors took into account all our previous comments. The manuscript now is much better, is well-written and the aims of the manuscript are well presented.
Experimental design: The authors did a good justification for my previous comments. Additionally, they applied the TSS test to validate their models.
Validity of the findings: The authors justify pretty well why they did the SDM analyses to section Fruticella instead of a single species analysis.
Additional comments: The new version is pretty good and I want to acknowledge to the authors for attending all our previous comments in this new version.


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: IDENTIFICATION AND VALIDATION OF HELLS (HELICASE, LYMPHOID-SPECIFIC) AND ICAM1 (INTERCELLULAR ADHESION MOLECULE 1) AS POTENTIAL DIAGNOSTIC BIOMARKERS OF LUNG CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: Wei Zhu et al. used integrated bioinformatics analysis to identify two genes, HELLS and ICAM1, involved in lung cancer. Lung cancer patients showed increased and decreased mRNA expression for HELLS and ICAM1, respectively. These two genes could be used to predict lung cancer as well as can serve as potential therapeutic targets.

The structure of the article conforms to the PeerJ standards. Clear and professional English was used in the manuscript. The introduction provides an appropriate background. The literature is relevant. The quality of the figures requires improvement. The raw data were supplied.
Experimental design: The manuscript clearly stated how the research fills critical knowledge gaps. The research questions are well defined. The methods were described with sufficient details.
Validity of the findings: Data was interpreted completely and supported the conclusion. The authors successfully established that HELLS and ICAM1 could be two essential genes related to lung cancer.
Additional comments: -	Please provide an English translation version of the informed consent and any other documents in the supplementary data.
-	Texts inside the figure 1B, 3B, 4B, 7A, 7B, 7C, 7D are hard to read. Please use the bigger font size.


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: IDENTIFICATION AND VALIDATION OF HELLS (HELICASE, LYMPHOID-SPECIFIC) AND ICAM1 (INTERCELLULAR ADHESION MOLECULE 1) AS POTENTIAL DIAGNOSTIC BIOMARKERS OF LUNG CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: Zhu et. al. used bioinformatics, systems biology approaches coupled with experimental analyses involving lung cancer samples, cell culture and RT-PCR to initially identify differentially expressed genes and candidate genes in pathways related to lung cancer. Further, Zhu et. al. expand their experimental and computational analysis to show that HELLS and ICAM1 might be the key genes involved with lung cancer progression, and elevated levels of HELLS mRNA and decreased levels of ICAM1 mRNA are predictive of poor prognosis in lung cancer patients.
This study is a nice study integrating experimental and computational methods to identify and validate diagnostic biomarkers for lung cancer. The methodology used in this study can be extrapolated to other types of cancer, to identify and validate potential biomarkers robustly. Therefore, I think this is a nice and important piece of work which will attract readers working in cancer research, and which will be used by other labs working in the field of cancer research.  There are some issues which will have to be addressed by the authors, as I have mentioned in my review, point-by-point. Also, the manuscript has many grammatical errors that need to be taken care of. I have done my best to point out some of them. But, I believe, there might be many more grammatical errors that need to be taken care of. If the authors can satisfy these concerns and the review points, I would be happy to see that this manuscript gets published in PeerJ.
Experimental design: No comment
Validity of the findings: No comments
Additional comments: REVIEW POINTS

Line 50, 51: “However, due to the heterogeneity of the tissue or sample in the existing studies, the results are limited or inconsistent”.
Could the authors elaborate on this statement? Also, it would help the readers if the authors provided one or two examples commenting on the shortcomings of previously published microarray data analysis and how their own method addresses these shortcomings.

Line 55:” We downloaded three original microarray datasets:”
Could the authors provide a rationale for selecting these three datasets over the other available datasets?

Line 140: Were the primers purchased or synthesized in the lab? If they were purchased, please include the name of the vendor. Primer sequences of GAPDH seems like a standard sequence that is being used. For HELLS and ICAM1, are these sequences standard to the available ones in existing literature?
Line 164: The text in the figure 1A and 1B is not readable. Could the authors include high-resolution figure that makes is easier for the reader to understand the text?

Line 169: In Table2, GO id (GO:0008285 ), the description tab does not contain the full information for that particular GO. It seems like an editing issue. Please rectify that.
Line 176: Go should be changed to GO
Line 178: The resolution of the Figure 1B should be changed, it is hard to read the legend. Since, the authors base this result on the network, a high-res figure of the network and the legend would be nice to have.
Line 183: “Using the string online database and Cytoscape software 13, a total of 232 DEGs of 232 common changes in DEGs were filtered into the PPI network complex”
This statement is confusing. Could the authors rephrase this statement?
Line 186: Could the authors explain what is meant by a “cell angle”
Line 186: “Using the Metascope to analyze the functions of the genes involved in this module is mainly focused on cell division, pre-mitotic stage and mitosis cell cycle transition”
Could the authors please rephrase this statement.
Line 192: Was the analysis of biological processes of hub genes carried out by the cBioPortal online platform in Fig. 4C?
Line 221: However,  levels of ICAM1 mRNA in human lung cancer cell lines, only HCC827, was a low expression, compared with normal lung epithelial cell line, BEAS2B(Fig.8).
Rephrase this statement, it seems confusing to understand
Line 228: “However, most previous studies have focused on the results of a single genetic event or a single cohort study,  and the results from these studies have been inconsistent and incomplete, the incidence and mortality of lung cancer worldwide remain high”
Please provide few references
Line 246: Please rephrase “This protein …..”
Line 257: Change “and we also revealed” to “and also revealed”
Line 260: Introduce the expanded name of the abbreviation, ICAM1, where it first appears in the manuscript.
Line 281: “Coupled with a series of previous studies, we revealed that decreased ICAM1 mRNA levels predict poor prognosis in patients with lung cancer. Therefore, ICAM1 may be a novel potential therapy target for patients with lung cancer”.
If decreased ICAM1 mRNA levels predict poor prognosis in patients with lung cancer, how can it be a novel target?
Line 292: Rephrase the statement.

Figures: Figure 1A, 1B, 3B, 5G, 6G 8A, 8B: Please provide high-res figures
 Also for figures 5G, 6G, please include what the Asterix means and provide relevant statistical information


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: RELATIONSHIP BETWEEN HEALTHCARE SEEKING AND PAIN EXPANSION IN PATIENTS WITH NONSPECIFIC CHRONIC LOW BACK PAIN
Review round: 1
Reviewer: 1

Output:
Basic reporting: I think the manuscript should be edited by a native English speaker. Examples of strange sentences or errors:
-	However, another study have not found the same results
-	Affectation?
-	Flyers were placed at the university centre and also at the local community, and those patients with CLBP who were not seeking treatment, were recruited. On the other hand, those patients who have gone to a health professional due to the presence of low back pain were classified in the care seekers group. It is therefore, these patients had an intention to be treated.
-	This process might a reason why in our patients seeking help had a greater expansion of…

Use consistent language: extension vs expansion.

Use consistent reference style: only surname, when all names, when et al?
Experimental design: Introduction:
-	I would recommend to at least mention somewhere the newer introduced term of nociplastic pain, and how it relates to CS.
-	I think the research question is not sufficiently introduced and teh relevance is not argued in the introduction.

Methods:
It would be better to restructure the methods. Cluster all information, regarding sample (now e.g. spread over the beginning, middle part and end of methods), the information regarding procedure, and then all information regarding the outcome measures.…
Add clinimetrics or references for all outcome measures.
Strange that the introduction is about central sensitization, and not/less about physical functioning etc., while in the methods outcomes are mainly on physical performance and cognitions? So again, I think the introduction does not fit with the rest of the article.
Cohen’s d effect sizes were calculated for multiple comparisons of the outcome variables. What do you mean with the “for multiple comparisons”?

Results:
Results can be shortened as everything is shown in tables.

Discussion:
I think, overall, the authors did a good job in discussing their study, although the discussion is lengthy. Readability would increase when the discussion would be shortened and restructured on some points. Cluster your paragraphs around similar constructs.
Regarding the limitations: I think more limitations need to be addressed (see earlier comments). I think the argument of the opioid system is not the most appropriate for discussing the differences in PA levels. Think the role of PA in pain deserves a better and more extensive explanation. Furthermore, I would rather consider the difference in PA also as a very interesting outcome, rather than discussing it in the light of comparability of groups? I have more problems with the age-thing! This could be more coincidence, or caused by selection bias, and might be independent from the complaints. So I think that is more confounding the study, while PA is in my opinion an interesting outcome?
For your conclusion and the rest of your article (e.g. statistics) always stick to the same consistent order of your objectives. So start with the expansion of pain, etc.
Validity of the findings: Methods:
The care seeker group: where they recruited via therapists/doctors?
More specific in- and exclusion criteria are lacking: age, comorbidities, time between seeking care and recruitment, …
Outcome measures:
-	Frequency of medication: so someone taking 10 days 1 paracetamol = person taking 3 tramadols for 10 days?
-	Why no hyperalgesia, allodynia, or some kinds of QST?
-	Explain the difference between PPSA and WP?
Statistics:
-	The Student T-test was used for the non-specific CLBP group comparisons. Why not everything with Anova?

Results:
-	There were differences in age between groups, were they recruited from the same population? Could you account for this difference?
-	Table 2: can you indicate the significant ones? Or add p-values?
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: RELATIONSHIP BETWEEN HEALTHCARE SEEKING AND PAIN EXPANSION IN PATIENTS WITH NONSPECIFIC CHRONIC LOW BACK PAIN
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the abstract and background there's a lot of speculation regarding causes of chronic low back pain and even a suggestion that CLBP can cause central sensitization, which is a theory worth exploring although completely irrelevant to the topic of this study.
What is lacking, however, is a background that provides the reader with an understanding of why this study has relevance (i.e. previous studies or underlying reasoning that have let the authors to believe that people who seek care are different from those who don't). It remains a mystery to the reader why the authors have included all the secondary analysis if the one true finding is that there is a significantly increased spreading of the pain (pain drawing) in one group compared to the two others. The reader should be presented with this information in a clear structure from background through to conclusion. To this end, a complete re-write of the manuscript appears the most obvious solution.
There are some issues with the language, which seem to confuse the authors; they seem most reliant on american spelling (e.g. line 51, 78 and 330) but use UK spelling for the esthesiometer. I suggest using only one. A general review of the written language is recommended.

In the results section the main results are hidden and only referred to as Figure 1 and Figure 2. Please provide the main results in the first or second paragraph.
Experimental design: A convenience sample is used, yet the basis for sample size selection is unclear; please provide precise data on effect measures and units used to calculate the sample size.

The research question is not clear (no hypothesis or relevant background is provided).

Please elaborate on the assumption that data was normally distributed; did you test it?

The manuscript should clearly show which results can be considered relevant to the power / sample size of the study to avoid any suspicion of type-2 errors. Group differences are analyzed with one-way ANOVA, but if the authors suggest that there is differences in the secondary variables, which could explain the group differences, why did they not use 2-way-ANOVA to assess their relationship?

Please justify that your measurements are trait, not state, dependent or in other ways justify that a single measure (at one time point) can support your conclusions (a non-seeker could seek care the day after the study; how would this influence the results)?
Validity of the findings: Results based on the sample-size calculation are not clearly separated from those of more speculative origin. This undermines the validity of the results and must be corrected. In the current format it is not possible to neither accept nor reject the findings since the outcome used to calculate power is unknown.

There are significant differences between the age of those who seek care compared to those who don't and controls. This is a major limitation and must be thoroughly discussed, if the authors believe that age cannot account for the results. Furthermore, authors should explain why 'age' is not analyzed in a one-way ANOVA since this is the way all other data is analyzed.

Finally, the conclusion should report on the primary measures only (spreading of pain).
Additional comments: It seems like a relevant finding that pain is reported to be more wide-spread among patients who seek care compared to people living with pain (and asymptomatic people). This should be the main focus of the article (the rest seems to be speculative or in need of justification methodologically). It would be interesting to know why you thought of this hypothesis in the first place (and indeed what you expected to find and why). The methods and results could be trimmed tremendously if they only account for the (exptected) hypothesis.
In the discussion there are several limitations and considerations, including clinicial relevance and least-clinically relevant difference, that needs to be addressed.


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: RELATIONSHIP BETWEEN HEALTHCARE SEEKING AND PAIN EXPANSION IN PATIENTS WITH NONSPECIFIC CHRONIC LOW BACK PAIN
Review round: 2
Reviewer: 1

Output:
Basic reporting: Introduction:
I am still concerned about the introduction. The language is not always clear, and consequently I don’t get the message soon enough. It is only at the end of the introduction that it becomes clear to me where the study is going to.
Do we need all the information about proprioception, about sensitization etc.? Because of the overload of information on more irrelevant points, the flow of the introduction is not clear.

Results:
OK, improved!

Discussion:
Still some strange and long sentences, that are not always easy to read/interpret.

Suggestion to change "seek care" to care-seeking whens used as descriptor or noun.
Experimental design: OK, rebuttal and changes OK.
Validity of the findings: OK
Additional comments: No additional comments