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: FRESHWATER CARBON AND NUTRIENT CYCLES REVEALED THROUGH RECONSTRUCTED POPULATION GENOMES
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: Linz et al. present additional analyses of 3 time-series metagenomic datasets, which were collected over several years from 2 fractions of a humic lake, Trout Bog (3 years) and 1 fraction of eutrophic Lake Mendota (5 years).   They provide 1) gene-centric analyses of the metagenomes (pooled by fraction) examining the differential distribution of a set of functional marker genes, and 2) population-genome-centric analyses of metagenome-assembled-genome bins (MAGs).  With the marker-gene analyses they infer differences in multiple metabolic pathways among the lakes and water column fractions.  They then use the MAGs to associate the identified processes with specific taxa, finding that certain metabolic processes appear to co-occur within taxa, and that common processes across sites are associated with (and attributed to) differing phylogenetic groups.  This manuscript is very well written and organized and materials and scripts have been provided to make it reproducible. The following two main concerns regarding their analyses and interpretations should be addressed:

1) 'Community Functional Marker Gene Analysis' Lines 179-194
•	A technical concern with the marker-gene analysis is that the authors are using merged reads (Lines 143-147) for which they predict ORFs and use blast to assign function.  Previously the authors stated that the merged reads range from 150-290bp (Lines 110-111).  The authors do not indicate the read lengths used for sequencing, this should be added to the relevant supplementary information, or if all are using the same read lengths (2x150?), this can be added to the text.  Even if these are all using the same read-lengths, please test that the distribution of merged read lengths does not differ significantly across sample groups.  I am concerned that a skewed distribution toward shorter merged read lengths would result in the underprediction/failure to detect marker genes, particularly longer ones.  If your method already controls for this, please add a statement explaining how.

•	Even once this is resolved, I am confused by the reporting of the marker gene analysis.  It is unclear why the authors used LEfSE to identify significant differences in gene 'abundance' among sites (Line 149), yet Figure 1 employs and presents results from pairwise Wilcoxon rank sum tests.  I understand that in the second case the authors are combining multiple genes together to simplify the presentation; however in the case of citrate lyase, Figure 1 indicates that the two comparisons are significant by this combined test, but the LEfSE results for aclA and aclB report "not_significant" for both (TB layers, ML/TB epi) comparisons.  Please explain this discrepancy.  Do your conclusions vary based on which results you are reporting? Additionally, please add to Supplemental Data S2 a notation so that it is clear which markers are combined to generate the categories on the y-axis in Figure 1.  Should you choose to display only the LEfSE results, a form similar to that used in Figure 2 might be better showing the actual genes and their groupings.

2) Overall, the remaining descriptions of the metabolic pathways identified within the MAGs were good but could benefit from additional interpretation.  There were several paragraphs where it felt that the authors were describing at length the results, which are nicely displayed in Figure 2, but I was left wondering 'why do I care?'  Please place these discussions in the environmental context.  A particular example is the paragraph on the cytochrome oxidases. To summarize, my recommendation is to revisit these paragraphs and confirm the conclusions were strongly stated and the linkages to differing chemistries across sites made effectively.
Additional comments: Additional points to address:
In 'How Representative are the MAGs?' (Lines 195-223) and 'Using MAGs to track population abundances over time' (Lines 469-491):
•	The authors make a qualitative comparison at the phylum level across the datasets and methods indicating that the assignments "largely" agree.  What is the point to this analysis?  If anything this analysis underscores the bias associated with all methods of describing microbial community composition and undermines the implicit assumption across the manuscript that the MAGs are representative of the community, and therefore are accountable for the observed differences in marker genes. Please summarize why this comparison matters and how it supports the conclusions reached in this manuscript.  Please explain explicitly at the end of this paragraph what the main takeaway from this analysis is and how it is related to the rest of the observations.  Or remove.
•	If the authors would like to rely on this similarity to ascribe the observed marker-gene abundances to the MAGs with similar pathways, this could be better achieved by making a direct comparison of the merged reads (marker genes) identified with those encoded in the MAGs in order to quantify which are actually associated with the assembled MAGs and what proportion remained unassembled.  I believe this is what the authors are trying to do with the final analysis of the paper, linking nitrogenase marker genes to the dominant cyanobacterial MAG, however in that analysis it is also unclear what exactly is being measured and compared.  It seems that the authors are correlating the abundances of nitrogenase genes with the abundances of the Cyanobacteria MAG.  Why then not make a direct comparison of sequences?  Lines 485-6, state "it is possible that other diazotrophic populations were more abundant, or that the nitrogenase subunits were derived from populations that did not assemble into MAGs."  The authors should have the data available to actually test this statement.  Please explain if there is some reason why this analysis could not be done, otherwise I think it would strengthen these observations if it is possible to directly attribute the nitrogenase counts to the MAGs rather than making the indirect link presented in Figure 4.

•	Line 213 - "...consistent with a higher likelihood of recovering MAGs from the most abundant populations in the community."  Please provide either a reference or analysis to support this statement or remove it.  It has been demonstrated that high-abundance populations can in fact be underrepresented in assembly (PMID 26033198 and others) due to technical issues with assembling strain variants.  Rather, it is often the opposite, where low abundance, low-diversity populations are the most amenable to assembly from metagenomic data.  Finally as the authors also noticed, some taxa are not identified via 16S rRNA amplicon sequencing despite their representation in the metagenome. (for example PMID 26083755 and others)

•	Line 221 - 16S rRNA amplicon sequencing not just "16S" please.

•	Lines 244-246.  Why does the observed diversity suggest horizontal gene transfer?  Are these taxa not typically associated with nitrogen fixation? Is this diversity particularly surprising for some reason?  Does analysis of the MAGs suggest these particular genes have been horizontally transferred?

•	Line 326:  "The co-occurrence of fixation pathways in these pathways in these populations are especially interesting given their relatively high abundance in their respective lakes."   Why is this especially interesting?  Please elaborate.

•	Line 328-336:  The discussion of the presence of rbcL in Chlorobium, is lacking some connections.  What is the genomic context of rbcL in non-Chlorobiales and in the Chlorobium isolates.  Is the context described for these new MAGs totally different from these other observations?

•	Line 344- "Unexpectedly, an Acidobacteria MAG from the Trout Bog epilimnion also contained genes suggesting aerobic anoyxgenic phototrophy."   And?  Why is this specifically called out - please explain why this is novel or interesting and worth the mention.

•	Lines 352-398:  Complex carbon degradation:
GH are necessary for complex-carbon degradation, but are also employed for structural purposes within an organism, this should be acknowledged, as the abundance and diversity of GH identified here are being used as a proxy for complex carbon degradation, and this may not be accurate.
In lines 338-391, the authors indicate that the relative numbers of GH identified may not be relevant, but then proceed to talk primarily about the most frequently identified GH families (lines 394-6; legend to Figure 3b).
Finally, the authors identify GH % values approaching 5%. This seems high (PMID 22536372, Figure 4). Both this study and that of He et al.  (presumably using similar methods) identified these high percentages.  If these are really accurate percentages, this seems like it would be a big deal and should be called out.  I wonder if there is some technical artifact related to assembly that might be inflating this value.  If so, I don't think that it changes the comparisons of these MAGs to each other, but to other genomes using different methods it might not be an appropriate comparison.  Please either a) acknowledge this large discrepancy and comment on its possible source (biological or technical) or b) show from the literature how this is not an unusually high value.  Regarding this analysis in Figure 3 B, C, D please add additional categories to the bar chart.  Surely there are others that might be biologically interesting to include here.  The large 'other' bar does not provide much information.

•	Lines 493-494.  These results have shown significant differences in marker gene abundances indicating POTENTIAL differences in microbial nutrient cycling.  Please adjust.

Other comments on Supplementary files:

S1- Please check that the data for the following samples is correctly entered, as these lines differ in format from the other samples.  HZIF, HZHX

S2 - Please add titles indicating which data is shown in panels A and B so that this is clear even without the legend.  What is y-axis showing in panel B?  This is unclear.

S6 - This table is incredibly sparse and not especially useful in this format.  Please consider melting in R and retaining only those comparisons with non-zero ANI values.  As a reduced 3-column file, this would be sortable and more readily usable for people who will make use of this excellent MAG dataset in the future.


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: FRESHWATER CARBON AND NUTRIENT CYCLES REVEALED THROUGH RECONSTRUCTED POPULATION GENOMES
Review round: 1
Reviewer: 2

Output:
Basic reporting: While the English was clear and professional, I found the writing style at times repetitive. For example, three out of four paragraphs in the ‘Nitrogen cycling’ section begin with ‘To identify…’. I also think that sections can be shortened (e.g. ‘Community Functional Marker Gene Analysis’, l. 178-194 which seems largely redundant with the methods section).
The introduction is rather short. It should be extended to include hypotheses about the data and to expand on the motivation of the present study. For example, the manuscript could be set up as a study of methodology (how does marker gene analysis perform compared to MAGs) or of comparing lakes with different environmental conditions (Mendota vs. Trout Bog) or in terms of the time series. I found that many of the results presented were not clearly connected to the introduction, making it difficult for me to evaluate their importance.
Results and Discussion are merged into one section, which does, as far as I know, not conform to PeerJ structural standards. I think it would help the manuscript if results and discussion would be teased apart because it would allow the authors to highlight main results and discuss their relevance in detail more.
The figures were clear, relevant and of high quality.
Experimental design: The research is original and within the scope of the journal. As mentioned above, I found the research question not to be clearly defined. The research was conducted to a high technical and ethical standard and the methods are described well. However, I would encourage the author to explain the experimental design in more detail (e.g. how many samples per year in the time series).
Validity of the findings: The data are robust and the analysis statistically sound. However, I think overall it could be presented in less detail, allowing more room for fewer results to be discussed in detail and linked to hypotheses. The conclusions are a bit muddy, because a clear research question is lacking.
Additional comments: The authors investigate 141 metagenomics datasets sampled as a time series from two lakes utilizing both functional marker gene and metagenomic binning approaches. As expected, the results obtained from this impressive dataset are complex and not easily summarized. However, I do feel that the presented manuscript fell a bit short in aiding the reader to understand these complexities and evaluate their importance in light of the existing literature. Specifically, I found that the manuscript in its present form lacked hypotheses about the work presented. As a consequence, the presented results come across a bit like a long list of findings, but their relevance is hard to gage.

-	Title: The title is a bit vague. What is connected exactly and what is the nature of these connections.
-	L. 44-50: The flow of this paragraph is a bit strange.
-	L. 115: Do primers for the different V regions have comparative biases? Otherwise, it might be questionable to compare 16S taxonomies between lakes.
-	L. 121-124: I don’t understand the sentence. Please clarify.
-	L. 132: Please clarify how many datasets were pooled? Based on which criteria?
-	L. 155: The sentence is redundant with respect to the previous paragraphs.
-	L. 180-194: This paragraph should be significantly shortened or incorporated into the methods section.
-	L. 208ff.: This part should likely be moved to the methods section.
-	L. 226: Vague. What specific differences and why?
-	L. 233: I don’t think O2 is the explanation here, lots of organisms have the ability to fix N2 in the presence of oxygen, including cyanos.
-	L. 246: Interesting. But could it not also have evolved independently? Is there support for HGT (e.g. nitrogen fixation genes are very conserved between different taxa).
-	L. 273-285: I don’t understand the point of this paragraph. I recommend removing it.
-	In general in the results/Discussion sections: background and motivation to study a specific pathway is given after a result is introduced. Maybe expand on the background info in the introduction.
-	L. 271: The hypothesis is not mentioned before.
-	L. 328-336: This paragraph adds little to the results. I recommend removing.
-	A table summarizing the results for functional marker genes and MAGs might be useful.
-	L. 351-361: This section is about glycoside hydrolases.  So I’d remove the opening paragraph, as it’s not helpful. And change the title to reflect what this section is about.
-	L. 469: This is the first time this is mentioned. Set the result up in the introduction with background information and a hypothesis.


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: TECHNOLOGY-ASSISTED WHITE CANE: EVALUATION AND FUTURE DIRECTIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a review of literature for rather small time frame of 2010 to the present.  It is not clear why the authors chose such a limited amount of time since there is a lot of literature dating back to the 1970s which is just as relevant today as what has been cited.  As one example the laser cane which was actually mass produced and introduced to the market in the 1970's is relevant to this topic.  Another is the Sonic Guide also produced in the 1970s.  Of course there are other technologies from the 1980s and 90s going forward.  The Pathfinder as one example.  The reason these products are relevant is because they covered the same approach to technology as what has been completed in the past 10 years.  While certainly sensors have become more advanced in information acquisition,  processing speed, they are smaller and less expensive, the underlying fundamentals of what these technologies do and don't do has not changed for the past 40 years.  So if the authors want to argue that there are changes to the underlying fundamentals the case has not been made.
Experimental design: This is a literature review.
Validity of the findings: I question the limited time frame of the literature review.  Perhaps there is a strong rationale.  It should be stated.
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: TECHNOLOGY-ASSISTED WHITE CANE: EVALUATION AND FUTURE DIRECTIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a generally well-written review MS aimed at obtaining an inventory of electronic enhancements of the white cane reported over the period 2010 – 2017, and at suggesting which of these (and further) enhancements will maximize the utility of the enhanced cane as a travel, orientation, and obstacle detection and recognition aid for blind users.  This is certainly a worthwhile endeavor in view of the multiple approaches to this problem that have been attempted, the wide range of technology available, and mostly the challenge it poses:  The white cane, for all its simplicity, provides the well-trained blind person with a wealth of information about his/her immediate surroundings and the obstacles that may be present.
In my opinion, the authors have met the basic requirements of a PeerJ MS, even if I have a number of suggestions for changes that may improve organization, clarity, and wording.  The references, figures, and tables are clear and provide the raw data on which their text presentation and interpretation are based.
Experimental design: The authors argue, convincingly, that the topic of their study is important and will help provide direction to the continued development of electronic travel and orientation aids.  Their search of the existing literature appears to have been thorough, and although they could have provided slightly more detail about the selection process used to winnow 573 papers down to 32, the remaining ones appear to provide a broad spectrum of tools used to supplement the white can, or in some case replace it with a virtual tool.
The authors have done a very nice job of analyzing the different aspects of the "enhanced canes" and presenting  the results in tables that are relatively easy to understand, although the layout could be cleaned up a little, and more detail in the table captions would be helpful.
Validity of the findings: To the extent that the validity of the data from a literature review can be  ascertained, it appears that the authors have done a very credible job representing all important aspects of the papers they included, and in my opinion this is what makes the MS very helpful.  The only thing that is somewhat disappointing is that there is not much effort on the part of the authors to discuss, cost, weight, power, ergonomics, etc., of the different approaches, even if those are not always explicitly mentioned in the original articles, and subject to change, and don't take these aspects into account in their conclusions (other than by saying that many of the papers did not provide this type of information explicitly).  I would encourage the authors to devote more attention to these aspects in the Discussion.
Additional comments: While the MS is generally well organized, improvements are possible on a number of points:
1)	The Results section start with a paragraph that, except for the last sentence should replace the opening paragraph of the Introduction, which is much less engaging.  Move lines 154-166 to replace
2)	What is missing from the Introduction (or Discussion), in my opinion, is a better explanation how the white cane provides echo location and "shorelining" (following a wall or pavement edge) capabilities as well as obstacle detection, and that any auditory output from an ETA should not interfere with the auditory aspects of echo location, traffic noise, and other sound beacons commonly used by cane travelers..
3)	Lines 354-381 (and possibly also some of the points in lines 333-351) of the Conclusion section should be moved to a General Discussion, and should be separated into points that were brought up by previous authors and are adopted by the current authors, and points that the previous authors  did not make but that the current authors have distilled from integrating these 32 papers.
4)	Repeatedly the authors cite privacy concerns as a potential downside of using auditory output, but with sound played into an earbud, hearing aid or cochlear implant this is not really a concern.  What is a concern, however, is the potential danger associated with loss of environmental auditory information, so the authors may want to mention safety as an important consideration in favor of tactile output.
5)	The presentation in lines 175 – 324 should refer to specific columns in Table 2 (just like it refers to specific panels in Fig. 3), and refrain from putting in too many citations, as these can be easily seen in the table
6)	In many places the authors speak of "extending the cane" when they really mean "enhancing the utility of the cane" or "supplementing the functionality of the cane."
7)	There are many other instances of awkward wording that should be addressed, I strongly suggest that the authorss have an experienced writer of scientific English comb through the MS after it has been revised.


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: TECHNOLOGY-ASSISTED WHITE CANE: EVALUATION AND FUTURE DIRECTIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: My comments are contained in the section for the editor
Experimental design: My comments are contained in the section for the editor
Validity of the findings: My comments are contained in the section for the editor
Additional comments: My comments are contained in the section for the editor


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: TECHNOLOGY-ASSISTED WHITE CANE: EVALUATION AND FUTURE DIRECTIONS
Review round: 2
Reviewer: 2

Output:
Basic reporting: It is good to see that the authors, at the request of reviewer  #1, expanded their search criteria to older publications and added 4 references pertaining to older technological cane solutions that are still being used.
Experimental design: The authors have carefully addressed the concerns of the reviewers and further strengthened the MS.
Validity of the findings: authors have carefully addressed the concerns of the reviewers.
Additional comments: Revision:
The authors have done a commendable  job in revising the MS along the lines of both reviewers.  I do have a few additional comments, mostly regarding issues that arose out of the text revisions, but these should be relatively simple to address.

Remaining/new  comments:
It is possible that the authors are not familiar with some of the terms in my previous review, and the same may be true for readers of the paper.  A good example of this is the following sentence: "…detect 47 obstacles in the range of 1.2 meters at ground level using echolocation and shore-lining"  This indicates that the authors consider echolocation and shorelining as methods of obstacle detection, whereas in reality these are 3 distinct techniques in cane use.  There are 3 basic uses of the white cane:
1)	Obstacle detection, i.e., as cane users walk along, they sweep the cane back and forth in front of them, to avoid running into obstacles or tripping over surface ridges, and to detect steps, curbs, and dropoffs.
2)	Shorelining, i.e. , following a border, which can be the wall of a building or corridor, the edge of the pavement, or pavement markings created especially to guide blind people in public places, such as bus stops, crosswalks,  shopping centers, etc.  The user still sweeps, but touches the border on every sweep to keep the distance from the border constant as (s)he goes forward.
3)	Echolocation, i.e., tapping the cane during the sweeping motion to hear the echo of a nearby wall, parked car, or any other sound-reflecting surface, and thus gain information about the surroundings, without actually having to touch them.
Adding these 3 concepts to the Introduction will resolve the misconception that seems to be present in Line 48, and also make it clearer in the presentation of different systems and reviews whether each technological innovation does or does not form an extension/enhancement of each of these basic uses.  My guess is that very few ETAs will assist with echolocation, but some may be better suited for shorelining than others.  Most importantly, in discussing various technologies, the author should ask the question whether the technology could interfere with any of the 3 functions mentioned above, as this would limit rather than enhance the original cane.

Wording comments:
The MS uses many abbreviations and some of them are not introduced in the text (e.g., the term "Cm"); even  if they are, this happens at varying points.  It would be good to have a list of abbreviations in one location; the caption of Figure 3 would be a good place for this, since they are all used in that figure.


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: TECHNOLOGY-ASSISTED WHITE CANE: EVALUATION AND FUTURE DIRECTIONS
Review round: 3
Reviewer: 1

Output:
Basic reporting: The authors have done a commendable job  to address the previous comments by reviewers and editor.  It is interesting to see that in a number of instances they have pointed out the importance of retaining the echolocation capabilities of the physical cane in designing ETAs, but have not done the same for the shorelining capabilities.  I am pointing out examples below.
Experimental design: No remarks
Validity of the findings: There are a few specific areas where I would like to see a broader interpretation that covers shorelining in addition to echolocation.
1) Line 238-245: I would argue that the shorelining and echolocation techniques don't need ETAs: The physical contact during shorelining and the classification of sounds during echolocation work just fine, so the ETA should not interfere with those, but augment the ability to detect obstacles, and possibly extend the range beyond the physical length of the cane.
2) Line 325-327: Similarly, this statement should be changed to indicate whether any of the ETA devices leave the echolocation and shorelining capabilities intact, and which studies have explicitly included these capabilities in their evaluation.
3) Line 356-364: This is a good argument, but it can be extended to shorelining:  It may be difficult to design an ETA that can detect differences in surface texture (such as grass along a walkway or different types of pavement) as well as physical limits, from edges just 1 cm high to walls or fences.
4) Line 539-543: Here again shorelining should be mentioned in addition to echolocation.

The major change I would like to see is in the functionality described and categorized in the tables: Rather than talking about Navigation (N) (which includes shorelining, echolocation and obstacle avoidance, but not much else that I can think of),  I would introduce echolocation (E) and Shorelining (S) as specific types of functionality, and evaluate all ETAs explicitly on those, so each cell in the functionality colummn of Table 2 gets an E+ or E- and an S+ or S- to indicate whether this device has those capabilities.
Finally, in Table 3 under technologies Audition (rather than "Audible") should be split into use of external sounds (e.g., listening to traffic patterns and footsteps) and use of sounds created by the device (echolocation); there also should  be a technology called Touch, and its role should be listed as obstacle/boundary detection but also texture detection
Additional comments: After everything else has been completed it would be good to get an outside reader with excellent command of English to proofread the MS one more time:  There are not many errors, but they are annoying and can easily be found and fixed by an attentive reader.


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

Input:
Title: THE RELATIONSHIP BETWEEN CARBON AND NITROGEN METABOLISM IN CUCUMBER LEAVES ACCLIMATED TO SALT STRESS
Review round: 1
Reviewer: 1

Output:
Basic reporting: See general comments
Experimental design: See general comments
Validity of the findings: See general comments
Additional comments: The manuscript by Naliwajski and  Skłodowska entitled “Relationship between carbon and nitrogen metabolism in cucumber leaves acclimated to salt stress” uses different biochemical approaches to study how cucumber plants response to salinity stress.
The manuscript is well designed and the biochemical methods are appropriated. I have only some minor suggestions. They are as follows:
1. Introduction section. The presence of NADP-ICDH, G6PDH and 6PGDH has been also described into plant peroxisomes. See Corpas and Barroso (2018) Peroxisomal plant metabolism - an update on nitric oxide, Ca2+ and the NADPH recycling network. J Cell Sci. 131(2). pii: jcs202978 and cited references. This could be mentioned considering the oxidative metabolism of this subcellular organelle which are involved in the mechanism of oxidative stress.
2. Describe with more details the used methods because it will be very useful to the potential readers. For example include concentration of substrate, used wavelength in the spectrophotometric assays, etc.
3. Result section Describe the panels of the figures in same order they appear in the figures
4. On the Y axis, write period instead comma in the Figs. 2A, 2B, 3C and 4.
5. Figs 5 and 6 show the phenotype of cucumber plants they should be moved to first and second figures with an appropriated description.
6. In the different figures showing enzymatic activities, on the Y axis, write the specific activity with the products or substrate used to its assay. For example write “nmol NADPH min-1 mg-1 protein” for the different NADP-dehydrogenases. This will allow to compare the present data with that already reported in other plant species.
7. Authors could explain why cucumber plants have been used in this study. Maybe because cucumber is a model to study salinity or for its agronomical relevance…
8. L336 Write ascorbate-glutathione cycle instead “Foyer-Halliwell-Asada cycle”.
9. L343-344. Very recently it has been described that Pro is not a ROS scavenger. See Signorelli et al. (2016) In vivo and in vitro approaches demonstrate proline is not directly involved in the protection against superoxide, nitric oxide, nitrogen dioxide and peroxynitrite. Functional Plant Biology 43(9) 870-879. Therefore, this statement must be deleted.
L315-316. On the other hand, similar consideration must be taken about sucrose which “is an effective ROS scavenger”. It is possible to speculate but this should be corroborated as experimental level. Therefore, this should be mentioned.
10. In the figures, the label to identify each column should be bigger it is difficult to distinguish. Moreover, it is suggested to change the lines inside of the columns, maybe color could be an alternative.
11. L72. Write matrix instead “marix”
12. Add a list of abbreviation


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

Input:
Title: THE RELATIONSHIP BETWEEN CARBON AND NITROGEN METABOLISM IN CUCUMBER LEAVES ACCLIMATED TO SALT STRESS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language should be improved to ensure that an international audience can clearly understand your text. Authors did not pay any attention to punctuation, grammar mistakes and spelling. I recommend to check the text by native English speaker.

Literature in many cases is quite old. I recommend to check and find more latest papers to base on.

The references mentioned below does not exist in the text:
'Bonnefont-Rousslot D. 2002. Glucose and reactive oxygen species. Current Opinion in Clinical Nutrition & Metabolic Care 5(5):561-568 zastąpić Krugerem'

'Bowsher CG, Hucklesby DP, Emes MJ. 1989. Nitrite reduction and carbohydrate metabolism in plastids purified from roots of Pisum sativum L. Planta 177(3):359-366.'

'Crawford NM, Arst HNJ. 1993. The molecular genetics of nitrate assimilation in fungi and plants. Annual Review of Genetics 27:115-146.'

'70. Mena-Petite A. 2009. The oxidative stress caused by salinity in two barley cultivars is 71. mitigated by elevated CO2. Physiologia Plantarum 135:29-42' - this reference is divided into two lines.

'Singh S, Srivastava PK. 2014. Purification and characterization of glucose-6-phosphate dehydrogenase from pigeon pea (Cajanus cajan) seeds. Advances in Enzyme Research 2(4):134-149'

Line 318 there is 'van Dongen' instread of 'Van Dongen'
Reference No. 23 Dal Santo is in reference, but in the text is Del Santo, please correct.
Reference No. 27 deSousa - between de and Sousa should be a space.
Reference No. 73 In the text there is Podgórska, but in reference is Podgorska, please correct.
Experimental design: There is no clear aim of the study. Authors emphasized that they did some experiments, but they did not mentioned what is the point of their research.

Why authors described time after stress treatment as 24th or 72nd. It's unnecessary. I recommend write 24 or 72 h after treatment as they did in figures description. I would try to unify the background of pictures.
Validity of the findings: Authors did grate job performing analysis, however I am not convinced why they used ANOVA and LSD test for such small group of repeats. Four repeats are too small to use parametric tests. Besides, unlike the Bonferroni, Tukey, Dunnett and Holm methods, Fisher's LSD does not correct for multiple comparisons. I recommend to analyze the data via one of the nonparametric tests.
Additional comments: No comment.


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

Input:
Title: THE RELATIONSHIP BETWEEN CARBON AND NITROGEN METABOLISM IN CUCUMBER LEAVES ACCLIMATED TO SALT STRESS
Review round: 1
Reviewer: 3

Output:
Basic reporting: -The ms is well written in general, although some basic proof-reading is needed as minor grammar and syntax errors can be found throughout (as early as in the abstract section - see showed high degree of... accumulation was found).
- The introduction is too long and needs some trimming. Contrarily, I would like to see some sort of information on the process of acclimation.
- Article structure is fine, although it would be nice to include a metabolic pathway including the enzymes examined herein to get a better idea of components covered.
Experimental design: - No queries in regard with experimental design. One point though: on what basis was the acclimation protocol followed? Was this based on prior literature? If not, did the authors carry out preliminary experiments?
Validity of the findings: - Data presented is robust and appears to be statistically sound. Conclusions discussed are well-stated; however, the Discussion section is too long and should be more concise.
Additional comments: - Authors quantify proline, glucose and sucrose. On that basis, they could also carry out enzymatic activity assays of proline biosynthetic enzymes (such as P5CR and P5CS) which would be interesting, while the same goes for suc-glu-related enzymes such as invertases. Would the authors care to comment in regard?
- Furthermore, I was a bit surprised to see that damage phenotypes were limited to loss of turgor. What about other salinity-related symptoms such as yellowing and/or leaf curling?


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

Input:
Title: THE RELATIONSHIP BETWEEN CARBON AND NITROGEN METABOLISM IN CUCUMBER LEAVES ACCLIMATED TO SALT STRESS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have included my previous suggestions, although I make some additional minor recommendations. They are as follows:
- L120   Write “16,552” instead “16552”
-L182  Write isocitrate instead isicitrate
-Throughout the text write “h” instead “hours”. For example L273
-In figure 2 and check again the units for specific activity because it is missing min-1. For example, write “nmol NADH min-1 mg-1 protein”  instead “nmol NADH mg-1 protein”. Check also in Fig. 4. Write period instead comma in the Y axis
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: THE RELATIONSHIP BETWEEN CARBON AND NITROGEN METABOLISM IN CUCUMBER LEAVES ACCLIMATED TO SALT STRESS
Review round: 2
Reviewer: 2

Output:
Basic reporting: As this is a revised version, any comments are shown in the General Comments to the Authors section.
Experimental design: As this is a revised version, any comments are shown in the General Comments to the Authors section.
Validity of the findings: As this is a revised version, any comments are shown in the General Comments to the Authors section.
Additional comments: I am generally satisfied with the way the authors handled my comments. However, I do not fully follow the response received in regard with my suggestion to carry out enzymatic activity assays for proline and sugar metabolism components. I can understand (and accept) the comment about sugar metabolism being currently examined as part of ongoing work. However, if I understood correctly, the authors did carry out p5CS and PDH activity assays but choose not to include these (although in the response letter they strangely mention that the results will be included in the prepared manuscript). I am confused: will they or won't they include these? If not, why? Doing so would greatly support the story being told as we would get biochemical evidence for proline regulation under the current experimental setup.


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

Input:
Title: A DIRECT APPROACH TO ESTIMATING FALSE DISCOVERY RATES CONDITIONAL ON COVARIATES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Please see the report attached.
Experimental design: Please see the report attached.
Validity of the findings: Please see the report attached.
Additional comments: Please see the report attached.


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

Input:
Title: A DIRECT APPROACH TO ESTIMATING FALSE DISCOVERY RATES CONDITIONAL ON COVARIATES
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors present a framework for estimating the false discovery rate conditionally on covariates, when the p-values are independent of these under the null hypothesis. In the analysis of large scale datasets, this is an important, challenging and potentially valuable task. The paper is well-written, well-motivated, and technically sound.

The underlying theme of this paper could be split into two parts: First, the authors propose an estimator of the proportion of null hypotheses conditionally on covariates. Second, they use the estimator to modify the standard Benjamini-Hochberg procedure. We remark on both aspects:

A. Estimation of $\pi_0(X_i)$:
---------------------------
The first part, i.e., estimation of $\pi_0(X_i)$ is, in our opinion, the selling point of this paper. The authors phrase the task of $\pi_0(X_i)$ estimation as a regression task. This key observation opens up many opportunities; in this paper the authors explore the use of linear and logistic regression potentially in conjunction with regression splines. However, their idea also enables the use of machine learning methods (say random forests, boosting, neural networks) to estimate $\pi_0(X_i)$, for example, if the covariates are complicated (say sequences or images) and high-dimensional. This is not mentioned explicitly in the paper, and we believe it would be worth mentioning.

Furthermore, the authors emphasize the importance of estimating $\pi_0(X_i)$ for tasks not directly related to down-stream multiple testing. For example, in the discussion they attribute the conservative behaviour in the right panel of Fig. 1 to publication bias. It would be interesting if this could be discussed in more detail.

Some missing references for this section include: the SABHA procedure [1], which also uses the thresholded p-values to estimate $\pi_0(X_i)$ but employs a maximum likelihood approach + convex optimization instead; AdaPT [2], which uses EM and logistic regression to estimate $\pi_0(X_i)$; and for categorical covariates, as in supplement S2.2., the GBH [3] procedure, which uses a standard $\pi_0$ estimator within each level.

It could also be interesting to see the following: How does averaging all the $\hat{\pi}_0(X_i)$ perform compared to $\hat{\pi_0}$, if we are just interested in estimating the global $\pi_0$?

B. Downstream multiple testing with FDR control:
----------------------------------------------
Another large part of this paper is concerned with modifying the BH procedure to account for $\pi_0(X_i)$ estimation. This is achieved by multiplying the adjusted p-values by the corresponding conditional $\pi_0$ estimate. We feel that this part of the paper is not as well motivated and could potentially be drastically deemphasized or even removed, similarly to an older version of this manuscript [4].

The main caveats of this section are as follows: The proposed scheme of modifying BH is essentially the same as that proposed in the SABHA procedure [1]. Second, as mentioned in [2] and [5], this scheme is inadmissible even under oracle knowledge of $\pi_0(X_i)$. Instead one should use a weighted BH scheme. One choice would be to use weighted BH with weights equal to $(1-\pi_0(X_i))/\pi_0(X_i)/(1-\pi_{0,\text{global}})$. This is the scheme proposed for categorical covariates in the GBH [3] procedure, and it leads to power increase both by upweighting the right hypotheses and by being adaptive (alpha-exhaustive). It would be important to see how such a scheme performs compared to the method presented here; we think it would further illustrate why task A. is so important. A further option would be to also use weights proportional to $(1-\pi_0(X_i))/\pi_0(X_i)$, but normalized to average to 1. Then the procedure would no longer be adaptive, but it could also be used with the cross-weighting scheme in [5] and would automatically enjoy finite sample FDR control guarantees.

Minor remarks:
----------------
* After Eqn. (1): "Namely the expected fraction": Conditional on at least making one rejections?

* $\theta_i = 1$ when null is a bit confusing and non-standard notation, maybe change it to $\theta_i = 0$.

* Page 5 typo "In section S3 we provide theoretical results for this estimator in Section S2 of the suppl. materials"

* Why not try the model with the cubic spline for Scenario 1 as well?

* It would be nice to see simulations under the global null as well.

* In the discussion it is mentioned that the method of Scott (2015) often does not control FDR. This was also mentioned/shown in [6]

* Proof of Supplement S3: Some parentheses missing after "then we can combine them as follows"

This review was prepared by Nikos Ignatiadis together with Wolfgang Huber.

References:
------------

[1] Li, Ang, and Rina Foygel Barber. "Multiple testing with the structure adaptive Benjamini-Hochberg algorithm." arXiv preprint arXiv:1606.07926 (2016).

[2] Lei, Lihua, and William Fithian. "AdaPT: an interactive procedure for multiple testing with side information." Journal of the Royal Statistical Society: Series B (Statistical Methodology) (2018).

[3] Hu, James X., Hongyu Zhao, and Harrison H. Zhou. "False discovery rate control with groups." Journal of the American Statistical Association 105.491 (2010): 1215-1227.

[4] Boca, Simina M., and Jeffrey T. Leek. "A regression framework for the proportion of true null hypotheses." bioRxiv (2015): 035675.

[5] Ignatiadis, Nikolaos, and Wolfgang Huber. "Covariate-powered weighted multiple testing." arXiv preprint arXiv:1701.05179 (2018).

[6] Ignatiadis, Nikolaos, et al. "Data-driven hypothesis weighting increases detection power in genome-scale multiple testing." Nature Methods 13.7 (2016): 577.


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

Input:
Title: A DIRECT APPROACH TO ESTIMATING FALSE DISCOVERY RATES CONDITIONAL ON COVARIATES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: I am satisfied with the revision and would recommend it 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: A NEW PHYLOGENETIC ANALYSIS OF PHYTOSAURIA (ARCHOSAURIA: PSEUDOSUCHIA) WITH THE APPLICATION OF CONTINUOUS AND GEOMETRIC MORPHOMETRIC CHARACTER CODING
Review round: 1
Reviewer: 1

Output:
Basic reporting: It takes the reader a bit of work to figure out the specific compositions of the datasets under comparison. It might be helpful to dedicate a section that explains clearly the ways that continuous, discrete, and geometric data are combined and compared. I realize that the information is all in the paper-- this would just help when readers are trying to track down what is meant by a 'DC' vs 'DM' comparison, for instance.

As the authors are probably aware, there exists a burgeoning literature dealing with more statistically modern approaches to the analysis of morphological phylogeneties covering all of the data sources explored in this manuscript (discrete, continuous/geometric, and stratigraphic). In light of this, the exclusive focus on parsimony methods in this paper strikes as odd. To be clear, I wouldn't suggest that the authors re-analyze their data under newer methods, but the lack of awareness in the manuscript of these developments is striking. In particular, I was struck by the authors' neglect of recent development in probabilistic phylogenetic analyses of discrete (Wright and Hillis 2014, PLoS One), continuous (Parins-Fukuchi 2018, Syst. Biol.), geometric morphometric (Parins-Fukuchi 2018, BioRxiv), and stratigraphic (Stadler et al. 2017, Arxiv) data in their otherwise extremely thorough review of existing methods. As a full disclaimer, I don't generally feel good about recommending citation of my own work, but I do honestly feel that a brief review of all four of these previous studies would be appropriate given the depth with which the authors describe relevant parsimony approaches. While the approaches used by the authors in their study are sufficient for their own questions, a broader awareness of modern methods in the manuscript would be helpful in framing the relevance of this study as these data types are applied in future studies that use updated approaches.

Here are the citations:

Stadler, Tanja, et al. "The fossilized birth-death model for the analysis of stratigraphic range data under different speciation concepts." arXiv preprint arXiv:1706.10106 (2017).

Parins-Fukuchi, Caroline. "Use of Continuous Traits Can Improve Morphological Phylogenetics." Systematic biology (2017).

Parins-Fukuchi, Caroline. "Bayesian and likelihood placement of fossils on phylogenies from quantitative morphometric data." bioRxiv (2018): 275446.

Wright, April M., and David M. Hillis. "Bayesian analysis using a simple likelihood model outperforms parsimony for estimation of phylogeny from discrete morphological data." PLoS One 9.10 (2014): e109210.
Experimental design: This study is very thorough. The authors have clearly thought and planned very carefully, and are very clear in describing each step. There are a few aspects that confuse me, however. Most notably, I'm left feeling slightly puzzled regarding the choice of methods and the general statistical mindset employed by the authors. Although thorough, the deep exploration of parsimony methods, and heavy reliance on frequentist statistics can feel arcane. For instance, the sentence in line 854: "However, the agreement subtrees suggest that the amount of overlap between these hypotheses is still greater than would be expected to occur by chance" comes across as old fashioned-- do we ever expect phylogenetic hypotheses from different datasets to overlap only due to random chance? I might suggest reconsidering the reliance on this type of reasoning.

As I note in the general comments, I wouldn't suggest that the authors need to reanalyze their data using more modern methods-- the thoroughness of their parsimony analyses result in more than enough clarity to address their questions, which may or may not even be benefited by alternative methods. But some tweaking of the presentation of the logic in the manuscript might make things feel less esoteric and pigeonholed in the fading cladistic and frequentist mindsets.

Aside from the comments above, I do have two specific questions regarding the methods used:

1) I see no mention of the bootstrap as a measure of node support. I would acknowledge the bootstrap to be flawed in some respects, but it is the standard in phylogenetics, and readily interpreted by biologists of most backgrounds. The authors apparently prefer to use Bremer supports, but since this manuscript will be published in an outlet intended for a general biological audience rather than Cladistics, I think it would be really helpful to switch the support measures to bootstraps, or at least describe Bremer support clearly, along with a justification for its' use over the bootstrap.

2) I enjoyed the authors' examination of the stratigraphic fit across topologies. But since the stratigraphic fit is used by the authors as an independent comparison of the reliability of different topologies, I am left wondering why they didn't perform any simple stratocladistic analyses? They hint at a dissection of the overall stratigraphic correlation for each topology, and potentially poor support yielded by particular subclades. In lieu of a full stratocladistic optimization (which I realize is challenging given the present state of available tools), it could be really interesting to compare patterns in stratigraphic parsimony debt incurred by each of the conflicting topologies. This should be achievable given available tools, and would mesh well with the cladistic focus of the manuscript.

Despite the length of these comments, I do not intend them as barriers to the publication of this study.  More generally, I found the goals and design of the study to be very clearly stated, and thoroughly and competently addressed by the analyses. I feel that the issues that I outline above could improve the reception and impact of the study among a more general audience, but at its core, this study is very well done, and most certainly worthy of publication and citation.
Validity of the findings: As I write above, this manuscript leaves me feeling confident in the the validity and thoroughness of the authors' results. My only concern in this area stems from the fact that the authors pour so much information in the results and discussion that the conclusion gets a bit buried. I would appreciate a less equivocating suggestion by the authors over their preferred resolution of the groups-- I know that they prefer the 'D' and 'DC' trees, but which aspects are most clearly resolved in these topologies? And how does the confidence that they recover in the relationships improve over previous studies, specifically? Finally, are the GM trees completely unsalvageable? Or can other insights potentially be gleaned from their use?
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: A NEW PHYLOGENETIC ANALYSIS OF PHYTOSAURIA (ARCHOSAURIA: PSEUDOSUCHIA) WITH THE APPLICATION OF CONTINUOUS AND GEOMETRIC MORPHOMETRIC CHARACTER CODING
Review round: 1
Reviewer: 2

Output:
Basic reporting: Manuscript is well organized and clearly written. Hardly any typographic or grammatical errors. A very clean manuscript.
Experimental design: The methods are well described in this manuscript.
Validity of the findings: I have made comments on the annotated versions of the main text and the main supplement text. I think there needs to be a little more discussion where the results affect things such as the use of isolated squamosals for biostratigraphy and the unstable taxonomy of the Leptosuchus/Smilosuchus group.
Additional comments: Very nice study although pretty lengthy which makes it hard to follow in places. Make sure you emphasize which treatment is best recommended for moving forward in future analyses of the Phytosauria. This is done at the very end of the conclusions, but it would be beneficial to have it emphasized in the abstract and maybe at the end of the Introduction section as well.

I've also corrected a bit of the stratigraphic and locality data in the supplemental files. Also note that the catalogue number for RLG 11/07-3 is PEFO 38340.


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

Input:
Title: A NEW PHYLOGENETIC ANALYSIS OF PHYTOSAURIA (ARCHOSAURIA: PSEUDOSUCHIA) WITH THE APPLICATION OF CONTINUOUS AND GEOMETRIC MORPHOMETRIC CHARACTER CODING
Review round: 1
Reviewer: 3

Output:
Basic reporting: Jones & Butler present a remarkable, solid, and well-written study on the phylogenetic relationships among phytosaurs, the most common group of reptiles in Late Triassic deposits. The study is an original piece of work that fits well in the scope of PeerJ and adheres to the structure of the journal.

I fully endorse publication in PeerJ, but I recommend three items of improvement below to enhance the clarity of the study and to complement its goals.
Experimental design: There is a number of points in which this study stands out positively compared to previous analyses of phytosaurs (and, as a matter of fact, in comparison with many other cladistics studies of extinct archosauriforms):
The analysis is the most comprehensive with respect to taxon sampling to date.
I am particular impressed by the revised and thoroughly justified combined database presented in the supplemental material. It is safe to predict that the revised data matrix will form the base upon which researcher will rely and expand for future phylogenetic analyses of the group for years to come.
The study introduces novel types of data (continuous, geometric morphometric – the latter to my knowledge never employed in phylogenetic analyses of extinct vertebrates), and the significance and utility for phylogenetic analyses.

The authors use rigorously a number of tests (e.g., decay indices, stratigraphic congruence, implied weighting) to evaluate their findings and the validity of phylogenetic hypotheses. Employing such a variety of independent tests is extraordinary and certainly not standard procedure in our field.

The methodical part is exemplary, and in combination with the supplemental data, the analysis is fully reproducible.

The purpose of the study is fully explained in the introductory section.
Validity of the findings: I suggest three points in which the manuscript can and should be improved:

1.) In the sections “High-level taxonomy” and “low-level taxonomy”, you present an exhaustive discussion and evaluation of previous hypotheses on phytosaur relationships in the light of their data. The conclusions are well-reasoned and supported by character evaluations and various tree statistics.
However, although the conclusions on the taxonomy or the phylogenetic position of single taxa are clearly stated at the end of the paragraphs of each topic discussed, the main conclusions are difficult to retrieve for the reader without filing through half of the paper. I feel the reader would benefit from a paragraph in the “conclusions” section summarizing the more important findings, in particular those at variance with the current consensus (like the position of Protome and Rutiodon, non-monophyly of Leptosuchus and Smilosuchus, Nicrosaurus as non-mystriosuchine leptosuchomorph. or the synonymy of Redondasaurus and Machaeroprosopus), including those conclusions which are outlined in the abstract.

2.) You include a number of specimens as separate OTUs in your analysis, with the explicit intention to test their phylogenetic affinities (supplemental material, lines 1094, 1118, 1131, 1165, 1178). However, for a number of these specimens the results of the tests are not even mentioned in the text, despite the potential significance of the individuals. These include MB.R. 2747 – the only substantial remains of a Rhaetian phytosaur from Europe, PEFO 34852 – the oldest phytosaur showing three sacral vertebrae, and NMMNHS-P 4256 and P 31094 – potential Redondasaurus that if substantiated would extend the range of the taxon and question its usefulness as index fossil for the Apachean biozone (Martz & Parker 2017).
I recommend a brief discussion of these specimens in appropriate positions within the subsection “Low-level taxonomy”

3.) Sections “Previously Referred Specimens” throughout the supplemental material:

I got confused with these sections. At first I assumed that you agree with these referrals, and the sections represent a ’list of specimens’ or what you include in the hypodigm of that species, until I realized that this is actually rarely the case. However, as a reader I am much more interested to know which specimens you include in that taxon (aka, which specimens match your modified diagnosis) rather than which specimens have been erroneously or without substantiation referred to the taxon in the past. The latter should be included and discussed in a comprehensive systematic review, but I do not think it is absolutely necessary in the database for a phylogenetic analysis. As such, the list of previously referred specimens is also tor a number of taxa far from incomplete (e.g., Spielmann & Lucas 2012 referred a multitude of specimens to Redondasaurus gregorii).
I suggest to change these paragraphs to ‘Referred Specimens’ and include previous assignments that you find correct (I do appreciate that you give credit to previous workers here) and those specimens you refer to that taxon for the first time. Thus, this paragraph represents your hypothesis of the hypodigm of the taxon (which need not to be comprehensive, and of course includes also the ‘holotype’ and ‘specimen(s) used for scoring’, both of which should remain separate sections). Any information you deem important (for example, Camp’s concepts of adamanensis, lithodendrorum, and gregorii, or the exclusion of AMNH 10644 from Mystriosuchus planirostris) could go in the ‘comment’ sections.

I include two sections with some minor points or additional comments for the main text and the supplementary file; the authors are welcome to include the information if so desired:

1. Manuscript: Detailed comments

Line 284: Nicrosaurus kapffi

Lines 1192-1193: “However, the fact that Rutiodon consistently forms the sister group to Angistorhinus makes the decision of whether or not to synonymize the genera entirely arbitrary” – In addition, your analysis supports an important implication from Hungerbuehler & Sues’ hypothesis with respect to character evolution: The depression of the supratemporal fenestrae, for long regarded as the hallmark of ‘derived’ phytosaurs (Rutiodon + Leptosuchomorpha) must have actually evolved independently twice in phytosaurs.

Line 1570: “Hungerbühler et al. (2013) were unable to recover ‘Redondasaurus’ gregorii and  ‘Redondasaurus’ bermani as a monophyletic group” – This is most likely because the taxa were scored after the holotypes only, which resulted in a high amount of missing data for several species included.

Lines 1617-1629 “Thickened orbital margin” – Spielmann & Lucas 2012 do not describe or expand on this character, but I assumed from their fig. 49 the character refers to the blunt (rather than sharp) and particularly the elevatation of the rims of the circumorbital bones (rather than the postorbital only) in at least some of the specimens figured. This interpretation would explain the comparison with Coburgosuchus, in which at least the dorsal rim is elevated (but not thickened).

Lines 1663-1664 “…these taxa are always monophyletic to the exclusion of species of Machaeroprosopus.” Correct, but what is with NMMNH 31094 which has been referred to Redondasaurus, and shares at least three potential synapomorphies with species of that genus (supplemental data, lines 1140-1142)

2. Supplemental Material: Detailed comments

Line 152: ‘Paleorhinus’. magnoculus

Lines 588-590: Nicrosaurus kapffi has, to my knowledge, no formally designated lectotype (nor do I think there is a need for a lectotype designation) – these specimens form the syntype series.

Line 647: “Machaeroprosopus” zunii holotype. In support of the authors’ conclusion about the validity of the species, I might add from personal inspection that the braincase almost certainly comes from a smaller individual than the postcranium, and it appears to be less derived than a basal leptosuchomorph phytosaur – thus even the holotype seems to be a chimaera.

Line 686-687: From Stocker’s description and figures (I do not know the specimen first-hand), these prongs are in the same position as two exoccipital/supraoccipital projections identified as proatlantes facets by Hungerbuehler et al. (2013: 298, fig. 24) for Machaeroprosopus lottorum. Provided these are indeed homologous structures, such prongs are present in numerous skulls referable to Machaeroprosopus and Redondasaurus (and perhaps more taxa, I have not conducted a comprehensive survey). I doubt that the exoccipital prongs are autapomorphic for Protome.

Line 713-714; “found not to be the type species of Machaeroprosopus.” - Reference needed

Line 782: As you include TTU-P 11423, the taxon also occurs in Texas.

Line 795-796: ‘tubular’, literally tube-like, implies a slender, hollow and round snout - I would not describe a low sharp-crested/triangular snout as tubular

Line 849-850: Omit the wording ‘and tubular’ in character 3.), otherwise it duplicates character 4.). As mentioned above, the word tubular aka “tube-like” implies a round, or here semi-circular, cross-section.

Line 1015; “2074.000, 2149.002, 2149.003, 2150.000” are GPIT specimens

Line 1098: “Chinle Group” – Dockum Group, to be consistent

Line 1723: “sausage-shaped” - narrow and curved? Please explain

Line 1738: “sub-temporal shelf” – please explain/describe this structure. Is this the dorsally facing facet of the jugal in character 83[1]?

Line 1750: How is this ratio calculated?

Line 1759: How is this ratio calculated?

Line 1774: Extends as ridge forward for… ? Would this be what has been called a narial crest?

Line 1776: …..of the quadrate? If so, the character makes no sense to me – the condylar area of the quadrate has two condyles, and I do not understand the character states. Please explain.

Line 1780: length of symphysis to post-symphysial mandibular length, meaning [0] short [1] long? Please clarify
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: A NEW PHYLOGENETIC ANALYSIS OF PHYTOSAURIA (ARCHOSAURIA: PSEUDOSUCHIA) WITH THE APPLICATION OF CONTINUOUS AND GEOMETRIC MORPHOMETRIC CHARACTER CODING
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This resubmission looks great. The authors adequately addressed all of my concerns over what was already a very strong paper in the revision and rebuttal documents. I am looking forward to seeing the final published version!


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

Input:
Title: A NEW PHYLOGENETIC ANALYSIS OF PHYTOSAURIA (ARCHOSAURIA: PSEUDOSUCHIA) WITH THE APPLICATION OF CONTINUOUS AND GEOMETRIC MORPHOMETRIC CHARACTER CODING
Review round: 2
Reviewer: 2

Output:
Basic reporting: This manuscript is very clean, without noticeable typographic errors. In my first review I was critical of the presence of a section in the Introduction discussing "Weaknesses" of previous work. I am happy to see that this section has been removed and for the reasons listed by the authors in their rebuttal letter.  The literature review is exhaustive and thorough and the article is well-organized. The results section is pretty dense as the section requires explaining and comparing four different trees with each other and past work. Breaking up some of the longer paragraphs and citing figures more often in the sections may help with this. In the tree choice section please iterate what the tree abbreviations are one more time for readers who struggle with remembering all of the abbreviations.

The Discussion section is also very dense with long paragraphs and sentences. For example lines 1094 to 1099 are all a single sentence. Where possible breaking apart long paragraphs will help the reader navigate through this section.
Experimental design: This is a very large exercise in phylogenetic database exploration using a group with a notoriously tortuous taxonomic history. In my previous review I criticized the manuscript for not suggesting which of the four analyses should be used by phytosaur workers to move forward. This is especially important as the authors are suggesting revisions to phylogenetic definitions of various clades. I'm glad to see the authors have added a suggestion of using the DC tree for future analyses, but also note that this recommendation is tentative. Just be aware that this makes your work difficult to use in future analyses, and instead relegates it to dataset exploration and a critique of past methodologies and scorings. As also stated because it utilizes continuous characters the DC tree is only useable with TNT and not other software packages such as PAUP*. It will be up to future workers to provide a final evaluation of the utility of the work presented here.
Validity of the findings: The use of exploratory methods creates a situation where a lot of data are generated that are not entirely consistent with each other. The conclusions are well formulated and stated, but again I hope because of the complexity of the methods and discussion that the results are useable for future analyses, especially since new phylogenetic definitions are created based on these various results.This is hard to evaluate without actually trying to use the information in future work. Overall, however, I feel that the questions asked and answered by this study are sound and useful. I believe the authors have accomplished their stated goals and will generate further discussion of phytosaur taxonomy and phylogenetic relationships.

The Supplemental materials are improved.
Additional comments: I recommend the following changes:

All uses of e.g. should be followed with a comma. This is standard for non-U.K. based journals.

Watch the prefixes for specimen numbers. I noted some differences in the conventions used. I specifically saw differences in ANHM specimens.

Line 1278: If you aren't sure that the observed character state in PEFO 31218 has not been affected by preservation, you should score it as unknown.

Line 1443: Note that the holotype specimen of M. mccauleyi is missing the end of the snout.

Any database exploration study is going to be critical of past authors. Please review and ensure that any criticisms are fair and necessary and toned down to not cause offense with any colleagues. This version is much better that the previous regarding this, but it does not hurt to review one more time to ensure you aren't offending any colleagues with your treatment of their work. Everyone expects to be criticized, and its acceptable if done in a fair manner.


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: SYMMETRY BREAKING OF THE CELLULAR LOBES CLOSELY RELATES TO PHYLOGENETIC STRUCTURE WITHIN GREEN MICROALGAE OF THE MICRASTERIAS LINEAGE (ZYGNEMATOPHYCEAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Good figures, attention to detail, Methods and Results descriptive and clear, thoughtful discussion

Language style issues: more clarity needed (specialized subject with a lot of jargon), lengthy writing style (Intro, 2nd half of discussion)
Experimental design: no issues raised
Validity of the findings: the findings and conclusions appear to be robust
Additional comments: SUMMARY
This interesting manuscript attempts to integrate morphological and molecular data in a model genus of desmids, Micrasterias. I am not an expert on this group or kind of analysis so I cannot fully evaluate the precedent evidence and the statistical methods. However, the questions are laid out and answered clearly and the figures are well presented. The analyses appear to be conclusive, the findings novel and the discussion is thoughtful, all making the manuscript worth publishing.

One thing that I was puzzled about was the use of maximum parsimony analysis for sequences: this was described in Methods but omitted in Results (or the authors did not make it clear which phylogeny they followed; I assumed ML). I wonder if MP analysis of molecular data is at all meaningful at this point (we know sequences evolve differently).

The other area in need of improvement is the writing style. The English is good but plentiful jargon makes the work difficult to understand for anyone outside the specific field. In large part, the technical terms cannot be avoided but, unfortunately, the difficulty in reading this particular text is compounded by lengthy writing, repetition and the presence of marginally relevant information. The authors should see a great space for improvement here for their own benefit. Many sentences could be more simple and direct: Introduction could be shorter by about 1/3 in size (if not more), the second half of discussion could be more focused on the important.

WRITING
Take the first paragraph of the Introduction as an example:

lines 64-65: "which is a pattern that is quite different from that of" ... "unlike". But note that you do not need this sentence.

lines 65-66: ", which often have ..") ... this is certainly not needed

lines 66-69: "Given this apparent relationship among cellular morphologies and species-level phylogenetic differentiation, it is surprising that individual major infrageneric clades .."	... "In contrast, clades of species as resolved by molecular phylogenies .." (and delete "of their member species")

To an outsider the language in the very first paragraph is rather difficult to understand. Apart from the cumbersome phrasing, I got most confused by "taxa" on line 64 (you really mean "species", I assume, but why not say "individuals" or "cells" instead?) and the fact that infrageneric clades of species are defined by the sequence phylogeny. The latter fact is important but not intuitively understood. Many similar objections to style hold for the remainder of the manuscript - aim for brevity and clarity wherever possible.

70-78: lengthy/repetitive with the first paragraph and within itself

79-84: "Neither X, emphasized in traditional taxonomy (REFs), nor Y characteristics correlate with the molecular phylogeny of Micrasterias (REFs)"

86: name the "entire lineage"

90-98: too long and some unneeded emphasis ("remarkable"). Could be replaced one or two simple sentences

99-103: "in essence", "in addition": these are parasitic words and you could write clearer. Consider this: "Micrasterias is bilaterally symmetric around multiple axes running through surface incisions; these separate the cell into cellular halves (semmicells), semmicels into lateral lobes and lateral lobes into successively branched lobules (Fig. 1A)."

105-through the end of Introduction: this contained areas with quite a lot of relevant information and the specific questions towards the end are really helpful, however, I also found it quite repetitive, unfocused (irrelevant detail) and difficult to read through (language, long sentences): the authors should cut here and simplify to be understood by readers outside their field.

Methods: could be more concise again but descriptive and generally well done

388-89: "the amounts of positional asymmetry were considerably decreased" .. awkward

404: your use of "conversely" confuses me: how does it reverse the previous statement in this case (and elsewhere)? It is not a synonym of "in contrast" if that was your intention - same issue elsewhere.

Consider similar edits across the whole manuscript

I could not find the legend for Fig. S1.


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: SYMMETRY BREAKING OF THE CELLULAR LOBES CLOSELY RELATES TO PHYLOGENETIC STRUCTURE WITHIN GREEN MICROALGAE OF THE MICRASTERIAS LINEAGE (ZYGNEMATOPHYCEAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Review:
This manuscript focuses on an interesting topic that deals with the usefulness and power of geometric morphometrics for symmetry/asymmetry studies of unicellular algae in a phylogenetic context. In general, the manuscript is quite short, appropriately illustrated and straightforward to read. The hypotheses are clearly presented and the methods seem appropriate for the study.
I suggest adding a short definition of symmetry breaking and explain what it means and why it is relevant in this precise context. To my knowledge, the idea of symmetry-breaking (in the context of biological symmetry, which is quite distinct from the general use of the term in Physics) is devoted to the cellular processes underlying the appearance of asymmetry.

The Procrustes ANOVAs yield significant results for the main factor “individual” and the interaction term “individualxposition” for most of species. Except for the interaction term “individualxposition” in “Micrasterias denticulata, 7LM, upper sublobe” and the main factor “individual” in “Micrasterias brachyptera, 7LM, two sublobes”. In the former could it be that measurement error was rather large compared to this asymmetry measure and in the latter, could it be that this asymmetry is indeed expected to be larger than variation among individuals in this species? Maybe one comment could be added on these results.

*Main text
- line 261: “compared in two analyses (Fig. 1A).” – simply add “Fig. 1A”
- lines 316-317: Indicate which regressions were performed
- line 531: “extraordinary”
- line 537: “actually”
- line 580: “for this kind of environmental stress” – remove “the”

*Figure 2
- Somehow all images are not at the same resolution and appear as quite low resolution. Especially F), J), O) , and T).

In my opinion, the manuscript is suitable for publication after these minor corrections have been addressed.


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

Input:
Title: SYMMETRY BREAKING OF THE CELLULAR LOBES CLOSELY RELATES TO PHYLOGENETIC STRUCTURE WITHIN GREEN MICROALGAE OF THE MICRASTERIAS LINEAGE (ZYGNEMATOPHYCEAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: The present ms Neustupa & Stastsny touches a very interesting topic, mapping the phylogeny of the model alga Micrasterias to morphological traits. By a detailed analysis of symmetry breaking the authors gain important new insights. The ms is overall very well written, rich in sophisticated details and statistical treatment of the observations and is therefore well worth publishing in PeerJ.
Experimental design: In earlier work (Škaloud et al. 2011) traits like the branching pattern, complexity, cell length and even biogeographic origin were mapped on phylogenetic tree, giving important information on evolutionary trends in this interesting organism. I am wondering only about the selection of strains, why these particular species have been chosen; please mention this more precisely in the introduction; and if the rational was only what was easily accessible and growing well, this is also OK.
Validity of the findings: According to Škaloud et al. 2011 H clade Micrasterias are represented in the present study only by M. americana. It has been shown, that M. americana has very similar morphological characteristics than A-clade Micrasteris. This might be true for the here investigated lateral lobes; but to my understanding the H-clade Micrasterias show a very distinct common feature, several lobules (particularly of the polar lobe) show in addition to their 2-D architecture a 3-D. So there is not only the numbers and symmetry of the lobules in a two-dimensional view, but also the 3-D architecture well worth to be considered. This is certainly beyond the scope of the present ms, but could at least be discussed. In his post-hum article on Micrasterias, Lionel G. Harrison (Harrison, LG, 2011 Micrasterias, and computing patterning along with growth. Chapter 5, pp. 77-109. In Harrison LG, The shaping of Life. The Generation of Biological Pattern, Cambridge University Press).
This is particularly obvious in the (non-European) M. muricata where even a 3-D branching of the lateral lobes is evident (e.g. Holzinger 2000, Nova Hedwigia 70, 275-288). In future studies particularly these H-clade Micrasterias with their 3D structure should be investigated; for the present study it is enough to include this aspect in the discussion (l. 471-477) Think the ms benefits when these aspects are mentioned and the references included.
It is clear that this ms deals primarily with a mathematical and statistically sound analysis of the asymmetry between the lobules. Some aspects how this shape is realized are mentioned in the introduction, while others are missing. The membrane recognition theory of the late Prof. Kiermayer is certainly the basis for deposition of primary cell wall material, but then the quality of the wall itself is crucial for further development. I would certainly suggest to mention the important works of Vannerum et al. (2010 J. Phycol. 46, 839–845, 2011 BMC Plant Biol. 11:128), showing the responsibility of expansins in this process.
Additional comments: Other than that, this ms is smart, interesting to read, in parts certainly only for a special audience. It contributes nicely to our understanding of evolutionary trends, when investigating a genus that has so delicate morphological features.


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: IN SILICO ANALYSES FOR POTENTIAL KEY GENES ASSOCIATED WITH GASTRIC CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: No Comment
Experimental design: No Comment
Validity of the findings: No Comment
Additional comments: The manuscript entitled ‘In silico analyses for potential key genes associated with gastric cancer’ by Dr. Weidong Zhao and coworkers was on understanding hub genes involved in gastric cancer (GC) metastasis.  The aim was to identify the hub genes and investigate the underlying molecular mechanisms of GC. The authors have done an integrated analysis and identified differentially expressed genes (DEGs) by using three gene expression profiles between human GC and normal gastric tissue samples from GEO database. Secondly, Gene Ontology (GO) functional enrichment analysis and Kyoto Encyclopedia of Genes and Genomes (KEGG) pathway enrichment analysis were further conducted to analyze the major biological functions of co-modulated DEGs. Then, constructed protein–protein interaction (PPI) network to identify hub genes related to GC by STRING and Cytoscape. The overall survival analyses of the hub genes were validated via “Gastric cancer” database on the online Kaplan-Meier platform. A total of 85 overlapped upregulated genes and 44 downregulated genes were identified. The study suggests that COL1A1, MMP2, FN1, TIMP1, SPARC, COL4A1, and ITGA5 may be potential biomarkers and therapeutic targets for GC. The authors can also investigate some studies reported by Chakraborty and coworkers Ann Gastroenterol. 2014; 27(3): 231–236. The authors have made a good attempt to understand the hub genes involved in the GC metastasis,  present paper is valuable in publishing in PeerJ.


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

Input:
Title: IN SILICO ANALYSES FOR POTENTIAL KEY GENES ASSOCIATED WITH GASTRIC CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: Authors have focused on genes involved in gastric cancer using bioinformatic approaches. Understating the role of key genes that can be potentially used as biomarkers/therapeutic agents is of key significance for cancer diagnostics and potential treatment. Authors have used professional scientific language in the manuscript, however they need to improve phrase construction and need to re check manuscript for spacing and other grammatical errors. Overall the manuscript was very well written only needing some revisions in particular areas. Using GEO, STRING, and cytospace software’s authors have narrowed down the identification of specific genes that might play an important role in gastric cancer. Major weakness in the manuscript is lack of in-depth analysis of the genes identified and the work is similar to several groups with some exceptions in terms of particular hub genes. However the findings are very important and future biochemical research on these particular genes are needed to understand gastric cancer. Conclusion and future directions need to be explained more clearly as identifying genes is one step but what can be done biochemically or clinically is a major step forward.
Experimental design: Authors have chosen bioinformatic approaches for this particular study.
The approaches used for identification of genes using bioinformatic tools are not novel and several other groups have also used similar techniques to identify key genes of potentiality. For examples Li et al used similar approaches based on microarray datasets and found potential hub genes in gastric cancer. Interestingly, the mRNA microarray that they have used are quite different from this particular study. Below is the reference for this particular group.
Li, T., Gao, X., Han, L., Yu, J., & Li, H. (2018). Identification of hub genes with prognostic values in gastric cancer by bioinformatics analysis. World journal of surgical oncology, 16(1), 114.
Authors mentioned in line 109 that they have used 3 microarrays after careful review. On what bases are these particular gene expression profiles were used was not explained very well.
Authors approaches for screening for DEG’s and further use of KEGG and GO analysis is logical in order to get more insight into the function of identified DEG’s. PPI network construction using STRING, hub gene identification, and survival analysis using Kaplan-Meier plotter was very well explained by the authors.
Validity of the findings: Bioinformatic approaches are of significant importance in the field of oncology and identification of potential biomarkers. Findings from the experiments are valid and have great potentiality for future results. However, results and discussion section needs to be elaborated. Figures and tables are represented appropriately showing their results but figure legends can be elaborated. Authors clearly shown the upregulation of key genes when analyzed by PPI network construction.  Authors are encouraged to highlight the 7 hub genes from figure 4 with the connection. If possible they can take out some unnecessary nodes and highlight the key interaction. Please consider this as a minor comments. Kaplan-Meier plot results show the prognostic values of identified hub genes.
Authors are encouraged to provide some information on the future research with the identified genes. In future, it is interesting to use protein structure prediction methods and design biochemical experiments on the identified genes. By predicting the tertiary structure, site directed mutagenesis can be performed on the particular genes.
Authors mentioned in Line 265, “Further molecular biological experiments will be performed to confirm the effect of CXCL8 and THBS1 on GC. Chen et al, 2018 group have performed studies on CXCL8 and they have shown that CXCL1 and CXCL8 participate in proliferation, migration process via specific binding with CXCR2. Below is the citation of the article.
Xuyan Chen, Ruifang Jin, Renpin Chen, Zhiming Huang: Complementary action of CXCL1 and CXCL8 in pathogenesis of gastric carcinoma. Int J Clin Exp Pathol 2018;11(2):1036-1045. Int J Clin Exp Pathol 2018;11(2):1036-1045.
THBS1 studies were also done by Huang et al (2017) group showing that THBS1 is upregulated by FGF7/FGFR2 growth factors and promotes and knockdown of THBS1 decreased cell invasion and migration. However these studies are don invitro and further characterization studies are needed.
Additional comments: Authors have intended to identify key hub genes that might be playing an important role in progression of gastric cancer. The manuscript is well written with professional language but need to check for errors and sentence fragmentation.
The methodology and approaches to screen and then narrowing down the results to identify the hub genes is appreciable. However this particular research and study is very similar to some other groups with some different results based on the microarrays that are screened. Interestingly.
Authors need to give an elaborate discussion on how they can use these hub genes as potential biomarkers. They need to address the disadvantages of this approaches as there can be some kind of over interpretation based on the findings. Nevertheless this kind of work is important as it can be used for prediction of gastric cancer progression and  the for future research for verification of the DEG’s in gastric 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: IN SILICO ANALYSES FOR POTENTIAL KEY GENES ASSOCIATED WITH GASTRIC CANCER
Review round: 1
Reviewer: 3

Output:
Basic reporting: I recommend the authors to carefully edit the manuscript to avoid typos and avoid errors like spacing between sentences.

All the literature references should be formatted to same style by incorporating volume numbers and initial and final page numbers.

The Figures 3 and 6 should be made more visible by increasing the font size
Experimental design: The manuscript in the present format is addressing a valid point and the research work is in scope of the journal. The authors have described the methods and experiments ver well.
Validity of the findings: The manuscript have novelty and impact in the field
Additional comments: The manuscript entitled "In silico analyses for potential key genes associated with
gastric cancer: describes  about understanding hub genes involved in gastric cancer (GC) metastasis that could lead to effective approaches to diagnose and treat cancer.

The manuscript is well written and the conclusions made by the authors are in line with their objectives and experiments.
Hence I recommend accepting the manuscript after a minor revision.

Minor comments:
1. I recommend the authors to carefully edit the manuscript to avoid typos and avoid errors like spacing between sentences.

2. All the literature references should be formatted to same style by incorporating volume numbers and initial and final page numbers.

3. The Figures 3 and 6 should be made more visible by increasing the font size

4. The conclusions of the paper should be rewritten to highlight al points in the paper. The highlights of the paper could be emphasized in 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: DOPAMINE AND EYE MOVEMENT CONTROL IN PARKINSON’S DISEASE: DEFICITS IN COROLLARY DISCHARGE SIGNALS?
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper examines how patients at an early stage of Parkinson disease can update their spatial representations during eye movements, and whether this ability correlates with the integrity of the dopaminergic system. Although the topic is interesting, the paper has important limitation.
Experimental design: My main concern is about the analysis model. I am not convinced that this is the best model to apply to these data. In many cases, the data from patients and controls are very similar. I do not understand how the differences come from.
Validity of the findings: Another major issue is about the sample and the use of medications. The sample is small and very heterogeneous, subjects were on different medications and one person did not take any medication. This is an important limitation of the study because the different drugs may have different effects in the eye movements control.
Additional comments: Comments (in order of reading):
The introduction is exhaustive, however it is too long. I would suggest to the Authors to shorten it focusing on main issues, especially section 1.2.
Line 121: “CD signals…” please define before using abbreviations.
Line 186-187: this is an unusual way to indicate the sample. Please write “8 women, 6 men and 7 women, 7 men”. Also, please provide age information for both sexes separately.
Line 203: medication. 11 subjects did not take medications on the morning of the test, 2 patients took medications and one patients did not have medication prescription. How can the Authors be sure that interrupting the medication on the same day of recording is sufficient for avoiding a pharmacological effect? In addition, some subject did not interrupt medication, so there could be mixed effects in the results. Also, patients were on different medications. Again, some effect could be due to the specific drug.
Line 217: “We assumed that…” Did the Authors mean, “hypothesized”?
Line 245: please write “round white target stimuli with the dimension of 0.6⁰ were presented on a black background. Please specify the target intensity.
Line 246: Please specify the type of eye tracker and the sampling rate of recordings.
Line 252: 16 degrees is a big distance for making an accurate saccade. Did the Authors consider this aspect?
Section 2.2 needs to be shorten and rewritten. There are quite a few repetitions. For example, there are two paragraphs explaining the double saccade task used in this and previous studies (see lines 227 and 254). These two sections can be merged for a better reading.
Line 260: were the trials randomly presented?
Line 293: the time between the scanning and the test is very long and variable, a lot of changes could happen between 8 and 29 months. Did the Authors consider this aspect?
Line 324: as I said before, I am not convinced that this is the best model to analyze these data. Indeed, this model has no standardize way to calculate the significance level. The use of the confidence interval could result difficult for general readers.
Line 346: Authors should write a detailed legend of table 1. It is not clear to me which data the Authors are reporting here, is it a questionnaire? Is it a recorded data? How was it measured? Please describe.
Line 360: please write a detailed legend for figure 2. What does the horizontal line mean? What does the dots mean? Which data are represented by the bar?
Line 368: from the data presented in figure 3 it looks like patients and controls have a similar oculomotor behavior in response to the two task. Tables 2 and 3 show the errors made by PD patients, the authors should show the errors made by controls to demonstrate that the two groups differ.
Line 400: data from control participant are not shown in tables 2 and 3, or at least this is not explained anywhere. I strongly suggest the Authors to pay much more attention at the figures/tables explanation.
Line 426: which unit is represented in figure 4 x axes?
Line 441: “This suggests that the observed correlations represent true correlation with the integrity of the dopaminergic system…”. It is difficult to believe this statement because the subjects were on medications; furthermore, different medications. See also my previous comments.
Line 475-480: the Authors state that there is not a difference between PD patients and controls, however when “side” is taken into account the analysis model shows differences. I think that this is not the best way to analyze the data. The “side” should be inserted in the model as a factor.
Line 488-491: here the Authors state that the laterality is included in the model. This is very confusing (see previous comment). I suggest the Authors to pay much more attention to the description of the model.
Line 500: The Authors state that the β coefficient of the Ideal angle × UPDRS interaction is much smaller than the the β coefficient of the Ideal angle × DAT interaction, but the relative size of this effect is very similar due to the fact that the range of motor MDS-UPDRS scores is much higher than DAT values. The analysis should not work like that. Your model should tell you if there is an effect or if there is no effect, you cannot interpret the results according to the values of the data, this is wrong. If the scores are much higher than the DAT values and you do not rely the data to the result, your model could be wrong.
Line 507 and figure 8: see my previous comment; I am not convinced that this is correct.
Figures 7 and 8: what does the dashed lines mean? Is it the fitted effects from the model? Please describe.
At line 537 the Authors say “our results suggest that in addition to general impairments in making saccadic eye movements, the patients may also have deficits in monitoring their eye movements”, while at line 556 they say “The result may indicate that the deficit is not in the internal monitoring of movements”. To avoid misinterpretation, I would suggest to rewrite one of the two sentence or to better explain what the Authors mean with “internal”.
Line 574: See my previous comment about “internal”. It is better to avoid the use of “internal”, please be more specific. See also line 537 and 582.
Line 583: “…it also remains possible that the contrasting findings in schizophrenic patients and PD patients reflect different mechanisms”, this is obvious, please delete it or be more specific.