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 AND DIEL VARIATIONS IN THE VERTICAL DISTRIBUTION, COMPOSITION, ABUNDANCE AND BIOMASS OF ZOOPLANKTON IN A DEEP CHILEAN PATAGONIAN FJORD
Review round: 1
Reviewer: 1

Output:
Basic reporting: The submitted manuscript reports the vertical distribution of (meso)zooplankton at a fixed station in a deep fjord of northern Patagonia (Chile). Zooplankton was sampled at four different dates covering all four seasons and samples were analysed with imaging approaches (ZooScan). Environmental data were also collected to help interpret the zooplankton distribution. The limited sampling (four dates in one year), does not allow to infer a true seasonal cycle (which would have required replication of the season sampling), but the information brought by the collected data is interesting allowing to focus on potential diel vertical migration, which is at the core of the study.

The rationale of the study is presented in the much broader context of the sustainability of cold water corals (CWC) which face calcification problems due to aragonite-undersaturated local waters. Their growth and survival depend on the availability of food resources that mainly consist in zooplankton, hence the question of its composition and distribution. If I acknowledge this broad context, I however consider that the study did not investigate the relationship between the diversity and distribution of the zooplankton and the sustainability of CWC populations, which is presented as the second objective of the study. The CWC are not studied in the paper, and only speculative hypotheses are inferred in the discussion section (no materials and methods, no results on CWC). Further comments on this point will be given in the following sections.

Overall the manuscript is written in an English that a non-native speaker can understand. Some ambiguous terms are reported in the detailed comments.

Some sections are a bit long and might be shortened. In the results section for example, line252-265, the paragraph is too detailed, and information is found in Fig. 4. I suggest to keep only key results. Overall the discussion is long and should be shortened. Many details are given, sometimes redundant with the results, with no real discussion. Shortening could be achieved by refocusing some paragraphs (e.g. 2nd paragraph should focus on vertical distribution and DVM, nothing else), and by removing parts which seem out of topic. As an example of this last point, part of the mysid paragraph (in second subsection of the discussion) (lines 458-464) could probably be removed, as this do not relate to vertical migration. So please try to keep only essential discussion. Similarly, the “zooplankton gap” part (lines 478-500) is very interesting but is too detailed given the results available, and should be shortened.

The Figures and Tables provided are all helpful and are overall well presented. Some detailed comments are provided in the following sections.

Raw data were accessible through the Pangaea repository. Data available consist of images of each ZooScan scan. Other data, like a table of counts of each plankton category, i.e. after image processing, or the accompanying CTD data, are not available. I don’t know whether this is mandatory.
Experimental design: The sampling design allowed to answer the question of the vertical distribution of various groups of zooplankton in the deep fjord, and to search for the existence of diel vertical migration patterns. One question was however why no flowmeter was used to measure more accurately the volume filtered. Is it not possible when sampling multiple strata?

As mentioned in the basic reporting, the study did not investigate directly the relationship between the zooplankton and the coral populations.

Some details in the description of the image processing were lacking or some points were not clear. These are higlighted in the attached manuscript. Among them are:
1. “ZooScan detection limit was set at the standard of 300 µm” (line 161-162): what does this mean?
2. You mentioned several times (lines 163, 179), the success of automatic processing or classification. What does this mean, and how is it determined?
3. Was the training set you used a combination of the global one and the Patagonian one, or only the Patagonian one?

Statistics. No statistical analyses were provided in this paper. In particular, in the analysis of the vertical distribution of zooplankton (with abundance), it is not clear if the seasonal or diel differences were significant or not. One example is the case of Calanus / Calanidae (lines 306-308, fig. 6C), in which day-night difference is not so clear; this is found in many other examples… Although I can agree that day-night differences are visible in Fig. 4 for biovolume and biomass, it is not so evident for abundance, so that statistical tests might be of help. The lack of statistics could arise from the lack of replication (which is not a problem per se for me because of the sampling constraints…), so the test of Beet et al. (2003) could not be applied, but maybe the method proposed by Solow et al. (2000) could be a solution. I am not sure if such an approach could also be used for biovolume and biomass, but certainly it could be used for abundance. Could you explain why you didn’t/couldn’t use any statistical test?
Beet, A., Solow, A. R. & Bollens, S. M. (2003) Comparing vertical plankton profiles with replication. Mar. Ecol. Prog. Ser. 262:285-287.
Solow, A. R., Bollens, S. M. & Beet, A. (2000) Comparing two vertical plankton distributions. Limnol. Oceanogr. 45(2):506-509.
Validity of the findings: 1. As already mentioned, the last paragraph of the discussion, "Ecological connection with cold-water corals” is very speculative and should be greatly shortened, if not removed. You did not study the relationship between CWC and mesozooplankton. Yes there is plankton that could serve as a food source for CWC. Yes zooplankton is more abundant in spring which is also the period of higher growth rate for CWC. But your data you don’t allow to show the relationship between both. Further you cannot show that DVM is important for CWC feeding: for this you would have needed feeding studies comparing shallow and deep corals, and day and night food consumption. Finally, I did not understand the calculations of prey consumption that allowed you to provide a threshold for prey availability that would be necessary to sustain a coral population. Again this sounds highly speculative. Similarly, the second part of the conclusion section is out of the core topic: the manuscript did not show that “The high amount of zooplankton in Comau Fjord provides sufficient nourishment to maintain a viable coral population despite the aragonite under-saturated waters”. This remains a hypothesis.

2. As mentioned in the previous section, if statistical analysis could be done, this would give more strength to the conclusion about DVM.

3. Line 300 and following lines: in this part of the paragraph you describe the vertical distribution of different size groups within one taxon (e.g. “largest Metridia”, “small specimens of Calanus”), but such results are not illustrated in any figure or table. This is however a very interesting result of your study. In the discussion you conclude (lines 437-438) that “It is possible that the size differences between day and night might be a consequence of the presence of different species or life stages”. This deserves more discussion, based on size data. Why not show size data? I am not talking here of the total biovolume of a taxon, but the vertical distribution of different size classes within this taxon, so that you can show their potential different distribution.

4. Taxonomy-1. I am not comfortable with the term “taxonomic” throughout your manuscript because the defined groups mix true taxonomic groups (e.g. Copepoda, Cirripedia) and developmental stage groups which can mix several taxonomic groups (e.g. crustacean nauplii which can include copepod nauplii, as you mentioned line 272, and cirriped nauplii; what then is included in the group Cirripedia? Cyprids?). I have no ideal solution, but you can either avoid the terms “taxonomic” or precise somewhere that what you call taxonomic is not really taxonomic… Please note that this may have consequences in the interpretation of the results in the discussion. For example when you state that “At this time, crustacean nauplii and young stages of calanoid copepods, which are indicative of intense zooplankton reproduction” (lines 355-356), this is only partly true, as crustacean nauplii can also indicate reproduction of benthic cirripeds as you (too) briefly recognize line 368 when mentioning meroplankton. Such a point would merit more discussion, as abundances of barnacle larvae may reach values similar to yours: for example, Meerhoff et al. 2014 reported abundances of barnacle larvae of up to 80 larv m-3 in october, of course in a different fjord.
Meerhoff E, Tapia FJ, Castro LR (2014) Spatial structure of the meroplankton community along a Patagonian fjord - The role of changing freshwater inputs. Prog Oceanogr 129:125-135.

5. Taxonomy-2. It is sometimes difficult to follow your statements on the taxonomic composition as taxonomic levels are different depending on the groups and depending on your statements. For Copepoda, sometimes you use the order (e.g. Cyclopida), sometimes the family (e.g. Euchaetidae). More importantly there are some differences between the text and the figures: for example when lines 290-294 you mentioned Metridia (also in Table 2), citing figures 5 and 6, the corresponding figures did not consider Metridia but Metridinidae. The same applies to lines 300-306. This could mean that Metridia is the only genus observed in this family or the most abundant one, but this brings confusion. Could you please make some efforts to keep things more homogeneous? The same comment can be made for Calanus, lines 306-312, while fig. 6C illustrates the family Calanidae. Please also update in the discussion accordingly (lines 422-436).
Additional comments: 1. Table 2: you cannot sum day and night abundances, because it artificially increases the abundance: the organisms present at nighttime are not added to those of the daytime, they replace them. So I suggest using a mean instead.

2. I suggest you avoid beginning your discussion by sentences like “The present study provides the first detailed data on the zooplankton community composition, distribution and dynamics in the northern Chilean Patagonia. There are only few zooplankton records with a high taxonomic resolution in Patagonian Chilean waters.” The interest of your study does not rely only on the fact that this is the first in your area… I also find not very convincing the argument on high taxonomic resolution as your own study does not provide high taxonomic resolution: at best you identified genera but all your figures and tables address much higher levels…

3. Lines 357-358: “During summer, biovolume and biomass reached their maxima (Fig. 3), indicating the growth of the zooplankton organisms.” I think that you cannot reliably draw this conclusion. First this has to be put in relation with the lower abundance in summer, and not only by itself (lower abundance + higher biomass, then larger individuals). Second, increase in biovolume/biomass not necessarily reflect growth, but may reflect different groups, with larger species, so this is not growth. If this is this idea that you had in mind, then I think that the word growth is inadequate.

4. There is a mix between the 2 first paragraphs of the discussion section, which could bring some confusion. For example lines 440-445 would be better in the first paragraph “mesozooplankton seasonal dynamics” than in the second one although it is of course “population dynamics”. The second paragraph should be focused on vertical distribution/migration. Lines 440-445 have nothing to do with vertical distribution. Same for lines 472-477…

5. Lines 501-510: this paragraph is very important, as looking at results described lines 247-251 immediately raises the question of the factors responsible of this. However, biological factors are probably not the only ones to explain this observation, and other factors like tides or others (those you mentioned lines 386-388) may be involved to transport plankton to the sampling site (in relation to the patchiness discussed in this paragraph). You may say something here.

6. Line 492/Fig. 7: You give a range of 68-82% for carnivores. But even in summer and autumn, it can be less (summer night). For the other months, it is much less, so you cannot simply give the range that you prefer (disproportionately large… in 2 months out 4!). I suggest changing the sentence to “In our study, biovolume of carnivorous organisms ranged between X and Y % of the total zooplankton in this water layer, reaching particularly high values in summer and autumn (Z-82%) (Fig. 7)”. Further, in this figure, it is not possible to contrast copepods and carnivorous zooplankton, because the category carnivorous includes the Euchaetidae, which are copepods (are there other carnivorous copepods?). So I suggest changing the name of the category copepods (e.g. non carnivorous copepods, stating somewhere that Euchaetidae are carnivorous).

7. Detailed comments
Fig. 4: Please add “Abundance (ind m-3)” on the X axis, not as a title (same for biovolume and biomass)
Fig. 6: For all taxa, do the counts include all developmental stages?
Other detailed comments are given in the attached manuscript.


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

Input:
Title: SEASONAL AND DIEL VARIATIONS IN THE VERTICAL DISTRIBUTION, COMPOSITION, ABUNDANCE AND BIOMASS OF ZOOPLANKTON IN A DEEP CHILEAN PATAGONIAN FJORD
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript deals with the spatio-temporal variability of the zooplankton in a fjord of northern west Patagonia. Using vertical hauls at different depths, with day and night collections during different seasons, and with novel methodologies for the identification and measurement of zooplankters, authors describe the vertical distributions (not the DVM, which is not statistically tested) of several taxa, as well as the CTD casts. Based on this large amount of data, the authors made a very nice description of the data, but it lacks statistical comparisons to validate the observed patterns. Also, no working hypothesis was tested by the authors. The incorporation of several methodologies in the data analysis will improve the manuscript quality. Some suggestions are included in the following sections.
Finally, the relationship between CWC and zooplankton biomass is not tested in the manuscript, and therefore, this should not be included in the Conclusions.
Experimental design: The experimental design of the study is correct, with three factors (depth, day/night, season), but without replicates (no additional hauls for each stratum).
The lack of replicates does not allow the use of two-way ANOVA for testing DVM, but a 2x4 table of contingency (day/night vs season) of the centroid depth may be an alternative for testing DVM.
Validity of the findings: This is the weakest section of the manuscript. The description of the results is sound, but the findings were not statistically tested. I suggest several methods throughout the Results
Additional comments: Introduction
line 119 and its relationship with zoo- and ichthyoplankton growth and feeding (Landaeta et al. 2015a, b)

Landaeta MF, Contreras JE, Bustos CA, Pérez-Matus A (2015a) Growth and condition of larval rockfish in a Patagonian fjord-type inlet: role of hydrographic conditions and food availability. Aquatic Ecology 49: 573-584. doi: 10.1007/s10452-015-9547-y

Landaeta MF, Bustos CA, Contreras JE, Salas-Berríos F, Palacios-Fuentes P, Alvarado-Niño M, Letelier J, Balbontín F (2015b) Larval fish ecology, growth and mortality from two basins with contrasting environmental conditions of an inner sea of northern Patagonia, Chile. Marine Environmental Research 106: 19-29. doi: 10.1016/j.marenvres.2015.03.003

line 227 How do you compare the abundances, estimated biomasses/volume and composition among seasons and depths?
Any correlation/covariance between the biological matrix and the environmental conditions measured by the CTD?

line 230 Any statistical comparison of the surface waters among seasons?

line 235 "mean average". Mean, median and mode are all averages, so "mean" by itself is enough
line 253 Any statiscal comparison?
line 254 Because of the lack of replicates during the diel cycle, authors cannot compare the abundances in the vertical scale using the classical approach (two-way ANOVA with day/night and depth as factors, being the interaction [day/night * depth] the evidence of vertical migration. Otherwise, you can estimate the centroid depths during day/night and seasons, and compare these values in a contingency table.
line 268 Additionally, you can compare the composition and abundance/biomass of zooplankton using two-way PERMANOVA or ANOSIM, and detect those taxa that support dissimilarity using SIMPER
line 273 Also, the multivariate approach to show the depth and seasonal variability of zooplankton composition is a nice option: PCA, PCoA and nMDS are the most common approaches.
line 328 I suggest comparing the biological matrix with environmental conditions measured by the CTD, in order to detect physico-chemical-biological interactions. You can use an univariate approach (multiple regression of environmental conditios against diversity indices), multivariate (PCoA, CCA, PLS) or modelling (GLM, GAM, GLMM)
line 331 Please, indicate the limits of this research (i.e., vertical hauls may reduce the presence of very motile zooplankters, such as adult euphausiids, Munida megalopae, large fish larvae- which are also important in terms of density and biomass across west Patagonia)
line 370 "Balbontín" instead of "Balbotin"
line 388 In terms of tidal mixing, in which lunar condition was carried out the sampling? because there is a noticeable influence of the tidal regime (neap tides vs spring tides) in northern Patagonia, this issue may impact the results and its interpretation
line 416 This "pattern" should be statistically tested
line 485 "this study" I cannot find the correlation test in the manuscript
Finally, the relationship between CWC and zooplankton biomass is not tested in the manuscript, and therefore, this should not be included in the Conclusions


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 AND DIEL VARIATIONS IN THE VERTICAL DISTRIBUTION, COMPOSITION, ABUNDANCE AND BIOMASS OF ZOOPLANKTON IN A DEEP CHILEAN PATAGONIAN FJORD
Review round: 2
Reviewer: 1

Output:
Basic reporting: I here acknowledge the thorough revision of the manuscript. All questions/comments I made (as well as those made by the other reviewer) were addressed, most of them satisfactorily (please see in the following further comments). For this I would like to thank the authors.

In particular, they have made required additional analyses to give statistical reliability of their data. I particularly appreciated the RDA analysis, which I think has been well interpreted. Without being completely sure, I think the test of the difference of centroid depth between day and night is appropriate, but still have doubt on how the SIMPER procedure could be interpreted: above which contribution threshold can you consider that the centroid depth differs for a given taxon (then to show significant difference in vertical distribution for this taxon)?

I also aknowledge the huge efforts made to reduce the length of the discussion (almost half has been removed), which allowed to better focus on the core topic of the paper (seasonal variations in zooplankton composition and abundance, and vertical distribution-DVM).

The part dealing with CWC has also been reduced. I would have expected even more reduction, but in the current form this is fine for me

Dealing with data availability, the authors provided additional tables, as was suggested
Discussion - section DVM. I think that before discussing details about DVM, you should first explain that you observe DVM, based on your results. For example based on the RDA, that clearly shows that differences in the zooplankton composition are higher in the surface waters between day and night, which could be due to DVM. Please also use your results from Fig. 7 and if needed the centroid depth and contribution (but see comments above and below). E.g. lines 467-470, it is not clear on what results your statement is based: from your SIMPER analysis, in autumn, calanoid < 1.5 mm contribute to the difference, and the same for copepod nauplii in summer and autumn (fig. 4). Did I misunderstand fig. 4? So it is not only a question of size. I suggest here that you don’t use the general phrase “while small organisms (individuals <1.5 mm)” which implicitly comprises the calanoid < 1.5 mm. Instead, use directly the names cyclopoid and hapacticoid, to state that some copepods do not migrate. Then you can talk about their size…

This might be unfair but I have identified an issue that I did not notice in my first review: in Fig. 7B-I, isn’t it a problem to use % of total zooplankton? If the species of interest does not migrate but that other species migrate downwards, then mathematically its % abundance (or biovolume) will increase at the surface, and decrease at depth. Why not use abundance, or percent of abundance of the species at a given depth in relation to its total abundance (all depths)?
Experimental design: All issues were correctly addressed, in particular for the statistical part (see basic reporting)

Centroid depth: if I understood well you calculated it based on abundance. But from the results you assessed the dissimilarity with abundance and biovolume. Is it possible? In this case why not on biomass? These choices are not clear to me.
Validity of the findings: L. 482-485: “In Comau Fjord, Metridinidae showed the highest values of biovolume and abundance at intermediate depths (100-200 m) during daytime, but in the surface layer (0-50 m) at night (Fig. 7B), which suggested the migration of the largest individuals towards the surface (Fig 8)”. I agree with the first part of the sentence (migration upwards during nighttime) but not sure for the second part: looking at Fig. 8A, summer and autumn for example, all sizes, not only largest, migrate upwards. Am I wrong? (see also additional comments).
Additional comments: L. 282-285 deal with vertical distribution (centroid depth), then should be in the following paragraph…Right?

L. 334-336: not clear. What do you mean by “the largest individuals” with the mean of 0.62… In summer you have individuals larger than this… Further I am not convinced that the size structure is really different between day and night. They seem to be very similar. The main difference in summer is that at night Metridinae can be found in shallower waters, but the “migrating” individuals (i.e. those at 0-50 m) seem to have the same size as those from 100-200 m (not the largest). Do you mean that individuals at intermediate depths are larger in average, i.e. only small specimens are at the surface, and small AND larger are at intermediate depth (and not the largest…)? I am not sure this is what you stated here. So did I misunderstand fig. 8? From this figure I can’t see a major difference in size structure between day and night, for both groups.

L. 344-345: “Euchaetidae showed higher abundance and biovolume in the deeper part of the water column during day time, ascending to shallower waters at night (Fig. 7I)” I can agree looking at the figure, but it is not so obvious… In particular, it seems not true in winter. But, Ok…

L. 542-543: here it is not question of abundance integrated over the water column, it is vertical distribution, as it deals with centroid depth. So please avoid using the term integrated. Moreover, I think that the whole paragraph (542-558) should be place at the beginning of the DVM section, to state that there is vertical migration (change in centroid depth between day and night). This cannot be put after the part on CWC.

Fig. 5: the legends of X-axes (abundance, biovolume, biomass) should be put above the graphs, not below

Table 1. Bivalvia: please add larvae. Same for Gastropoda

RDA: I couldn’t find the legend of fig. S1 but I guess the arrows were the 13 taxonomic group which were the most abundant? Its quality (resolution) should be improved as the different symbols are not easy to distinguish. Instead of “The physicochemical variables have higher influence on abundance and biovolume between daytime and nighttime and within the most productive seasons (spring and summer) in shallow waters (0-50 m)” (L; 362-364), I suggest “For both abundance and biovolume the main differences were observed between day and night samples in shallow waters (0-50 m), during spring and summer”.


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 AND DIEL VARIATIONS IN THE VERTICAL DISTRIBUTION, COMPOSITION, ABUNDANCE AND BIOMASS OF ZOOPLANKTON IN A DEEP CHILEAN PATAGONIAN FJORD
Review round: 2
Reviewer: 2

Output:
Basic reporting: The new version of the manuscript has considered all the comments and suggestions made by me in the previous review, and I acknowledge that. This situation has improved all the aspects of the manuscript.
Experimental design: no extra comments
Validity of the findings: Now, with the inclusion of the RDA and centroid depth distribution, the validity of the results has been highlighted
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: IDENTIFICATION AND VALIDATION OF A NOVEL SIGNATURE FOR PREDICTION THE PROGNOSIS AND IMMUNOTHERAPY BENEFIT IN BLADDER CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.	There are numerous grammatical errors and typos that affect readability.
2.	Some of the references are outdated and shall be replaced with more up-to-date literature.
Experimental design: 1.	The authors used five GEO datasets for the screening of differentially expressed genes between normal and tumor tissues. How are these datasets selected? What are the selection/exclusion criteria for datasets?
2.	Have the authors compared the prediction performance with other methods? Does this 8-gene signature outperform other gene signatures in predicting prognosis and responsiveness to immunotherapy? Does it outperform models using only clinical variables, which will be much less expensive and laborious to conduct? (An example would be the six-factor prognostic model for patients with advanced urothelial carcinoma receiving post platinum atezolizumab by Pond et al., 2018)
3.	RT-PCR analysis of mRNA expression of the genes in established cancer cell lines does not necessarily provide validation of the gene signature nor of the prediction model. First, the changed gene expression in the GEO or TCGA datasets might represent the upregulation or downregulation of genes in the tumor microenvironment (e.g., immune cells, tumor-associated fibroblasts, etc.), but not that in the tumor cells. Second, cancer cell lines can behave very differently from patient tumor samples because of culture conditions. Also, the authors used a cell line called “EJ”. This is confusing because there are several cell lines named EJ, including a human diffuse large B-cell lymphoma cell line.
Validity of the findings: It is important to develop prognostic models that can identify patients who might benefit most from new immunotherapies, Once confirmed, these tools could provide a critical decision-making tool for clinicians. However, previous literature has described numerous immune-responding signatures in bladder cancer. For example, Lv et al1. have reported a risk model based on eight immune-related genes that predict the prognosis of BLCA patients, which can also “predict response to immunotherapy, reflect different BLCA subtypes, immune and mutation status”. Comparably, Fu et al2. have built a 30 gene risk signature to predict the effect of immunotherapy in BC patients. Moreover, in an almost identical approach, Wang et al. have developed a 13-gene signature that can “classify the immunotherapeutic susceptibility of patients with BC”. The Result and Conclusion sections of the current manuscript are nearly identical to that of Wang et al., Cancer Med, 2020.

The authors need to compare their findings to previous work and explain explicitly how their “discovery” is different from previous reports and highlight their novelty.
Additional comments: NA


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 A NOVEL SIGNATURE FOR PREDICTION THE PROGNOSIS AND IMMUNOTHERAPY BENEFIT IN BLADDER CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In the present research, the authors identify the gene signature as a predictive indicator of immunotherapy treatment for BC.
I have several reservations. My comments are appended as below:

Major comments:
1.	Abstract- In the background section, please specify the dearth of studies in the present literature and how your research fills the gap. In methods, please specify the cell lines used. Results- please specify the 8 gene-based signatures.
2.	Introduction- Authors should first discuss the general facts on prognosis and pathological types of BC, especially with reference 2.
3.	Introduction- please include median survival on checkpoint therapy in BC.
4.	Introduction- authors should revisit a few reviews while discussing the cofounders for immunotherapy efficacy. For instance- PMID: 33076303, PMID: 31102620
5.	 Authors should describe the GEO dataset characteristics (may include a table with relevant information). Was it includes immunotherapy responders and non-responders? How do authors stratify the samples?
6.	In the flowchart, please show inclusion and exclusion criteria.
7.	Figure 2- please annotate the volcano plot with the corresponding GEO dataset. In addition, authors should provide the complete list of genes in supplemental tables.
8.	I have a question on the figure 2F- the commonly predicted genes as PD-L1, Inf gamma signaling was not visible in the list. Authors should justify.
9.	Line 216- please elaborate the regression analysis. Which datasets were used?
10.	Figure 3 A, B- is it PFS or OS?
11.	Validation of nomogram- authors should use responder/nonresponse cohort. It is not clear the characteristics of the samples used.
12.	It is not clear to me the rationale to use the cell lines. Are they tested to be sensitive/resistant for selected treatment?
Minor comments:
1.	Please provide catalog number of all used reagents.
2.	Line 179- qRT PCR- please specify how RNA purity was detected and what quantity of RNA was used.
3.	Survival curved- please specify PFS/OS


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 A NOVEL SIGNATURE FOR PREDICTION THE PROGNOSIS AND IMMUNOTHERAPY BENEFIT IN BLADDER CANCER
Review round: 1
Reviewer: 3

Output:
Basic reporting: The language used is very clear , and well supported with the correct references.

Just a few minor corrections are suggested:
1. In the introduction, on line 75, correct the spelling "gens" to genes.
2. In the discussion, on line 311, change the word "Previously" to Previous.
Experimental design: This study identified a novel signature ,that would be applied as a prognosticator and a promising biomarker in individualized immunotherapy for BC. The experimental design and the methods employed, sufficiently address the main objective of this study.
Validity of the findings: All the data provided, is well supported with correct rationale and is statistically sound.

One minor suggestion - Please elaborate further on the role of the 8 individual genes, in promoting Bladder cancer specifically.
Additional comments: A well written manuscript, with excellent  findings , which can help design better individualized treatments for bladder cancer.


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 A NOVEL SIGNATURE FOR PREDICTION THE PROGNOSIS AND IMMUNOTHERAPY BENEFIT IN BLADDER CANCER
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors’ response letter and the revised manuscript have addressed most of my concerns. In particular, the authors have compared their gene signature with existing literature and showed that the novel 8-gene signature is comparable or superior to previously described gene signatures. The authors also moved their not-so-relevant RT-PCR results to the supplementary data. I have one remaining minor concern about figure 4. The figure, especially Fig 4C, is hard to read because of poor resolution and small font size. After this is addressed, I would recommend the manuscript for publication.


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

Input:
Title: IDENTIFICATION AND VALIDATION OF A NOVEL SIGNATURE FOR PREDICTION THE PROGNOSIS AND IMMUNOTHERAPY BENEFIT IN BLADDER CANCER
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I congratulate the authors for providing the modifications. All my concerns are successfully addressed. I recommend accepting this manuscript.


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

Input:
Title: IDENTIFICATION AND VALIDATION OF A NOVEL SIGNATURE FOR PREDICTION THE PROGNOSIS AND IMMUNOTHERAPY BENEFIT IN BLADDER CANCER
Review round: 2
Reviewer: 3

Output:
Basic reporting: The corrections have been made , as per suggestions. No further changes needed.
Experimental design: No further changes needed.
Validity of the findings: The justification provided for the queries in the discussion, have been responded to , appropriately.
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: PERCEIVED PHYSICAL ACTIVITY DURING STAY-AT-HOME COVID-19 PANDEMIC LOCKDOWN MARCH–APRIL 2020 IN POLISH ADULTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: INTRODUCTION
Please, lengthen and deepen the introduction. some studies that could help you are:
1.	https://pubmed.ncbi.nlm.nih.gov/21291246/ to comment the difference between outdoor activity and indoor (lockdown) activity
2.	https://pubmed.ncbi.nlm.nih.gov/31077254/ physical activity and motivation
3.	https://pubmed.ncbi.nlm.nih.gov/34302530/ Child factors associated with mental health and well-being during COVID-19
4.	https://pubmed.ncbi.nlm.nih.gov/33588981/ Impact of COVID-19 Lockdown on physical activity and lockdown
5.	https://pubmed.ncbi.nlm.nih.gov/33311526/

Line 56-57, 60. Is this writing reference correct, or is it more accurate to insert only a year? E.g. Jafari et al. (2021) show that etc.
Please check the editorial rule

Line 63-64. Please insert which study

Line 65. Walking between brackets, it is not an abbreviation

Line 71-76. Please, think to rewrite the goal of the study in a more explicit manner, avoiding inserting part of material and methods (e.g. IPAQ)

MATERIAL AND METHODS
Line 81-82. Please explain and insert references

Line 84-85. Please could you explain? When it was writing the paper, before or after that, you have collected data? This concept was not clear

Line 114-116. I think that it could be more ordinated if you insert a section to describe and explain the IPAQ questionnaire

DATA ANALYSES
Please, consider writing this section (Data analyses) again in a more precise manner

DISCUSSION
Discussion is a reply to results. Please discuss more deeply the results using literature
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: PERCEIVED PHYSICAL ACTIVITY DURING STAY-AT-HOME COVID-19 PANDEMIC LOCKDOWN MARCH–APRIL 2020 IN POLISH ADULTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The introduction section needs the insert of a more supportive rationale and required a better explanation of many arguments. I suggest including more information about the health negative effects of augmented sedentary behavior and the positive benefits of an active lifestyle. I suggest adding an explanation about the different exercise intensities, how is important to measure vigorous and moderate PA, and the walking and sitting time. Then, I suggest paying attention to the lockdown period and the effects it has on the population, especially young adults, and adults. Several studies investigated these peculiar aspects.
The hypothesis of the study is not well clear, and the aim of the study is not supported by a logical and clear background. This section needs a complete rewrite.
Line 73-76: I suggest moving this information from the introduction section to the method section.

All the figures needed a clear legend of the acronyms at the bottom. Moreover, they need the insert of significance values or not. The captions are shown. Tables need partial corrections. I suggest deleting the “missing data”, “minimum” and “maximum” from the table and linking mean+SD.
Experimental design: The scope of this paper fit with the aims and scope of the journal.
Method section required some corrections.
I suggest moving the lockdown restrictions in a supplementary file to lighten the reading and maintain only the most important restriction related to the PA level. I suggest removing the link of the survey from lines 131 to 135 and maintaining only the shorter link. I suggest checking the unit of measure through the paragraphs. I think it would better explain why the minutes of these activities were truncated to 180 minutes if the activity was higher than 180 minutes (line 170). The inclusion and exclusion criteria are not well reported. I suggest adding them.
The sample is not representative of the entire Poland population, so the results cannot be generalized. I suggest refining the sample such as active people or a specific area of Poland.
Validity of the findings: I suggest rewriting this section explaining the results of the study and not only reporting them. An accurate comparison with the findings of other researchers is needed. More explanation and justification of your results are required.
In the end, I suggest adding some tips to reduce sedentary behavior during the lockdown period or to return to an active lifestyle in a safe way.
Additional comments: I would thank the author for this paper, the aim of this study was sure interesting. The unique period that we all are living needs evaluation and consideration. Before publication, this work needs many corrections.
In general, this manuscript showed several mistakes that required revisions. The introduction section and the discussion section showed a lack of clarity and logical paragraphs constructs. English languages need a relevant revision. Many phrases are not supported by recent literature. Then, I suggest to re-write the abstract in accordance with the corrections.


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: PERCEIVED PHYSICAL ACTIVITY DURING STAY-AT-HOME COVID-19 PANDEMIC LOCKDOWN MARCH–APRIL 2020 IN POLISH ADULTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: investigating the perceived physical activity during the stay-at-home lockdown March-April 2020 in Poland. I really appreciate the effort of the authors working in this field, because there are few evidences regarding the consequences of lockdown and social distances on physical activity and its impact on health. From a methodological standpoint, the research was well conducted. However, several issues need to be fixed to improve the general quality of the manuscript. At this stage, my indication is to request a support of a Native English speaker to improve the general readability of the article.

Lines from 46 to 76. In my opinion, the introduction need to be more hypothesis driven to allow readers to see the basis of your study. It is important to be clear what the practical question was trying to address to help readers to understand your study. The key issue here is to set-up the experimental approach to your study.

Line 53. I would suggest to insert here as a paragraph the part relating to the Poland National Health restrictions (Lines from 87 to 116), in order to give to the readers what was the situation in Poland.

Lines from 67 to 69. I would suggest to include here as a reference a recent article of Vitale et al, 2020 (PMID: 33352676) who evaluated the effect of a six-month home-based resistance-training program on muscle health and physical performance in healthy older subjects during the unique condition of home confinement caused by the COVID-19 pandemic in Italy.

Lines from 71 to 76. My suggestion is to define pre-specified primary and secondary aims. This will help readers to understand the research question that you are trying to address.
Experimental design: The methods needs to be improved so the study can be replicated as to equipment, subjects, context of physical activity level and rationale for the design of each dependent and independent variable. Therefore, readers needs to know more about enrolment, subjects procedures etc.

Lines from 80 to 85. I would suggest to call this paragraph “Study design”. Please, describe also in this paragraph the study design and the experimental approach to the problem. In accordance to the pre-specified primary and secondary aims of your study, you have to describe here the primary and secondary outcome measures, including how and when they were assessed. At this point a flowchart of the study will help readers to understand the temporal order of your study.

Lines 81 and 82. I would suggest adding here “all procedures were performed in compliance with laws and regulations governing the use of human subjects (Declaration of Helsinki)”. Please check it over.

Line from 82 to 84. I would suggest adding here “All subjects received explanation of purpose, methods, potential risks and benefits of the study and written informed consent was obtained from all participants”.

Lines from 118 to 124. Please place here all the information regarding the inclusion and the exclusion criteria of subjects’ participation in your study.

Line 125. I would suggest to move “There were 326 records registered in Google Forms between 08 – 21 April 2020” in the results section.

Line 126. I would suggest to move “The survey was anonymous.” In the survey section.

Line 125 and 126. I would suggest to move “All participants 126 volunteered to participate in the study (by ticking the online box).” In the study design section.

Line 127 and 128. I would suggest to move “Data from one participant was removed as she was 14 years old, whereas the IPAQ-LF is dedicated to adults.” In the result section.
Validity of the findings: In your result section, please insert only the raw results and the specific p values without discussions or speculations.
I would suggest creating only one table about the participants’ characteristics at baseline. Specifically, please merge Table 1 and Table 2 together.

I would suggest creating only one table regarding the Bayesian t-test results. Specifically, please merge Table 3, Table 4 and Table 5.

I would suggest creating a panel with your Figure 1, Figure 2, Figure 3 and Figure 4.

Line 208. I would suggest calling this paragraph “Study population”.

Line 210. Could you please specify here which the contraindication to exercises were?

Line 213. Could you please justify why you did not disqualify the missing data from your analysis?

Lines from 293 to 338. The discussion needs to reflect what you found, how it relates to the literature and then what it means physiologically or from a practical aspect and each paragraph should be in a logical sequence as at present it is a bit hard to follow. The clarity of your discussion needs to be improved a bit and qualified where appropriate as you need to stick to what your experimental design can tell us with your data and limit speculation or qualify them, and make sure that your statement are referenced.

Lines 319 and 320. I would suggest to delate the first limitation of your study. In fact, I understand that you have performed an observational study which does not need a randomisation process.

Line 341. I would suggest inserting in your conclusions the practical application of your study. What should now physicians, trainers and practitioners now have to do after reading your paper? Does it affect practice is the key factor for this section.
Additional comments: Line 55. I think there is a sort of typo at the beginning of the line.


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: PERCEIVED PHYSICAL ACTIVITY DURING STAY-AT-HOME COVID-19 PANDEMIC LOCKDOWN MARCH–APRIL 2020 IN POLISH ADULTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I think it's appropriate and clear
I would not make any recommendations to that effect.
Experimental design: the research question now is well defined, and the research is original.
Further, aims are clear
Validity of the findings: Paper talk about the pandemic period, it is interesting and now the conclusion supports the results
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: PERCEIVED PHYSICAL ACTIVITY DURING STAY-AT-HOME COVID-19 PANDEMIC LOCKDOWN MARCH–APRIL 2020 IN POLISH ADULTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: In the conclusion section, I suggest adding a sentence about the sedentary habits reduction, also by specific advice/suggestions provided by the Government, but the limitation of virus transmission remains the first imperative condition.
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: PERCEIVED PHYSICAL ACTIVITY DURING STAY-AT-HOME COVID-19 PANDEMIC LOCKDOWN MARCH–APRIL 2020 IN POLISH ADULTS
Review round: 2
Reviewer: 3

Output:
Basic reporting: Nothing to report.
Experimental design: Nothing to report.
Validity of the findings: Nothing to report.
Additional comments: Thank you for addressing my comments. Congratulation the article has improved, and in my mind, ready for publication.


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

Input:
Title: ALMOST ALL KNOWN SAUROPOD NECKS ARE INCOMPLETE AND DISTORTED
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I liked reading this article: In a time of ever more sophisticated methods, it is good to be made aware of the general imperfections of the fossil record - your method might be extremely exact and sophisticated, but if the basic data is insufficient, your results can still be highly questionable. I thus recommend the article for publication. As this is mainly a manuscript reminding us of this simple fact, I have little to add, and have made most of my comments on the annotated manuscript, which is attached. I would only add a few further, more general comments here.

- This article makes it clear how important mode of preservation and taphonomy is for our understanding of fossil organisms. Even if a skeleton was not found articulated, the exact mode of preservation can make a difference to our understanding of its original anatomy. Important aspects might be the degree of disarticulation, the transport or sorting of elements, general modes of compaction or distortion, and, very basic, whether remains of other animals have been found in the same locality or not. All of this information will have an impact on how reliable a reconstruction of such aspects as neck length might be seen. It might be worth to point this out somewhere in the text: report not only what of an animal has been preserved, but also what has not been preserved, what other animals might be present, and how the remains were found.

- As for the materials of Giraffatitan (skeletons SI and SII), I would be less critical than the author concerning the articulated series of SII. From the comments by Janensch and additional field sketches (one of which was reproduced by Heinrich 1999: fig. 18) it seems clear that most of the presacral vertebral column of this individual was indeed found in articulation, with only one vertebrae having been slightly rotated from its original position (but without disturbing the sequence of vertebrae). Thus, the sequence of vertebrae seems to be at least complete as far as it was preserved (with no additional elements missing) - whether the first preserved vertebra was C3 (as argued by Janensch) or might have been another number, cannot of course be said on the basis of these considerations alone.

- Identification of cervicodorsal transition: It might be worth to see how this is in other archosaurs, as similar problems exist, for example, in theropods. Here, the most reliable identification of the first dorsal vertebra is the form of the rib - cervical ribs are parallel to the vertebral column, whereas dorsal ribes stick away from it, and this is usually used to identify this transition in cases where you have complete, articulated skeletons. Other possibilities for identification exist as well, though, and it might be good to reference some of these problems here.

- In the discussion it might be good to also show ways towards possible solutions. Do you think digital retrodeformations might help with deformed elements? And if so, what would be the criteria for retrodeformation? What is your view of the evolution of cervical vertebral number in sauropods, in the light of your results from looking at how much we know about complete series? Might phylogenetic bracketing help in decisions about how many vertebrae there were?
One thing that I think is clear from your manuscript is that careful documentation of the taphonomy of specimens in the original osteological description can indeed help to judge whether a given number of cervical vertebrae is realistic, or should be seen with caution. The same argument could be made for species for which more than one specimen is known - if you can find reliable criteria for identifying vertebral number in partial articulated specimens, this can then be used to overlap different individuals to reach a reliable vertebral count (Does this apply to any of the cases dealt with in the manuscript? Given, for example, that multiple specimens of Diplodocus are known, is it really impossible to say with certainty that Diplodocus had 15 cervicals, or can we get to this conclusion by overlapping several partial, articulated skeletons?). I would suggest to add these points to the discussion to improve anatomical description and reasoning for giving vertebral counts.


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: ALMOST ALL KNOWN SAUROPOD NECKS ARE INCOMPLETE AND DISTORTED
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a clearly written and well presented paper, with high-quality figures. I would like to compliment the author on the detail of his scholarship, with extensive examination of the relevant literature. I found a few typos, grammatical errors, and other minor problems,listed below –

Lines 22-23 Abstract – ‘deposited quickly enough to cover a giant carcass on land; and distortion of presacral vertebrae is common due their lightweight hollow construction. This ubiquitous incompleteness’

‘due their’ should be ‘due to their’

Line 44 – ‘…The consequent incompleteness of known sauropods’ necks, and the ubiquitous…’

This should be ‘sauropod necks’

Lines 227-228 – ‘…Mamenchisauridae — although it is unfortunate many of these specimens are not well well described in English:’

Repetition of ‘well’

Lines 600 onwards – discussion of sauropod body size and preservation. This section would benefit from incorporation of the findings of Cashmore et al. 2020, Palaeontology.

Lines 638-641 - For highly pneumatized cervicals in particular, the chance of the shape surviving through taphonomy, fossilisation and subsequent deformation would be tiny, as is also the case with the vertebrae of highly pneumatic fossil birds.’

This statement about fossil birds could do with a supporting reference.

Lines 668-676 - ‘…we may never know. None of this is necessarily disastrous, so long as we properly acknowledge the degree of uncertainty that afflicts our work. Problems arise when studies such as that of Stevens and  Parrish (1999) draw apparently firm conclusions about sauropod neck posture based on  specimens that are deficient in respects not acknowledged in the text, lending the results a veneer  of definitiveness that they do not merit. It might be argued that the venue of this study (Science)  is too constrained for space to allow a proper discussion of degrees of uncertainty; this may be  true, but is really only an argument that such venues are not suitable for the publication of  rigorous scientific work.’

First, I think that suggesting that Science might not be a suitable venue for rigourous scientific work could cause offence. Second, in any case, the issue of limited space in short format journals has been greatly alleviated by the ability to publish extensive online supplements. I think the author should remove or greatly modified the point being made here.
Experimental design: I have two fundamental, and I fear fatal, problems with this paper. First, and most importantly, I think it attempts to address a problem that does not really exist. It sets up a strawman with regard to the need to tell researchers that sauropod next are less complete than we previously thought. However, I would argue that we are well aware of these issues and that the current paper does not provide convincing evidence that there is a problem with the way we are doing things now. To be clear, I am not saying that the incompleteness of sauropod necks is not a problem – it definitely is. What I’m saying is that there is little value in a paper whose main message is to tell us what we already know and take into account (as far as we can) when looking at neck function and phylogenetic characters. The author does not provide a convincing case for why the details he gives need to be presented to his fellow researchers – he would need to document substantial cases of current or very recent work that has gone badly wrong because of an unawareness of the issues – generally this justification is missing from the paper (see below(. It may well be that members of the public etc are misled by the level of certainty put across in some scientific papers – but the author has already published three blogs and a preprint on this issue, I would imagine that that is sufficient. The scientific community working on these issues does not need to be reminded of the general importance of understanding the limitations on the data we use

The second problem is that the paper is rather qualitative, with the possible exception of the introduction of some indices relating to aspect ratios (which is novel). There are a number of ways in which the paper could become more quantitative and statistical, and I suggest some of these below. Nevertheless, without a meaningful research problem to address, the addition of such analyses would be pointless at the current time. I justify these views below by quoting portions of the paper and giving my responses.

Lines 38-39 – ‘…rudimentary measurements to be made – for example, neck length or shoulder height. In fact, the problem is more significant than is generally realised. It is not just that we do not have large…’

The utility of this paper hinges largely on the claim that the problem is greater than is generally realised as stated above. However, there are no references to back this up (at leat from the last 20 years), and no analyses to demonstrate that palaeobiologists are making the mistake of ignoring the problems with sauropod neck preservation. Rather, those of us working on these animals are very well aware of the problems already, down to the individual specimen level, but we use the data we have with caveats (a good example is the set of assumptions made by Bates et al 2016 when they needed to estimate sauropod neck lengths and volumes). If the relevant workers are already aware of the problems, then what is the value of publishing a paper that tells us what we already know? None. The author must show that a reasonable number of recent studies have made Significant errors by assuming greater completeness of necks than is warranted.

Bates, K. T., Mannion, P. D., Falkingham, P. L., Brusatte, S. L., Hutchinson, J. R., Otero, A., Sellers, W. I., Sullivan, C., Stevens, K. A. and Allen, V. (2016). Temporal and phylogenetic evolution of the sauropod dinosaur body plan. Royal Society Open Science, 3, 150636.

Similarly –

Lines 256-257 – ‘Several well-known sauropod specimens are often thought of as having complete, undamaged necks, but in each case the truth is less clear. I now discuss three important specimens.’

And

Line 658 – ‘What does it all mean? Only this: we don’t know as much as we may assume we do.’

Again, there are no references cited in the above quotes to back up these claims. Who has claimed these necks are undamaged and complete? I bet that in most cases, palaeobiologists have described these as ‘nearly’ or ‘virtually’ complete, or a vague ‘well preserved’ – rather than really stating that these are truly undamaged  and complete even down to the atlas etc (when is a sauropod ever undamaged in the strict sense?]. To suggest that palaeobiologists working on sauropods are unaware of these issues or are making false assumptions about completeness/preservation is, to my mind, setting up a straw man that is then easily knocked down in this paper.

In fact, I would argue that even the evidence presented by the author supports my point about the attitude of palaeobiologists. The examples given of researchers perhaps being over-confident are from very old literature – Hatcher 1901 etc. Other contemporaries such as Holland were clearly sceptical about the number and completeness of the cervicals of Diplodocus, and even Hatcher’s work includes some caveats. Where is the evidence that even these historic researchers, let alone modern ones, are working on the basis that sauropod necks are complete and undamaged?

The nearest we get to modern researchers making a false assumption about neck completeness and getting it wrong is given in the section on Apatosaurus. Here, Stevens and parrish 1999 assumed a complete and well preserved neck for their biomechanical modelling, even though the last three cervicals were badly crushed and heavily restored. So, modern researchers can be over confident at times., However, interestingly this problem was spotted by Upchurch 2000 (both references cited in the current paper). So, clearly researchers are already on the lookout for such unwarranted assumptions, and either address them in their own work, or criticise others when they overstep the bounds of what represents a justifiable simplification/assumption/extrapolation made for the purposes of making progress.

Around lines 490, the author also cites the Elongation Index as a good example of where ignoring distortion could cause major errors in phylogenetic data, taxonomic comparisons or functional analyses. I agree. However, the elongation index has been largely replaced by the Average Elongation Index. Whereas the former is based on centrum length divided by height ()and is therefore very prone to problems caused by distortion), the latter uses centrum length divided by the average of the height and width of the cotyle. It is conceivable that, as a centrum is crushed vertically so that its height is artificially reduced, is width is also artificially increased. Therefore, AEI might be less prone to problems caused by crushing. We cannot be sure of this, but the author’s point would be enhanced if he looked at AEIs. Indeed, a comparison between AEI and EI could be instructive, as would a comparison of AEIs across sauropod necks and extant taxa. I encourage the author to go down this route in the future.

Lines 658-667 – ‘…We don’t even know how many cervical vertebrae well-known sauropods such as Diplodocus and  Giraffatitan had. We don’t have complete necks for either of these sauropods, nor for almost any others. Even those we do have are in some cases badly crushed (e.g. Mamenchisaurus hochuanensis). We are woefully short of sauropod necks.  As scientists, we must carefully avoid blithely asserting factoids such as “Diplodocus had 15  cervicals and Giraffatitan only 13”. We simply don’t know know whether this is true. Evidence  supports it as a hypothesis – these numbers are certainly the best guesses for the taxa in question – but a hypothesis is all it is. Hypotheses of neck posture and flexibility should be held even more lightly, since they are based on inferences drawn from distorted elements who true shapes

I think the author overstates the case here. Clearly such statements are hypotheses and should be regarded as such. But I would argue that they are already regarded as hypotheses. seWe all, as professionals, talk to each other in a shorthand which to the outsider might sound like we are pronouncing facts when we actually mean hypotheses. This is done for brevity, not because we have assumed that hypotheses are facts. For example, it would become rather tedious if every paper on sauropods had to say things like ‘Giraffatitan is thought to have 13 cervicals, although there are several factors that mean caution is required’. In any case, I think my colleagues are fairly cautious, and I’ve often seen ‘estimated or ‘?’ placed before such numbers. No doubt the literature contains some sloppy or imprecise phrasing, but there is no need to write a paper based on this, unless the author can show that such imprecision is causing major errors in our understanding of the animals.

For me, the strongest and most useful part of the paper is the review of how the cervicodorsal junction is identified in sauropods. certainly, this is a problem, and the author is right that many modern workers still state cervical and dorsal numbers without clearly explaining why they have drawn the line between them. However, this section needs further work. For example, if we are uncertain how to draw the line between cervicals and dorsals, how can we cite evidence that critiques some of the criteria used to define the cervicodorsal junction? A good example is that of Mamenchisaurus hochuanensis, cited in this paper. the author points out that posterior cervicals can have free rather than fused ribs, and mentions that the last three cervicals of M. hochuanensis have free cervical ribs. That’s correct, but this depends on the view that the cervicodorsal junction occurs after presacral 19 – if we assume that there were actually just 16 cervicals, then the free ribs would only occur on dorsals, and the valid status of this criterion would be restored. Such argumentation would, of course, then contradict other criteria such as parapophysis position etc. – but this example serves to demonstrate the difficulties in adequately analysing the strengths and weaknesses of different criteria for definition of the cervicodorsal junction, since the evidence for or against them in part depends on first knowing where the cervicodorsal junction is. Moreover, for me, this discussion of the cervicodorsal junction is incomplete. Many other workers have discussed this issue – e.g., see Wilson and UPchurch 2009 – and there are other criteria that could be considered (e.g. number of vertebrae anterior to the first appearance of the hyposphene). In short, this section has potential, but in its current form I do not think it stands up as a publishable unit in its own right.
Validity of the findings: The findings are valid insofar as they provide evidence that sauropod necks are incomplete and discuss these issues in detail. The evidence that incompleteness and distortion are widespread is correct. However, as noted above, I do not find that the research question is a valid one for a scientific publication. Documenting a problem is only useful if fellow researchers are not aware of it and are making invalid assumptions. Of course, given the available sauropod necks, we do make some assumptions and approximations in order to use data for functional and phylogenetic work – what the author needs to do is demonstrate that the conclusions from such work have been significantly compromised buy such assumptions and approximations because of a lack of awareness of sauropod neck incompleteness and distortion – but he does not really do this.

Also –

Lines 189-192 -• ‘…MOZ-Pv1232, the holotype of Lavocatisaurus agrioensis, described by Canudo et al. (2018). This is complete from C1-C11. Canudo’s guess is that this is complete neck (Jose I. Canudo, pers. comm, 2021), but the specimen doesn’t demand that conclusion and no known eusauropod has fewer than 12 cervicals.’

This claim about no known eusauropod having fewer than 12 cervicals is bold and problematic given that this paper also argues, quite rightly, for difficulties in estimating cervical number because of the problem of determining exactly where the cervicodorsal junction lies. For example, in Amargasaurus there are just 22 presacrals – it is hard to tell how many of these are dorsals and how many cervicals - but in my personal observation of the specimen I suspect that there might just be 11. So, a more cautious and nuanced statement is needed here.
Additional comments: I reviewed the previous version of this paper. The author has certainly attempted to take my criticisms, and those of the other reviewers, into account. Certainly the discussion of various necks is much more comprehensive now. However, the fundamental problem has not been addressed, because in my view it cannot be addressed. As I have said above, telling fellow researchers that a problem exists, when those researchers are already aware of that problem, does not represent a meaningful Advanced in our knowledge. I recommend that the author should focus on a more quantitative assessment of Completeness and distortion, and then use these data to look for potentially interesting taxonomic and/or taphonomic patterns. This might actually make a useful and novel contribution. For example, rather than the qualitative assessments of neck completeness in the current paper, perhaps the author could look at completeness from the point of view of the completeness metrics developed by Mannion and Upchurch and subsequently used by many others. This could be combined with the AEI study noted above. Finally, it is one thing to show that distortion affects the proportions of cervicals, but the author needs to show that this makes a difference to phylogenetic and functional studies – e.g., buy showing that variation in proportions from one cervical to the next  means that a taxon scores a 0 and a 1 for a given character. He might also form collaborations with other workers to look at how distortion might affect functional interpretations and whether this is adequately handled By current sensitivity analyses.


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: ALMOST ALL KNOWN SAUROPOD NECKS ARE INCOMPLETE AND DISTORTED
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript is a really interesting (critical) review on more classical bibliography, gathered together with actual references and discussions with other researchers.

By providing in-deep analyses and discussions on the preserved sauropod remains and their descriptions, this work opens our minds, questioning the validity of the term "completeness" when speaking to articulated/associated fossil remains. This should serve as basis for re-studing the other sauropod "complete" necks, but also when describing other skeletal material.

The table and figures are informative and complement with the text of the manuscript.

I have no further comments or suggestions, and recommend this manuscript for its publication as it is.
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: IMPERVIOUS SURFACE AND LOCAL ABIOTIC CONDITIONS INFLUENCE ARTHROPOD COMMUNITIES WITHIN URBAN GREENSPACES
Review round: 1
Reviewer: 1

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: Dear authors,
Thank you for the opportunity to read and review your text. I read the paper with great interest and I think that the topic is very important. In particular, I appreciate that you have taken a multi-taxon approach to your work, which is extremely important for understanding biodiversity dynamics along rural-urban gradients. I understand that identifying such a large number of different orders is very difficult and time-consuming, but I think that the importance and significance of your study would be much greater if it were possible to identify at least some orders further down to species. In the current version, unfortunately, too much significance is lost for me, as the environmental effects are only analysed in relation to a very rough taxonomic level. Symptomatic of this is, for example, the NMDS (Figure 2), which only shows the arrangement of different orders along the gradients. What is really exciting, however, is whether certain species communities develop within the orders and whether there is an effect of urbanisation.
I am sorry that this criticism means that I cannot recommend the text for acceptance. Overall, the methods are very well chosen, the study design is very good and the flow of thoughts is also very good. I would therefore encourage you to identify the species in at least some orders and then repeat the analysis. If you do this, you could still consider the different management of the plots (I had understood it to mean that the plots differ in this respect). If a further determination of the species is not possible, it would be a possibility to work with morphospecies in order to have a better value for diversity. Taking the number of taxonomic orders present at each site as a measure of species diversity is problematic because it is very inaccurate and not a measure of actual species diversity.
I wish you much success and would be happy to review a new version of the text.
Best regards,
Sascha Buchholz


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: IMPERVIOUS SURFACE AND LOCAL ABIOTIC CONDITIONS INFLUENCE ARTHROPOD COMMUNITIES WITHIN URBAN GREENSPACES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This study investigates the arthropod communities within different urban greenspaces across metropolitan Grand Rapids, Michigan (USA). The manuscript is well written and the general idea of the work is good, I enjoyed reading it. However, I found some issues that are of concern. The main observation is the use of level order to determine the species richness and diversity. I am afraid it is difficult to obtain conclusions regarding biodiversity with such a broad level of identification. For abundance, I think it is not a problem, but it is for richness. Authors should give a proper explanation of why they did that when available keys and specialists are in the USA. Otherwise, they should be very careful with the scope of their conclusions and mention this point as a limitation of the study. On the other hand, I am worried that the authors did not distinguish in the models between the two types of green areas used. Urban gardens and pocket prairies may be different in terms of plant species richness, plant origin, management,  etc, so if authors did not measure any of these variables at least they must include the type of site into the models.
In the Introduction there is no mention of the possible effects of flower availability on insects, a variable included then into the models. One would expect that will be important for pollinators, of course, but what about other groups? Why also did you explore the effects of different colors? Please explain and give predictions also about that. In addition, there is no reference to temperature and humidity in terms of previous evidence on insects in urban areas or what you could expect regarding those variables in your study system. Please add some background on that which may help to formulate your predictions. The work of Fenoglio et al 2021 could help to give you a broader picture of the inter-relations between different urbanization drivers.

Fenoglio, M. S., Calviño, A., González, E., Salvo, A., & Videla, M. (2021). Urbanization drivers and underlying mechanisms of terrestrial insect diversity loss in cities. Ecological Entomology. DOI: 10.1111/een.13041
Experimental design: Several issues in Material and Methods should be addressed:
Line 103: Please characterize a bit more the two types of sites considered
Line 104: are there familiar or community gardens?
Lines 117-118: Which values did you use of temperature and humidity in the analyses? What was the average mean daily temperature during the sampling period? Please clarify
Line 118: Regarding the 15m transect, how did you choose the starting point, you went always to the north/south, please add more information.
Line 119: You measured only the number of total flowers, but not plant species richness which is known to affect insect diversity. Why that? Please clarify
Line 119: You have considered four colors of flowers, please explain or cite a reference to justify that selection
Lines 120-121: Why did you use two sizes of bowls? Please explain
Lines 128: You should provide some kind of justification for estimating species richness at the order level. Besides, in methods, you did not mention anything about diversity (how did you calculate it for example). I strongly suggest being consistent along with your manuscript with the response variables used as well as with the explicative variables, from the introduction to the discussion.
Line 153: Here you said that you used as a response variable the abundance of two orders, why that? Please explain better
Line 155: The models showed in S3 to S7, which response variable have? It is not clear to me what did you do. Did you do that to select the variables entering the model? why?  In addition, you could condense all these separate tables into one larger in order to have fewer supplementary files.
Validity of the findings: Results
Lines 189-190: Now it seems that you considered also Diptera abundance but you did not mention it in methods. Please, put this part in the methods sections and justify it.
Fig 3D: Please change the name of the “y” ax to arthropod richness

Discussion
In general, I found you did not discuss some parts of the results. For example, there are no almost discussions related to temperature effects on overall insect abundance and Hymenoptera abundance (I see in references the work of Dale & Frank, 2017 but it is not mentioned in the text).
Urban Ecosystem, 21, 419–428.
In addition, when you talk about the importance of flower additions for insect abundance (lines 218-220), please be careful in the way you explain that since you found that the number of flowers had no effect on it. Besides, you did not discuss anything about the effects of different variables on insect composition, for instance, the close relation between humidity and Dermaptera or Hymenoptera and white flowers.
You should mention the caveats of the study and the scope of the interpretations of your results if you insist on maintaining diversity at the order level. You possibly will be underestimating the effects of any of the other variables, beyond the impervious surface, if you consider such a level of resolution in your taxonomic identification.
Additional comments: I think the article could improve a lot after considering all my commentaries.


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: IMPERVIOUS SURFACE AND LOCAL ABIOTIC CONDITIONS INFLUENCE ARTHROPOD COMMUNITIES WITHIN URBAN GREENSPACES
Review round: 1
Reviewer: 3

Output:
Basic reporting: I have reviewed the article entitled “A survey of above-ground arthropod communities within urban greenspaces in Grand Rapids, Michigan (USA)”. Maher and collaborators investigated insect communities in urban gardens and prairies and their responses to environmental factors related to urbanization and flower availability. While the topic is not entirely novel and there are several studies addressing similar questions, I think it can be a valuable contribution to improving our understanding of community-level responses to urbanization. Nevertheless, I have found many important issues that need to be addressed in order to improve the data analyses and provide clear communication of their results. In my opinion, the article could be substantially improved after revising all the listed aspects. In the following three sections, I outline my major suggestions, whereas in “general comments to the author” I listed several minor suggestions.

English writing is good and clear in most of the manuscript. The context provided in the introduction is supported with appropriate references and generally covers the needed topics. Perhaps the paragraph on lines 51-68 condenses a lot of information, but it is not entirely clear. Maybe the first part, regarding impervious surfaces and their effects on the abiotic conditions of cities could be integrated with the first paragraph and the second could be focused on biotic homogenization?

Raw data is fully provided as supplementary tables. Finally, all the figures are justified and of good quality, though I have some suggestions for all of them.
-Figure 1: It would be good to add a panel showing one site as an example, with a landscape circle around the study site to clearly visualize the impervious cover in one of the sites. Perhaps adding a photo of one garden and one prairie in Figure 1 on a separate panel would help readers to get a better idea of how the two types of sampled habitats.
-Figure 2: I think that plotting the study sites in the NMDS would help to visualize how different were your sites if gardens and prairies had particular environmental conditions, and if the insect orders were related to particular sites as well.
-Figure 3: the legend from Fig. 3 needs more detail. State clearly that you are showing raw data points and what do the lines represent. Are those the fitted lines from the GLMs? Also, adding the confidence intervals for those fitted relationships would be nice.
Experimental design: -I believe that the research topic is relevant and fits well within the scope of the journal. At the same time, the main research question and the specific questions addressed by the authors are specified, although the hypotheses and predictions need some additional work.
Firstly, not all investigated drivers are described in the introduction. The focus is on the gradient of impervious, but adding a small paragraph with more details on the remaining environmental drivers would be helpful to understand their design. In connection to this, the hypotheses and predictions are a bit vague and the authors’ expectations regarding drivers other than the impervious surface would be interesting. I think the choice of the variables is logical and that the authors had previous ideas about how them would affect insect, so it would be good if they described them in the hypotheses. On another hand, the choice of particular flower colours as predictor variables needs to be justified as well. Was that based on a priori hypotheses or literature? Or was the decision taken based on the abundance of flowers?
-A relevant issue, in my opinion, is the study sites. Gardens and prairies are used as replicates but they can certainly be different. I imagine that prairies and urban gardens are structurally very dissimilar and are subjected to different levels of management. Therefore, I think habitat type should be included as an additional predictor in the models to account for this possible difference. Note that this is also interesting, as the authors could determine if one of these urban green spaces has a higher potential for supporting insect communities. Finally, I believe pocket prairies need to be defined clearly. I am not familiar with the term and the text gives only a slight idea of what they are.
-Another important thing is that the authors use the number of orders as a proxy of richness and to calculate indices of diversity and evenness. I believe that more caution should be taken here. Despite that there is a clear variation in the number of orders, I do not agree that this can be called “species richness”. I am not familiar with studies using order richness as the response variable and calling this species richness, not even in those studies using family richness. Thus, I think that throughout the text, if the authors decide to keep order richness, the variable should be called like that (and community/order diversity and evenness, perhaps?). And if there are studies published using a similar method, it would be good to cite them in methods. Furthermore, I expect at least a brief mention of this limitation in the discussion as well.
-L 146-150: why did you measure collinearity between response variables? I agree with the method regarding environmental variables, but I don’t think response variables need to be reduced in this way, as they are not evaluated within the same model. Even if Diptera and total abundance are correlated, they could respond differently to environmental variables, so I think you should use Diptera abundance as a response variable as well.
-Statistical analyses: Why not performing models with more than one environmental variable? Interactions between variables probably cannot be analysed due to the reduced number of replicates, but additive models with at least combinations of two environmental variables could be tested, as both structural and climatic variables could affect your response variables conjunctly (see Fenoglio et al., 2021 for a revision of the combined effects of multiple drivers). In connection with this, I would include habitat type as an additional predictor as mentioned above. Moreover, the results of additive models including, for example, both impervious cover and flower availability may provide a clue about the effects of both factors discussed in lines L213-224.
The R code provided in the supplementary material suggests that you had a full model with all the environmental drivers, but this is not reported and the methods suggest that only univariate models were tested. Also, the code and text suggest you used GLMs, but the family (i.e., error distribution) is not specified. Was it a Poisson distribution for order richness and abundance? Was overdispersion not a problem with abundance data? Models for diversity were GLMs or LMs with a Gaussian distribution? This needs to be described in more detail.
In connection with statistical analyses, why did the authors average the June and July samples instead of using separate samples from each month and using mixed models? A lot of variability in the data linked to climatic variations (and/or flower availability) could be lost, reducing the probability of finding relevant effects of these variables.
Validity of the findings: I think the replication is acceptable and allows the authors to test for the investigated factors. The data are robust but the taxonomical level of identification should be justified, and the statistical analyses should be revised (see comments in the previous section).

The conclusions section is mostly describing which type of studies are needed in the future, so I think it needs to be reshaped. These observations could be included in a paragraph addressing the taxonomical limitations of the study, whereas the conclusion section should focus more on the interpretation and relevance of their result. I encourage the authors to re-analyse their dataset following some of my previous suggestions and I expect this section to change at least partially.
Additional comments: Minor comments:
-This is just an opinion, but the title is not very attractive and sounds rather local. I think switching to a title stating the main results would be much more interesting and catchy.
-L 80: the end of the sentence is not completely clear to me. Are you stating the previous research (the references from that sentence?) suggest that greenspaces benefit people and arthropods? It reads as if performing research on green spaces provides the benefit, but I do not see the link.
-L 93: perhaps here it could be specified that impervious surfaces were measured at the landscape scale. Some studies include this variable on a rather local scale, so it is good to indicate which approach you took from the beginning.
-L 106-108: I don’t see why the permissions for using those discarded 4 sites should be mentioned. Instead, I would only leave the minimum distance that we selected to maximize spatial independence.
-L 114: considering the international readership of the journal, I suggest at least add the temperature in °C.
-L 153-154: were Hymenoptera and Hemiptera (please use uppercase letters when writing the Latin order name) chosen based on their abundance? If so, please indicate the minimum abundance that you considered to make analyses on separate orders.
-L 207-208: in my opinion, this sentence would read better if rephrased as “shows that the impacts of urbanization may be difficult to overcome for some taxa” or “shows that for some taxa the impacts of urbanization may be difficult to overcome”.
-L 214-215: mentions to figures are not common within the discussion and, since you only refer to these two examples, I believe it is better to remove them.
-Lines 235-237: indeed. There are evidence for this that you could mention in this sentence. For example, Sanchez Dominguez et al. (2020) found that landscape-scale grassland cover increased predation rates.
-L 242-254: I think more discussion on temperature effects (i.e., heat island effect) is needed here. Despite that most studies working on the urban heat islands are focused on herbivorous insects and not on community-level responses, McGlynn et al. (2019) is a recent example of how temperature affects a highly diverse insect group.

References cited:
-Fenoglio, M. S., Calviño, A., González, E., Salvo, A., & Videla, M. (2021). Urbanisation drivers and underlying mechanisms of terrestrial insect diversity loss in cities. Ecological Entomology.
- McGlynn, T. P., Meineke, E. K., Bahlai, C. A., Li, E., Hartop, E. A., Adams, B. J., & Brown, B. V. (2019). Temperature accounts for the biodiversity of a hyperdiverse group of insects in urban Los Angeles. Proceedings of the Royal Society B, 286(1912), 20191818.
- Sanchez Domínguez, M. V., González, E., Fabián, D., Salvo, A., & Fenoglio, M. S. (2020). Arthropod diversity and ecological processes on green roofs in a semi-rural area of Argentina: Similarity to neighbor ground habitats and landscape effects. Landscape and Urban Planning, 199, 103816.


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: IMPERVIOUS SURFACE AND LOCAL ABIOTIC CONDITIONS INFLUENCE ARTHROPOD COMMUNITIES WITHIN URBAN GREENSPACES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Thank you for the revision of the text. I am very glad that it was possible to make further species identifications and thus significantly increase the information content and informative value of the study. It is still a very large consideration of urban biodiversity but nevertheless the morphospecies approach succeeds very well in making an interesting contribution to urban ecological biodiversity research. In my opinion, the study is now an interesting contribution that should definitely be published. The statistical models have clearly gained in precision and the results and statements are now easier to understand.
Experimental design: See 1.
Validity of the findings: See 1.
Additional comments: no 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: IMPERVIOUS SURFACE AND LOCAL ABIOTIC CONDITIONS INFLUENCE ARTHROPOD COMMUNITIES WITHIN URBAN GREENSPACES
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript has improved a lot since the authors considered most of the aspects that reviewers pointed out. I really appreciate their effort to
Identify to a lower taxonomic resolution the species found. However, there are still some issues (especially related to statistical analyses) that need to be to be revisited or better justified. I consider that the manuscript will be publishable after the authors consider these comments.
Experimental design: The main problem I see is related to the construction of the statistical models. Previously, one of the reviewers has observed and asked why doing univariate models instead of additive ones. The authors argued that by parsimony they decided still work with univariate models. However, for me is not a fully reasonable explanation since biologically is more probable that two variables like humidity and temperature act in an additive way than separately. If authors tested those models, as they mentioned in the rebuttal letter, why they do not include those results as well? Besides the problem of multiple hypothesis testing is that there is always a chance that what the result considers true is actually false (Type I error), thus some kind of correction should be applied (perhaps Bonferroni is too conservative, but there are others). In addition, I do not understand why they tested multicollinearity between independent variables if then they used univariate models. This is not consistent, please correct it. In addition, there is a mistake in the term used in line 160: the correlation test was used to “check” possible multicollinearity problems not to “reduce” as they said. Please, in case you decide to keep the models the way they are, I strongly suggest adding a reference to support your model construction and selection.
On the other hand, the authors mentioned that quantified the number of flowers of different colors but in the analyses, red and orange flowers did not appear and the reader does not know why. Please, clarify.
Regarding overdispersion testing, is not clear which adjustments they did…did they change the distribution? To a quasipoisson or negative binomial? Please better explain
Validity of the findings: The validity of the findings depends on a clear justification of the statistical method used or instead the use of a proper one that consider several variables in just one model.
Additional comments: No additional comments