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: ALTERNATIVE REPRODUCTIVE STRATEGIES IN BLACK-WINGED TERRITORIAL MALES OF PARAPHLEBIA ZOE (ODONATA, THAUMATONEURIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English used is generally clear but should be improved for a general readership.  For example, in l. 38 I think the authors probably mean 'In contrast' rather than 'Nevertheless,' the word 'oscillated' is used when 'ranged' or 'varied' would be more idiomatic (e.g. l. 197), and 'associated to' is used but 'associated with' is correct (e.g. l. 39).  There are occasional problems with subject-verb agreement, e.g. ll. 226 and 311.

The cited literature gives sufficient context given for the research and is relevant, and the structure of the article is appropriate.

Although the table/figures are appropriate, more information should be provided about some of them in the legends for clarity's sake.  For example, in Table 1, giving the result in one-two sentences would be helpful (e.g. 'Spot size manipulation significantly affected only whether males were dominant or submissive, and only for Day 0 versus Day 1 and Day 0 versus Day 2.').  Some figures lack needed information.  For example, are the confidence intervals in Fig. 1 95% confidence intervals?  Also the word 'males' should be in that figure's legend.  Is the X-axis in Figure 2 in days?
Experimental design: The research is within the scope of the journal, and there are some good data in this paper addressing the behaviors of male color morphs.  However, the research questions and the author's approach to them are confusing.  For example, in ll. 76-80, the authors write 'The aim of our study is to determine whether dominant and submissive roles of BW males are condition-dependent [sic], in particular in relation to asymmetry and size of the wing pigmentation....To investigated [sic] that, we first, using mark-recapture methods, estimated survivorship rates and the effect of body size on survival of BW males (dominant and submissive0.  The problem here is that the methods do not address the putative question.  It is thus difficult to determine the authors' aims.

In addition, the methods are incomplete.  Examples of fundamental questions remaining:  Was this research conducted in a stream?  A pond?  How much area was covered?  How often were surveys conducted and at what times of day? Exactly what marks were used to identify individuals, and how did these marks not interfere with the spots/stripes on males' wings?

The research questions are clearly defined individually, but the links among them are not clear, and as noted above the methods do not always match the goals.  The authors would have a paper with greater clarity if it were more focused.
Validity of the findings: It is difficult to assess the validity of the findings without more detailed methods, but the analyses are generally appropriate.  More than three days of focal observations would have been very helpful and made the findings more convincing.

The authors might explain more fully in the introduction why they predict painting submissive males with larger black spots would change their behavior.
Additional comments: This is an interesting topic, and as you point out there are not many species with these kinds of polymorphisms that have been well studied. If you can re-organize your data, write the paper so that tests of your hypotheses are logical and clear, improve the flow, and clarify the methods, the manuscript would be much improved.


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: ALTERNATIVE REPRODUCTIVE STRATEGIES IN BLACK-WINGED TERRITORIAL MALES OF PARAPHLEBIA ZOE (ODONATA, THAUMATONEURIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well organized and structured and written in professional English.  However, it is confusing in part due to some critical typos and confusion between the types of male damselflies (BW and HW) that undermine a clear description/understanding of the experimental design.  The description of the wings of the males is not completely described, ignoring chromatic elements that may be very relevant to their potential as intraspecific signals.  In addition there are two studies that explore similar questions about a very similar damselfly that are not considered (Xu & Fincke, 2015; Schultz & Fincke, 2009).  They are very relevant to this study.  Figures and tables are OK but table S2 should not be in supplementary materials but should be included with the body of the text. Given the importance of conveying what the different morphs look like, photos of the damselflies and wing treatments would be better if they appeared with the text.
Experimental design: This species and the topic of alternative morphologies and reproductive strategies are very interesting and worth studying.  The experimental design is not clear due to several critical misprints and conflation of morpho-types (BW and HW) males.  There are three critical flaws in the study.  First, the alternative personalities of the territorial BW males, categorized as dominant or submissive, are not supported with quantitative measurements of the insects behavior such as number of aggressive pursuits or strikes or retreats as a percentage of opportunities for male-male interactions.  There are only descriptions of aggressiveness that could be challenged as subjective.  I can see no reason why the so-called submissive males should not be treated as satellites. Secondly, in the exploration of plasticity in the territorial roles of male damselflies by manipulating the wing spots, the authors apparently hypothesized that changing spot size would change the aggressiveness of the male.  It is unlikely that the insects have a sense of self, but rather their territorial status is determined by how rival males react to the wing treatments.  For example, does reducing the size of the spots of a dominant male result in more or prolonged challenges from other males.  Finally, as far as I can tell, the resource holding power of the males are assessed by their persistence in a territory.  That is OK when comparing existing physical parameters such as size and asymmetry or outcomes such as reproductive success, but it is a very indirect measure of the effect of intrasexual signals.  The actual behaviors of competing males needs to be observed.
Validity of the findings: The data comparing physical attributes and reproductive success of territorial and satellite males are valid and informative.  But the manipulative experiments testing the plasticity of the territorial roles and the significance are not valid so the results are inconclusive rather than negative. Perhaps the authors should drop this portion of the study from the manuscript, but that makes it less interesting.  In my opinion, they should follow their previous documentation of significant morphological differences between the BW and HW males, and pursue the exploration their alternative strategies and wing patterns.
Additional comments: Introduction

Reviewer's comments:  I am perplexed by the description and consideration of the wing spots on BW males.  Photographs of the species in the field indicate that the dark portions of the wing tips are iridescent blue in reflected light but may appear dark or black in diffuse or transmitted light.  Why is the wavelength of spots ignored given that the color may well be an important component of the visual signal?  The wing spots of BW males in P. zoe are remarkably similar to the wing patterns of Megaloprepus coerulatus in which males are also territorial.  Why do the authors ignore recent studies (Schultz & Fincke, 2009; Xu & Fincke, 2015) of the function and significance of wing patterns in this latter species which may be informative in understanding P. zoe? Xu & Fincke Xu (2015. Ultraviolet wing signal affects territorial contest outcome in a sexually dimorphic damselfly. Animal Behaviour 101:67-74) showed that territorial status of males was related to the size of the white spots, which may in turn be honest signals of fat reserves since the spots consist of extruded wax.  The potential significance of the white spots of the BW males of P. zoe was largely ignored in this manuscript.

Text pp. 65-72 "BW males that do not defend a territory have been previously found in P. zoe (Romo-Beltrán, Macías-Ordóñez & Córdoba-Aguilar, 2009), and are considered as satellite males. Our preliminary observations suggested that BW territorial males can behave as dominants, when their territory is close to the water or as submissive, when they occupy a territory away from the water, in a similar way as the behaviour described for D. obscura (Bañuelos Irusta & Araújo, 2007). Dominant BW males are highly territorial and highly aggressive against submissive (males), probably giving them resource advantages (Baker, 1983), and submissive males are less aggressive, usually avoiding confrontation with dominants, but nevertheless defend their territory against satellites."

Reviewer's comments: In trying to understand how dominant and submissive BW males were identified, I read the cited papers.  It is not clear to me how territorial but submissive BW males differ from satellite males as described in Romo-Beltran et al. (2009). The Bañuelos Irusta & Araújo (2007) study distinguished the males as territory holders or satellites, not as two types of territorial males with different degrees of aggressiveness.  I cannot find in this manuscript or in the previous studies of P. zoe any quantitative evidence for recognizing distinct categories of “personality” (dominant or submissive) or Resource Holding Power (RHP).

Text lines 95-97: "Based on previous studies with odonates that have found that more pigmented males have higher success (e.g. Alex Córdoba-Aguilar, 2002) we hypothesized that increasing the black-wing spot of the HW submissive males would change their status towards dominance, while increasing the black spot size of the BW males would not affect their role, because they are already dominant."

Reviewer's comments: Previous discussion above (lines 67-69) indicates that dominants and submissives are sub-categories of BW males.  The HW submissive males referred to in line 96 must be a misprint and would seem to refer to BW submissives, since HW males don’t have black spots to enlarge.

Text lines 98-102: "For the white spot there is no information about its function. So that, if we conceal the white spot, we could either expect that BW dominant males change their status to submissive if this spot is related to aggressiveness, or that they maintain the same dominance, if the spot is not related to dominance. In the case of submissive BW males, concealing their white spot would not affect their behaviour under the assumption that the white spot is not related to dominance."

Reviewer's comments: The logic here seems flawed.  The text repeatedly implies that manipulating the wing spots will change the behavior of the territorial (dominant or submissive) males, when what is relevant is how rival competitors perceive the altered males and lower or escalate their efforts in displacing the territory holder.  It appears that a change in status as a territorial holder was determined by whether the altered male was still on the territory.  This is only an indirect and imprecise measure of a change in territorial status as a function of the wing manipulation.  What is required is direct observation of contests between males and a determination of which male wins.

This is all the more confusing because of the existence of the HW males, some of which are territorial (Romo-Beltran et al. 2009).  I would have expected the authors to manipulate the wings of the HW males and record any change in territorial status and RHP versus the BW males.

Methods

Text lines 107-108: "Males and females were captured with an entomological net and marked with a black permanent pen."

Reviewer's comments: Marked how?  On wing?  If on the wing, how is it known that the markings don’t affect responses of conspecifics.

Text lines 109-113: "Male behavioural status was divided into two categories: territorial males (BW), defined as those individuals who stayed in the same place for more than two days and returned to the same perch site after participating in a fight in flight with a conspecific male, while individuals who did not meet this criterion were considered as non-territorial HW (satellite) males (Romo-Beltrán, Macías-Ordóñez & Córdoba-Aguilar, 2009)."

Reviewer's comments: Again confusing. Are HW males the same as satellite males. Wouldn’t HW males  be distinguished by wing morphology rather than behavior?  Misprint? BW instead of HW?

116-118 Submissive males were defined as those that perched inside a territory, but further away from the water and at a distance of 0.5-1 m from the dominant male, and were unlikely to engage in fights…..

Reviewer's comments: Why aren’t BW males that perch away from water regarded as satellites rather than submissive territory holders. How do you tell the difference. In Calopteryx, such males would be considered to be satellites since a territory contains a resource to be defended.  Returning to the same perch does not necessarily indicate territorial behavior.

And again, how was the likelihood to engage in fights quantified?

Text lines 171-175: "We conducted a manipulative experiment to test if wing spot size is related to the dominant/submissive roles. To this end, we manipulated black and white spots in four treatments: (i) painting over white and black spots without changing their size (control 1), (ii) un-manipulated males (control 2), (iii) erasing the white spot using black painting (EWS), (iv) increasing the black spot and moving the white spot maintaining its size (IBS) (Figure S2)."

Reviewer's comments: The logical first step is to determine if there are differences in the black and white  wing spots between BW dominants and BW submissives in the field.  The authors apparently did this, but did not describe the procedure in the methods.  The results appear in supplementary table S2 cited on line 241.  This data is too important to not include with the main body of the text.  It is an indirect test of the significance of the wing spots as intrasexual signals.

What media were used to paint over the spots?  This is important to report should other researchers wish to conduct a similar experiment.

Results

Reviewer's comments: The metrics comparing the morphology, survival rates, reproductive activity, and lifetime mating success are all solid and informative.  The results regarding the plasticity of dominant and recessive roles are flawed for the reasons outlined above.  The measurements/analysis of spot size for dominant and submissive BW males should be reported here.  The results of continued residency on territories by manipulated males are not a direct measure of RHP.

Discussion

Text lines 249-255: "Our results indicate that: i) BW males can behave as dominant or submissive: we found evidence for a positive effect of territory quality (measured as the number of males occupying the area over time) and lifespan on mating success, and that morph strategy and sex affected the probability of recapture, and larger individuals had higher survival. However, black wing spots asymmetry was not correlated with the reproductive strategy of HW males, and the experimental manipulation of the black wing spots did not affect male dominance. We will discuss these findings in relation to what is known in this species and other territorial animals."

Reviewer's comments: Differences in the behavior of so-called dominant and submissive are not quantified, but the potential reproductive consequences associated with the two putative behaviors is evident from the study.    It is perplexing to me why the authors perceive these apparent differences in aggressiveness as alternative reproductive strategies rather than conditional tactics.  The reproductive behaviors of the BW and HW males would seem to be alternative strategies and worthy of further pursuit.  It would be VERY interesting to see the effect of manipulating the wings of HW males.


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: POLLEN METABARCODING REVEALS BROAD AND SPECIES-SPECIFIC RESOURCE USE BY URBAN BEES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The language used if fairly clear throughout, though there are a few spelling mistakes that need to be checked.The introduction is reasonable but could use a little more nuance when setting the stage for global bee declines and the role that urban management can play in this overall picture. The layout and structure conforms to PeerJ standards (though see acknowledgements). The results presented are relevant to the hypotheses.

Title – ‘habitat’ use. Since you present data on use of different pollens by bees, the use of the word habitat is slightly perplexing to me. Surely ‘resource’ use would be more appropriate?

Introduction

L45-48. Use of ‘severe’ is quite strong. Most of the data for wild bee declines comes from bumble bees, and indeed you cite four bumble bee papers in this sentence, all focusing on North America and Europe. I would take more time to specify that you are talking about wild bees, since you later go on to present data on honey bees, and find additional citations to more broadly support wild bee and ‘other pollinator’ declines.

L57. The Baldock paper found higher species richness of wild bees in urban areas compared to rural areas, so this is a surprising citation. Overall, the principle that urban areas have lower species richness than rural areas is contested, with papers on both side of the argument.

L53-55. The topic of urbanisation comes out of the blue here. You have not introduced urbanisation as a factor that can or could cause bee decline. Perhaps a citation to explain that urbanisation is expanding – and is it expanding in the western world, the only area which your papers demonstrate bee declines have occurred?

L59-60. Check formatting.

L66. Significantly

L71. Carreck and Williams 1997 is a little out of date perhaps

L73. Most of the differences in community visitation in these studies stems from the constituent wildflowers chosen. Many bee species have narrow ecological niches, and hence will respond differently to different seed mixes as they may or may not provide their preferred forage plants. When you write that “will help to ensure that utility for pollinators is maximised” this is highly dependent on what your desired outcome is – e.g. helping bumble bees or solitary bees for example. I would make your wording a little more precise – do you want to build a species specific picture of sown resource utilisation in urban areas, since this seems to be the knowledge gap as currently written? If so, specify this.

L89-91. This destructive/non-destructive concept would benefit from some introduction

Acknowledgements should not be used to report funding, that information will appear in a separate Funding Statement on the published paper, see guidelines.
Experimental design: I do not have sufficient experience with the metabarcoding technique to assess this part of the paper.

Methods

L99 total cover or relative cover?

L100-101. Were bees observed only or also netted? If observations, were bees placed into groups, e.g. small bee, bumble bee, honey bee, and so on? Also, it is not quite clear, did you have 3 10-minute counts at each quadrat (total 90 minutes) or a single 10-minute count at each quadrat (total 30 minutes)?

L102. How long was this collection period?

L117. 30 1/s, is this a rate, and how long were they shaken for?

L125. Check date format against journal standards
Validity of the findings: Results

L231. I’m not sure why you report an R2 since a permanova is only saying whether the communities are different. How can you have an explanatory factor?
There was no mention of PERMANOVA or NMDS analysis in the methods. When looking at the NMDS plot, you have three dots for each site – I assume this is one for each quadrat? This is not in the methods, and strictly speaking samples should be pooled per site (since data was collected in the same place on the same day) otherwise you have pseudoreplication (subsampling from the same population) and hence you can’t actually do NMDS community analysis since you don’t have a grouping factor (n=1 per site) such as seed mix a, seed mix b and so on.

L232-235. Counts during the pollinator surveys? What statistical test did you use to test for observed difference in abundance? You do not specify it here or in the methods – just referring to reads and genus diversity which I assume refers to the sequencing dataset.
L249. Minimum of one – for a single individual?

L252-254. You have to be very careful here. Up to this point you have been referring to pollen removed from the bodies of pollinators. You now state that pollinators collected pollen from. This is not something you can assume. Many, many, many bee species (if not all) visit more flower species for nectar than for pollen. Some of the pollen types you detect with the very sensitive metabarcoding approach will be from nectar plants only. Since you did not use destructive sampling from the bees collected from the wildflower plots, you cannot be certain if the bee was collecting pollen or it was simply on its body from a previous nectar visit (as opposed to removing pollen directly from the scopa to ensure that it was purposefully collected). You will be able to infer a certain amount from the number of reads but you must be careful to note that the technique as you use it has clear flaws when trying to unambiguously identify pollen sources as opposed to plants used as nectar sources only.

L262-263. Do you mean detected by metabarcoding but not detected by floral surveys?

Discussion

L308. Table 4 doesn’t seem particularly relevant to this particular point

L327-340. It is important to discuss a third reason – pollen grains present on the body from nectar visits. Honey bees are indeed predominantly flower constant when pollen gathering, so multiple detections are highly suggestive of pollen accumulated on the body from nectar visits.

L392. This is a minor point but Asteraceae is used by bumble bees for pollen in small quantities, see Kleijn and Raemakers 2008 Ecology. I also feel it is worth discussing the difficulty in distinguishing between the very similar Anthemis and Chrysanthemum using the barcoding technique a little more.

Acknowledgements should not be used to report funding, that information will appear in a separate Funding Statement on the published paper, see guidelines.

Figures and Tables
Standardise formatting of the tables.
Table 1. This should be moved to supplementary information
Table 3. Requires additional formatting. “Site number” should be added as an additional row above the numerical sequence
Table 4. Check spelling of Andrena. Why is ‘male’ specific for certain taxa? If sex is specified, an additional column should be added. The table heading is ambiguous and cannot be interpreted without reference to the text. Sequenced how – to determine the insect species identity, or the identity of pollen on their body? “proportion of pollinators that produced a visible band and were successfully sequenced” is not correct, since you present a total not a proportion. Moreover there is a difference between the number successfully sequenced (heading) and the number sequences (table).
Table 5. Check spelling of Leucanthemum
Additional comments: I enjoyed reading this paper as it provides additional resolution to the flowering resources used by some species of urban bees visiting patches of annual flowers in urban areas. I think there are valuable results presented here, specifically in highlighting the value of annual flowers for bees (namely poppy and small flowered Asteraceae) and that these bees also use a wider variety of plant species found across the urban environment. As outlined in my comments above, I feel that the introduction needs a bit of work to more smoothly introduce the concepts and hypotheses you deal with.


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: POLLEN METABARCODING REVEALS BROAD AND SPECIES-SPECIFIC RESOURCE USE BY URBAN BEES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well-written with appropriate background.  Raw data is shared on NCBI SRA.
Experimental design: The tables could be reorganized to make them more easily understood

Table 1: Include summary of seed mix components in table heading?
Would be more broadly accessible to provide latitude/longitude rather than grid reference.
Table 2: The meaning of the column “% Reads in shared genera” is not clear.  Please change or provide additional information in the table to help interpret
Tables 3 and 4 should be combined into a single table so that the reader can compare number of bees collected with number yielding rbcL PCR products.
Validity of the findings: The data reported in the manuscript was collected only in July -- it should be made clear in the abstract and throughout the manuscript that these results are from a relatively limited period of time and that there could be differences outside of this time period.
Additional comments: I question the use of the term “pollinator” throughout the manuscript when “bee” would be more descriptive of the taxa sampled.  “Bee” already takes the place of “pollinator” in the title.  I understand that the intention of the research was to include flies and other insect groups, but the results presented are almost exclusively about bees.

Abstract: Include mention of rbcL in abstract so readers immediately know which gene was used
Introduction:
Line 86: mention that rbcL is a chloroplast gene
Methods:
Line 105: provide a bit more detail about sample tubes -- were these standard plastic microcentrifuge tubes?
Line 109: Rephrase “not be distinguished in the non-destructive field during sampling”
Line 121: Remove “that”
Line 212: Should be “six _Bombus terrestris_ individuals”?
Line 223-224: This was already reported in lines 189-190
Discussion:
Lines 383-385: Please reword to be more explicit.  This would have biased analyses against nectar-foraging bees because there would not have been sufficient pollen to produce a band on the gel?


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: POLLEN METABARCODING REVEALS BROAD AND SPECIES-SPECIFIC RESOURCE USE BY URBAN BEES
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: The introduction has been rewritten to more thoroughly introduce the question that the work addressed and to set it within a wider context.
Validity of the findings: The statistical methods employed have been improved from the original submission.
Additional comments: Thank you for your work addressing the concerns from the first review. I am very happy to see this work published in its current form, though there are a couple of very tiny changes that are needed but I don't think that merits the minor revisions category.

L37-40. Repetition of certain, consider altering
L42. Check paragraph formatting
L47-48. First example is within brackets with the references whilst the following examples are outside brackets
L112. Double full stop
L118. Check sentence end for missing full stop
L235. Change 7 to seven and 9 to nine
L266-267. Specific numbers?
L385. Remove c.f.


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: POLLEN METABARCODING REVEALS BROAD AND SPECIES-SPECIFIC RESOURCE USE BY URBAN BEES
Review round: 2
Reviewer: 2

Output:
Basic reporting: I previously reviewed this manuscript and I find that the authors did a nice job improving the manuscript and responding to both my comments and the comments of the other reviewer.  Overall, I think this is a really nice paper and demonstrates the kind of ecological and practical applications for which pollen metabarcoding is very suitable.  The discussion of the weaknesses of the non-destructive collection methods are nuanced and include needed discussion of incidental pollen (though that is still good evidence that a plant is providing benefits to bees through provision of nectar).

Take a careful look at all Table/Figure references.  I caught a few that appeared to be incorrect.

L224: Should this be Table 1 referenced here?
L265: Again, I think this is referring to Table 1.
Experimental design: As before, the experimental design appears to be good and the experiments thoughtfully executed.

The “Data Accessibility” section has been removed in the revised version.  It is important that the reference to the NCBI submission remains in some form in the manuscript, whether here or in the Methods section.

L150-153: Report lat/lon to the thousandths place as in Table S1.
Validity of the findings: As before, the findings appear to be valid and the changes made have improved the manuscript.
Additional comments: No additional comments


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

Input:
Title: MULBERRY EIL3 CONFERS SALT AND DROUGHT TOLERANCES AND MODULATES ETHYLENE BIOSYNTHETIC GENE EXPRESSION
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Mulberry is an important economically plant which has a very wide distribution range in world, especially in China. In this manuscript, the authors investigate the function of EIN3/EIL, the key component involve in ethylene signal transduction, in response to abiotic stresses in non-model plant mulberry. Using quantitative real-time PCR analysis, the authors found that expression levels of MnEIL3 were significantly upregulated in roots and shoot in response to salt and drought stress. Meanwhile, overexpression of this gene in Arabidopsis enhanced plant’s tolerance to salt stresses and showed better ability to survive from drought stress after re-watering. Further, authors tested the influence of MnEIL3 on the transcription of four downstream ethylene biosynthetic genes and showed that MnEIL3 significantly enhanced the activities of two promotors. Based on their experimental results, a working model of mulberry MnEIL3 in response to abiotic stress was proposed.

This manuscript is well organized and well written. The authors familiar with the background and progress in the field. Characterization of the function of MnEIL3 in abiotic stresses tolerance and ethylene biosynthetic genes expression will provide new clues for the community. I am in favor of this study being published in PeerJ after the “Discussion” be revised by adding the comparison of the function of EIL3/EIL in response to abiotic stresses in model plants and non-model plants. Is there any difference? Another suggestion is revision of the title. The title should be concise, provide an overall view of the paper’s significance.

Typo mistake:
Line240 : “on” significant differences should be “no” significant difference.


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: MULBERRY EIL3 CONFERS SALT AND DROUGHT TOLERANCES AND MODULATES ETHYLENE BIOSYNTHETIC GENE EXPRESSION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript was clearly written and easy to follow. The Introduction section provided sufficient background information of the research field with proper literature references. Minor wording issues: line 42, “ethylene and resulting in”, should be “ethylene, resulting in”; line 57, “stabilized” should be “stabilizes”; line 236, “enhanced the tolerance to salt stresses” should be “enhanced the tolerance to salt stresses (Fig. 2)”; line 240-241, should correct to “no significant differences appeared between the growth of”; line 247-248, “the data has been reported” should be “the data reported”; line 251, should be “The analysis suggested”; line 262, should be “results reported in kiwifruit”; line 264, “providing” should be “provide”; line 268, “(Fig. S2)” should be “(Fig. S3)”; line 284, “overexpressed” should be “overexpressing”. It would be better if the authors can mention in Introduction that ein3-1 and eil1-1 are ethylene-insensitive mutants. Moreover, to remain consistent, “ein3 eil1 Arabidopsis” should be referred to as “ein3-1 eil1-1 Arabidopsis”.  As for figure legends, the authors should add what significance levels letters “a”, “b” and “c” refer to in Fig.1.
Experimental design: Sufficient details were provided in the Materials and Methods section as well as supplementary materials to allow for replication. It would be nice if the authors can explain the rationale as for why MnEIL3 was chosen as the focus of the study, not MnEIL1 or MnEIL2. The fact that MnEIL1/2 were able to modulate the activities of MnACO/MnACS promoters as demonstrated in the strawberry transient analysis is a sign that MnEIL1/2 could also play important roles in ethylene signal transduction.  If this is the case, it will be more informative if the authors can evaluate the expression profiles of MnEIL1/2 in response to salt/drought stresses.
Validity of the findings: In general, the data presented in this manuscript are robust with experimental replicates and supported the points the authors tried to make. One minor issue with Fig.3, the error bar was not clear for AtACS3. Were the numbers too tight to produce error bars or not enough replicates existed? In the Results section, although the authors stated that “the activities of MnACS1 and MnACS3 promoters were regulated by salt and drought stresses”, it was not clear from Fig. S3 how the MnACS1 promoter showed responses to abiotic stresses. Therefore it will be helpful if the authors can elaborate in the Results section how MnACS1 was regulated by abiotic stresses.
Additional comments: 1. The authors showed enhanced expression of AtACS/ACO genes in MnEIL3ox Arabidopsis as well as increased activities of MnACS promoters in Arabidopsis induced by salt/drought stresses. If possible, it will be better to measure the MnACS/ACO expression levels in Mulberry and see how they change upon salt/drought stresses.
2. In Fig.1, the MnEIL3 expression showed no significant differences at selected time points compared to no treatment. It will be nice if the authors can provide some hypothesis/speculations in the Discussion section as for why this might be the case. Or were similar time-dependent profiles previously observed in model plants for EIN3/EILs genes?


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: MULBERRY EIL3 CONFERS SALT AND DROUGHT TOLERANCES AND MODULATES ETHYLENE BIOSYNTHETIC GENE EXPRESSION
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript of Liu et al. describes the effects of the MnEIL3 gene on salt tolerance and drought stresses in Morus notabilis. They analyzed the role of MnEIL3 by heterologous overexpression in Arabidopsis by measuring resistance to salt and drought stress and induction of ethylene biosynthesis genes.The data provided in the manuscript are interesting, but unfortunately, the results presented are not sufficiently precise and rigorous to be accepted as is.

A native English speaker must revise the English language of this article.

The introduction of the manuscript is clear and the working hypothesis and objectives clearly exposed. However, there is an overall bias in the paper with no mention of occidental researches that are at the origin of the major discoveries on the ethylene biosynthesis and signalling pathways.  Despite the fact that this work is impressive, the presentation of the work lacks precision and consistency in its formal construction.

There is confusion for an uninitiated person between Morus alba L. (line 86) and Morus notabilis Schneid (line 106). Are alba and notabilis the same specie? Are they different species? Why are genes noted with MnEIL3 instead of MaEIL3? Can the authors present the genus Morus more clearly for an uninitiated reader? Which genus Morus model species have been already sequenced?

Throughout the article several acronyms are not defined: TFs, SIEDS, AP2, ESE1, CBFs, ARR, XTH33, LSUI, PERE, ECBS, ...
Finally, some major results are presented in the additional data. However, they are cited in the result section as major results. Why are not they integrated directly into the result section? There is therefore a major problem of coherence in the construction of the manuscript( ex: line 195-222).
There is an absence of homogeneity in the references: ex: line 430-435
Experimental design: This paper answers to the aim and scope of the journal.

However, the material and methods section suffers from a lack of precision. For example, there is no mention of the number of technical and biological replicates performed during PCRs and housekeeping genes used as control. How the calculations are made? Similarly, in the section statistical analysis, the nonparametric or parametric tests used are not indicated: T-test, Kruskal-Wallis, Mood's median test, ANOVA, ... nor the number of repetitions used.

I have a personal problem of understanding this study in relation to the induction of salt and water stresses that are never done on plants of the same age and in the same way. In my opinion the results are therefore difficult to compare. For example, in material and method section, see the different ways to get water stress: line 109 line 112 line 137 line 141. How the authors can justify these differences in the plant treatment?

Furthermore, Figure 2 that is supposed to show the effects of salt and water stresses is very poor scientifically. There is no serious quantified evaluation. Why did the authors not quantify the results of drought stress resistance by measuring the changes of proline and ABA concentrations, water loss of detached leaves, stomatal conductances, transpiration rate,...(see for ex: Yu, H., et al. Plant Cell 2008; 20:1134-1151)?
Validity of the findings: As mentioned earlier, the work lacks quantified results of the effects of water stress and drought on the transformed plants. This seriously affects the strength of the conclusions and the hypothetic model based solely on the expression data.
It is imperative that the PCR data be better explained (number of biological and / or technical repeats, control housekeeping genes, calculations...) and the statistics used indicated.
Additional comments: In conclusion, the publication cannot be reasonably accepted in this state without being rewritten and without additional data to better quantify at physiological level the effects of salt and water stresses in arabidopsis and Morus notabilis.


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: MULBERRY EIL3 CONFERS SALT AND DROUGHT TOLERANCES AND MODULATES ETHYLENE BIOSYNTHETIC GENE EXPRESSION
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors revised the title and text according to reviewers’ comments. Their efforts to provide more evidence to support the findings are appreciated. At the same time, detailed descriptions of methods and figure legends make the manuscript clear. The present result is recommended to publish.


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: MULBERRY EIL3 CONFERS SALT AND DROUGHT TOLERANCES AND MODULATES ETHYLENE BIOSYNTHETIC GENE EXPRESSION
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors revised their wording according to reviewers' comments. Their efforts to proofread the language by an editor should be appreciated.
Experimental design: The authors addressed my comments really well by elaborating on their choice of using MnEIL3 and by incorporating the expression profiles of MnEIL1/2 in Figure 1.
Validity of the findings: The authors addressed my comments by providing further descriptions of GUS activities (MnACS1) in transgenic Arabidopsis seedlings.
Additional comments: I really appreciate the authors' efforts to add MnACS/ACO expression profiles to Figure 5, which helped support their conclusions. Although it will be better, as I suggested in my original comments, to provide MnACS/ACO expression profiles and how they respond to salt/drought stresses in Mulberry instead of the model plant Arabidopsis. I understand that this data could be challenging to obtain, but would make the conclusions much stronger if available.
It's very nice that the authors provided the expression profiles of AtEIN3 and AtEIL1, which help address my 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: SULFATED POLYSACCHARIDES FROM PHAEODACTYLUM TRICORNUTUM: ISOLATION, STRUCTURAL CHARACTERISTICS, AND INHIBITING HEPG2 GROWTH ACTIVITY IN VITRO
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article does a wonderful job of isolating and testing the efficacy of sulfated polysaccharides from PTP. The manuscript is well written albeit a minor fixing and would be easily assessable to the international audience. The authors did a commendable job in introducing the wide spread usage of  Microalgae citing literature and the different uses of PTP.  Figures are relevant but lack labeling, legend and description.  (See my comments for the author)
Experimental design: The research is original and clarifies the aims and studies the role of Polysacs from PTP. The methods section seems to be incomplete and lacks a lot of material for instance MTT assay, cell numbers used for the experiment, time points assessed which would make replication impossible.  (See my comments for the author).  The most important issue I have here is the missing time-course of the effect of the drug.  (See my comments for the author).  I also have the question as to why only 1 cell line was tested for drug efficacy (HCC).  It would be nice if the authors can replicate the same results in another cancer type.
Validity of the findings: The data is robust and proper statistical methods were used. The conclusions for the most part are well stated.
Additional comments: The manuscript is well written and is easy to follow. It has a concise methodology and results are well presented and adhere to the standards of Peer J. However, there are some issues that need to be clarified, a few experiments performed before acceptance. Please see my comments below:-
Methods and Experimental Design:-

 1] I would suggest the authors perform a time course experiment to determine for the efficacy of PTP.  (Day 0, Day 1,3 and 5) along with the PTP concentrations mentioned here. Also, it would be good if you show how PTP compares to No treatment overtime and see the uninhibited growth rate of HepG2 without any perturbation. Methods section does not even mention about the MTT assay at all, I strongly suggest the authors add a description about the MTT assay. I would also suggest the authors describe all the information like number of cells used, time points assessed and analyzed.

2] Why was HepG2 chosen as the model cell line for the manuscript? I would strongly suggest that the authors repeat these experiments with different cell lines of different cancer types and show that PTP indeed has anticancer activity and is not limited to HepG2.  Again a time course study would be welcomed here. I would also suggest toning down the claim of anticancer activity based on the current findings from 1 cell line or be specific about HepG2 or Hepatocellular carcinoma if we can reproduce this effect in other HCC cell lines.

Results:-
1] Titles for results can be made more relevant so as to give the  gist of the result which can be expanded upon in the description. For instance, “PTP inhibits HepG2 growth invivo”.

2] Line 147 to 150 is confusing and contradicting. The current phrasing makes it difficult to comprehend and is convulative.  I suggest stating your findings in a more succinct manner.

3] I would suggest the authors expand upon the findings in the Section 3.3 “Cell Cycle Analysis” instead of statements like from the result we deduced…. (line 162 -172). In the current format, the authors leave the interpretation to the readers.

Figures:-
1] All the figures lack a description. Figure 1 lacks Y-axis information and description.

2] Figure 2 lacks description

3] Figure 3 lacks description, axis information ( Please indicate what does red and green colors represent)


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: SULFATED POLYSACCHARIDES FROM PHAEODACTYLUM TRICORNUTUM: ISOLATION, STRUCTURAL CHARACTERISTICS, AND INHIBITING HEPG2 GROWTH ACTIVITY IN VITRO
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript peerj-31007 reported isolation, structural characteristics, and
anticancer activity of sulfated polysaccharides from Phaeodactylum tricornutum.
The subject of this study meets the scope of PeerJ . The article has been carefully reviewed and I come up to the conclusion that the acceptance of this contribution may be considered after major revision.
Experimental design: Only specific comments about characterization (Mw).
Validity of the findings: Conclusions should be more straightforward. Therefore, please re-write this section to be more effective.
Additional comments: The manuscript peerj-31007 reported isolation, structural characteristics, and
anticancer activity of sulfated polysaccharides from Phaeodactylum tricornutum.
The subject of this study meets the scope of PeerJ . The article has been carefully reviewed and I come up to the conclusion that the acceptance of this contribution may be considered after major revision.
Specific Comments:
1.	Molecular weight (Mw) determination: The experiment described corresponds to a molecular weight distribution determination and the standards used were in the range 1-670 kDa while the estimated Mw of the sample was 4810 kDa. It is necessary to use standards presenting Mw in the range of the sample analyzed.
2.	In Table 2, chemical composition (sugars and sulfate) represent around 50% of the sample. What is the other 50%? Was protein content determined? Minerals?
3.	Neutral sugars quantification is reported ‘according to Sun YH, Chen XL, Cheng ZQ, Liu S, Yu HH, Wang XQ and Li PC. 2017. Degradation of
Polysaccharides from Grateloupia filicina and their antiviral activity to avian Leucosis virus subgroup J. Marine Drugs 15, 345’. However, it is necessary a more detailed description of the method used.
4.	In general, Figures resolution need to be improved.
5.	In Figure 1, FT-IR spectrum y-axis corresponds to % Transmittance?
6.	In Figures 3, 4 and 5 what does it means CK?
7.	In general, Figure captions need to be improved.


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: SULFATED POLYSACCHARIDES FROM PHAEODACTYLUM TRICORNUTUM: ISOLATION, STRUCTURAL CHARACTERISTICS, AND INHIBITING HEPG2 GROWTH ACTIVITY IN VITRO
Review round: 1
Reviewer: 3

Output:
Basic reporting: Background and Literature is nicely written.
Experimental design: Experimental design is good.

Need more information-as mentioned in comments below.
Validity of the findings: Conclusions need further data to support.
Additional comments: Comments on manuscript # 31007 "Sulfated polysaccharides from Phaeodactylum tricornutum: isolation, structural characteristics, and anticancer activity" by Yang et. al.
The author studied the sulfated polysaccharide from algae-

Following things need to be explained in the MS.
1.	Result 3.1 section, author mentioned characterization in table 1: Author didn’t show purification product after HPLC, which is important to make clear the starting material is perfect. Should be included as a Fig. before characterization?

2.	M&M heading, Extraction section: Author used ultrasonication to extract the polysaccharide and didn’t showed optimization parameters, saying length limit of paper (line 71-72)-I wonder why author thought that is not important? Quality control parameters are important always to reproduce the technique-should be included as supplementary data.

3.	Author characterized anti-cancer property against HEPG2 cell line and showed 60% at 250 ug/mL. In FT-IR results author mentioned that this polysaccharide is acidic in nature (line 137)-Did the author checked the pH of the culture medium after addition of the polysaccharide? Low pH will also kill the cells.

4.	Or is it cell lysis? Cell imaging will also show does it lyse the cells (like HEPG2).

5.	FTIR results, polysaccharide is sulfated in nature (same line 137)-Did the author checked any anti-oxidant property? What happens to ROS after addition to HEPG2 cell line, will give the clue about the mechanism of action?

6.	Author didn’t check the stability of the polysaccharide in the culture media. Stability Should be checked? For how long the HEPG2 cells were treated? Should also be included in Fig 2.

7.	Line 166-normal cells accounted for about 63%-It is a wrong sentence-Should be corrected by saying double negative PI-Annexin V cells.

8.	 Figure 3 and 4 are same, one is sufficient.

9.	Purification flow diagram can also be good to represent the technique of extraction.

The paper is technically sound and well written in nice English. Comments above- will make the MS better.


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: SULFATED POLYSACCHARIDES FROM PHAEODACTYLUM TRICORNUTUM: ISOLATION, STRUCTURAL CHARACTERISTICS, AND INHIBITING HEPG2 GROWTH ACTIVITY IN VITRO
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors made the necessary changes and the manuscript is ready to be published.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No comment


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

Input:
Title: SULFATED POLYSACCHARIDES FROM PHAEODACTYLUM TRICORNUTUM: ISOLATION, STRUCTURAL CHARACTERISTICS, AND INHIBITING HEPG2 GROWTH ACTIVITY IN VITRO
Review round: 2
Reviewer: 2

Output:
Basic reporting: In general the manuscript has been improved.
Experimental design: The methods are well described in this version.
Validity of the findings: The discussion and conclusion sections have been improved.
Additional comments: All the comments made by the reviewer are well addressed by the authors. So I would  suggest to consider for its 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: SULFATED POLYSACCHARIDES FROM PHAEODACTYLUM TRICORNUTUM: ISOLATION, STRUCTURAL CHARACTERISTICS, AND INHIBITING HEPG2 GROWTH ACTIVITY IN VITRO
Review round: 2
Reviewer: 3

Output:
Basic reporting: Poor English-Should be proof read by all authors-see comments.
Experimental design: Experimental design can be improved-see comments
Validity of the findings: Conclusions need further experimental validation-see comments.
Additional comments: Comments on manuscript # 31007v1 "Sulfated polysaccharides from Phaeodactylum tricornutum: isolation, structural characteristics, and inhibiting HepG2 growth activity in vitro" by Yang et. al.

My following comments last time-they are still unanswered

I believe following things need to be explained in the MS for the betterment of science.
1.	Result 3.1 section, author mentioned characterization in table 1: Author didn’t show purification product after HPLC, which is important to make clear the starting material is perfect. Should be included as a Fig. before characterization?

Author response: In this manuscript, we did not use HPLC to purify the polysaccharide. We used HPLC to determine monosaccharide composition.
In revised MS, Line 87: Author wrote Mw was determined by HPLC- the chromatogram should be included in MS in order to show how much purity is in the starting material?

2.	M&M heading, Extraction section: Author used ultrasonication to extract the polysaccharide and didn’t showed optimization parameters, saying length limit of paper (line 71-72)-I wonder why author thought that is not important? Quality control parameters are important always to reproduce the technique-should be included as supplementary data.

Author response: We would supply these parameters as supplementary data.
Author provided these parameters that is nice.

3.	Author characterized anti-cancer property against HEPG2 cell line and showed 60% at 250 ug/mL. In FT-IR results author mentioned that this polysaccharide is acidic in nature (line 137)-Did the author checked the pH of the culture medium after addition of the polysaccharide? Low pH will also kill the cells.

 Author response: Although PTP is acidic, it is chelated with other positive cations, so the pH is about 8.0. And the condition cannot kill the cells.
Author concluded by chemical characterization (line 159 in revised MS) and FTIR (line 166 in revised MS), that it is acidic in nature-By science that means overall charge is acidic? Otherwise author should mention in MS that acidic charge is neutralized by others and overall charge is?????

4.	Or is it cell lysis? Cell imaging will also show does it lyse the cells (like HEPG2)

Author response: In our opinion, the conditions and the characteristics of PTP did not make the cell lyse, although cell imaging was not done.
Cell imaging is easy to highlight what this PTP is doing to whole cells?

5.	FTIR results, polysaccharide is sulfated in nature (same line 137)-Did the author checked any anti-oxidant property? What happens to ROS after addition to HEPG2 cell line, will give the clue about the mechanism of action?

Author response: We did not check the antioxidant property of the polysaccharide. Maybe, just like other algae polysaccharides, PTP might have antioxidant property and we can do separate experiments to certify it. However, in culture media, it is difficult to determine the antioxidant property and it is not our emphasis.

For authors Clarity-Check ROS after PTP treatment vs no treatment? Include in MS.

6.	Author didn’t check the stability of the polysaccharide in the culture media. Stability Should be checked? For how long the HEPG2 cells were treated? Should also be included in Fig 2.

Author response: The treatment time has been added in Fig.2. Although we did not check the stability of the polysaccharides in the culture media, according to our experience on polysaccharides study, the polysaccharide was stable in the culture media unlike protein. And there is other paper about the polysaccharide anticancer activity( Samarakoon et al., 2014) which did not show the stability of the polysaccharide.

Whether other studies included stability or not is not the proper answer. Pre-incubation in complete culture media (for treatment time period) before adding onto the cell culture vs freshly added one will tell the stability-simple.

New comments:
7. Line 151: Author mentioned Yield is 1.5%- First author should mention that yield is written w.r.t. what, initial dry weight or something else? Second that represents a poor experimental procedure for Extraction (nobody is going to use that)-Did author optimized the extraction method, is the best one used (or given in revised MS) finally?  These should be clearly written in revised MS, that is why in comment 2, technique parameters are important to highlight your experimental procedure in order to reproduce those results.

8. Line 174: While, what’s the manner of PTP inhibiting HepG2 growth? This was not clear-should be rephrased in a good English.

9. Line 216: There was no other information about polysaccharide in this reference-Should be connected to the previous line sentence of Ref Agustini, otherwise no meaning. Connection between sentences is missing.

Poorly written English. MS should be proof-read by all authors which is lacking in revised MS.
Comments above- will make the MS better.

I recommend the MS “acceptance for publication with major revision”.


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: SULFATED POLYSACCHARIDES FROM PHAEODACTYLUM TRICORNUTUM: ISOLATION, STRUCTURAL CHARACTERISTICS, AND INHIBITING HEPG2 GROWTH ACTIVITY IN VITRO
Review round: 3
Reviewer: 1

Output:
Basic reporting: Written in standard English.
Experimental design: Experimental methodology well written.
Validity of the findings: Conclusions well stated.
Additional comments: Chromatogram should be well labeled (what each peak shows???) and included in MS.
Flow cytometry results for cell lysis should also be included in MS.


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 ANATOMY AND PHYLOGENETIC POSITION OF THE ERYTHROSUCHID ARCHOSAURIFORM GUCHENGOSUCHUS SHIGUAIENSIS FROM THE EARLIEST MIDDLE TRIASSIC OF CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Butler and colleagues provide a competent, detailed description of the erythrosuchid Guchengosuchus shiguaiensis, a yet poorly known member of an intriguing clade of Early/Middle Triassic predators. Although I’m not a native English speaker myself and probably not the best person to evaluate this, the manuscript seems to be written in clear, professional English and, apart from some minor misspelling of anatomical terms (see below), I did not detect any language errors. The authors provide a relevant, well referenced background, being fully successful in contextualize their objectives. The authors provide high-quality photographs and one drawing of the specimens, and all relevant structures are correctly labeled and described within the text.
Experimental design: The experimental design (that is, the phylogenetic protocol) is adequate, and the methodology well described (but see below).
Validity of the findings: Although the data is meaningful and the phylogenetic analysis is sound, I have some concerns about the availability of data (see below). All the conclusions are well supported by methodological background and presented results.
Additional comments: I have some minor to moderate concerns that, although not compromising the quality of the manuscript, should probably be addressed by the authors:

1.	Raw data availability: as the phylogenetic protocol was based on a still unpublished data matrix (Ezcurra et al., in press), reproducibility of experiments is compromised. Although this is maybe unlikely to happen, in case the manuscript here evaluated is published before Ezcurra et al., the raw data should be provided.
2.	Despite the description being exceptionally detailed, some comparisons are missing. I suggest the authors to improve the text by adding detailed comparisons between Guchengosuchus dorsal vertebrae and ribs with the same elements of other archosauromorphs.
3.	Figures: “postzygodiapophyseal lamina” and “prezygodiapophyseal lamina” are misspelled in Figure 13 label. Also correct similar terms in text lines 707 and 711. Also in figure 13, the label pp.af is not indicated on the photographs.
4.	Keywords: I suggest the authors to not repeat words from the title as keywords.

Line 52: Ezcurra et al., 2013; Ezcurra et al., in press.
Lines 53-54: please cite, for instance, Ochev (1958) and Gower & Sennikov (2000) to refer to Russian erythrosuchids.
Lines 180-182: As the anterior process of the maxilla is broken, maybe it would be precipitate to infer that this structure is ‘anteroposteriorly short’.
Lines 198-200: This lateral thickening of the ascending process is apparently interpreted as an earlier stage of the transformation series that led to the development of the characteristic maxillo-nasal tuberosity of later forms. It would be interesting to see this scored as a multistate character in the data matrix (in this case, Ezcurra, 2016 character 46).
Lines 289-292: Teyujagua paradoxa has marginal teeth that appear superficially to be fully thecodont, meaning that teeth are deeply inserted into alveoli and tooth crowns are apparently separated from bone walls, without striae. CT scans, however, showed us that, deep inside the alveoli, the teeth are ankylosed to surrounding bone. Could this be also the case for Garjainia and Erythrosuchus?
Lines 676-677: Could the transversal compression of the vertebrae be exaggerating the oval outline of the articular surfaces of centra?
Line 717: Could you please provide examples of the presence of spinoprezygapophyseal laminae in other archosauromorphs?


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 ANATOMY AND PHYLOGENETIC POSITION OF THE ERYTHROSUCHID ARCHOSAURIFORM GUCHENGOSUCHUS SHIGUAIENSIS FROM THE EARLIEST MIDDLE TRIASSIC OF CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors have done a very good job of redescrbing the holotype material of the basal archosauriform Guchengosuchus shiguaiensis and discussing its phylogenetic relationships to the erythrosuchids. Redescription of this specimen is important because it greatly improves on the detail of the figures included with the original description of the material by Peng (1991) and because of the damage and loss of material that the specimen has sustained since its original description. The damage sustained to the G. Shiguaiensis holotype and the loss of the holotype of the other Shanxi taxon Fugusuchus hejiapensis greatly limits the ability to reinterpret the basal states of erythrosuchids based on subsequent analyses.  The paper is clearly written, the descriptions appropriate, and the new figures represent a dramatic improvement on the figures from Peng (1991).

Lines 577-578 – remove ‘for’ or complete the phrase.
Experimental design: The authors split their morphological descriptions between new descriptions of the holotype material based on examination by the authors and attempts to re-interpret the photographs, drawings, and descriptions from Peng (1991) for the material that is now either missing or damaged. The new descriptions are thorough and the characters well illustrated and labeled. However, it appears that some of the information based on Peng’s (1991) illustrations and descriptions may be interpreted beyond the available resources, most specifically  in lines 853-864 discussing a putative tuberosity on the scapula which is barely visible in Peng's figures and in the discussion of the possible second ant orbital fenestra (lines 945-971), the existence of which cannot be evaluated fully without the complete ascending process of the maxilla and, ideally, the posterior margin of the premaxilla (an element not known in Guchengosuchus, although Peng also speculated on the fenestra's presence).
Validity of the findings: The phylogenetic conclusions of the authors seem consistent with the material as described.  However, it would be helpful to readers if more information was provided in the article and supplemental materials so that readers could interpret the data without having to refer to other analyses done by one or more of the co-authors. Specifically, Appendix A should describe the characters being modified from the Ezcurra et al (in press) character list, not simply list the numbers in the original analysis. In the discussion of the matrix in Materials and Methods (lines 89-95, the authors mention that the data set originally published by Excurra (2016) was used as a basis for the study, but as modified by findings in six subsequent studies. With so much modification, the matrix used should either be provided as an appendix or made available as a link in an online source like treebase.  Also, the assertions in lines 926-928 ( “The phylogenetic relationships of Erythrosuchidae found in our analysis are congruent with those previously recovered by Ezcurra (2016) and Ezcurra et al. (in press). The interrelationships within Erythrosuchidae are relatively robust and do not generate substantial ghost lineages.”) should be expanded in light of the extensive tree analysis and manipulation described in lines 92-114. Even though the focus of the paper is relationships among erythrosuchids, some outgroups should be included in Figure 20 or an additional cladogram, along with a more detailed discussion of how the altered character states affect the larger phylogenetic results.
Additional comments: Overall, an important addition to the anatomical and phylogenetic knowledge of the Erythrosuchidae. I have photos of the Guchengosaurus material taken during my 1990 visit to Beijing that show the specimen in its original state that I would be happy to share with the authors if I can get the slides scanned into a digital format. Incidentally, I was shown the material during that visit but asked not to include it in my analysis because of Peng's pending publication, which is why it was not included in my 1992 paper on erythrosuchid systematics.


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: GUANIDINE THIOCYANATE SOLUTION FACILITATES SAMPLE COLLECTION FOR PLANT RHIZOSPHERE MICROBIOME ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: First, I think this method holds promise. Harvesting rhizosphere samples from individual plants can be a time consuming endeavor and one not particularly well-suited for field work. However, the introduction needs a better justification for why this method is needed. Lines 60-63 state that outdoor temperature is the foremost factor affecting the analysis of rhizosphere microbiota (note: the authors should provide a citation for this), but what does this mean and how does their method alleviate it? The authors need to clearly state what the potential problem is (e.g. is it time until freezing? temperature of field sampling?) and how their method may present a solution. In my opinion, the workflow to isolate the rhizosphere sample – harvest root, vortex, filter, centrifuge, remove supernatant - seems much more of a problem for field based rhizosphere studies than the inability to freeze immediately. In what circumstances would researchers have access to a vortex and a centrifuge capable of spinning 50 mL tubes at 3200 g but not a -20 C freezer? I would like to see a more thorough explanation of why field-based rhizosphere sampling is challenging in general and exactly how the method presented here may offer a solution to some, but not all, the existing challenges.

I think very clear questions in the final paragraph of the introduction will help improve the focus and clarity of the entire manuscript. I suggest these questions centre around the following objectives: 1) the optimization of the GTC protocol (i.e. the number of rinses with PBS prior to DNA extraction); and 2) the comparison of GTC samples with RT and FR samples. Questions related to objective 2 should explicitly state what exactly will be compared (i.e. the diversity within and between samples and the abundance of individual bacterial taxa).

In my opinion all text related to the peanut microbiome specifically (lines 74-76; 214-225; and 264-272), should be removed. As it is, this component of the study comes across as superficial and not particularly interesting. Lines 214-225 is simply a list of the OTUs found in common bacterial phyla in the peanut rhizosphere. This neither advances our understanding of the peanut rhizosphere specifically, nor the plant rhizosphere more generally, but instead distracts from the most important results.

Additionally, the English language should be improved to ensure that an international audience can clearly understand the text. For example, lines 231-233 could be improved as: “These studies demonstrate that rhizosphere microorganisms might play an important role in future efforts to develop sustainable agriculture”.

Several of the included figures seem unnecessary. Figures 3 and 4 exhibit redundancy, the authors should choose one figure to present the findings related to differential abundance. Figures 6 and 7 are redundant. The PCoA is much more intuitive and informative than the plot of relative abundance correlations. Finally, figure 8 is not terribly relevant and is redundant with figure 3.

Line 44: add “The” to the beginning of this sentence.

Line 47: Lugtenberg and Kamilova 2009 not in references.

Lines 66-67: Surely the ability of GTC to denature DNAse and RNAse is relevant here.

Line 69: What does “robust stability” mean? The authors need to be more precise with what measures of “stability” or “reliability” (line 163) mean. Does stable = no change in alpha diversity, no compositional changes, and/or no changes in the abundance of individual taxa? How long were fecal samples left at room temperature for in these cited studies?

Line 86: I think the authors want Bulgarelli et al. 2012

Line 164-166: This seems redundant with lines 93-95

Line 236: citation?

Lines 251-256: This is a very long sentence. Please split into at least two.
Experimental design: In general, the Materials and Methods need greater detail and some important points are completely missing. For example, why are the methods leading to the results presented in lines 151-161 not described or even mentioned in this section? Additionally, the results could be bolstered by more rigorous statistical methods:

1) Why not analyze the effect of sampling on alpha diversity indices (Table 1)? A simple ANOVA could be used here.

2) PERMANOVA can be used to assess whether compositional differences among sampling treatments are significant. See the Adonis function from the R package vegan for an example.

3) I’m not convinced that analyzing differences in the relative abundance of individual bacterial taxa across sampling treatments is the appropriate analysis (line 131 and 134). This is due to properties inherent to NGS datasets including compositionality and high sparseness (see Fernandes et al. 2014 Microbiome). There are now a number of sophisticated methods to analyze the abundance of bacterial taxa across experimental treatments, which take into account the compositional nature of microbiome datasets. For example the R packages DeSeq2 and ALDEx2 both do this.

Line 82: What is Huayu22? A peanut cultivar?

Line 87: How much root? Was it a standardized amount?

Line 91: What is 100-mesh? 100 microns?

Line 93: 900 mg of rhizosphere sample is a lot of material even from 9 plants. How did you obtain this much material from root samples that could only fit into 50 mL tubes? Additionally, how did you ensure that the 9 subsamples were homogenous?

Line 96: Why were the GTC samples not frozen at -70 C? The comparison between FR and GTC is made more difficult to interpret because of this difference.

Line 100: How were the frozen GTC samples treated? Surely some thawing took place with these samples as well? In general, I think most researchers would agree that some thaw is unavoidable when extracting DNA from frozen samples. In fact, when extracting DNA from many samples simultaneously, as is often the case, a 15 min thaw is very optimistic and my guess is that many samples thaw for greater than 30 mins. My point is the 15 min thaw, if only introduced for the FR samples, is a strange and potentially confounding treatment to add.

Line 108: The authors state they used a MiSeq here but on line 118 state they use a HiSeq.

Line 110: The authors need to cite the source where they obtained their barcodes and primer constructs or else provide them in the supplement.

Line 119: What is a tag (also in lines 121 and 122)? The authors until this point have used the term read or sequence, please keep the same terminology throughout.

Lines 119-120: The authors need a much better description of their sequence quality filtering. I have no idea what would be removed from this statement. Did the authors use Q scores to filter? What does “N in over 95% of positions and low-quality” refer to? Also please cite the authors of Trimmomatic.

Line 121: What is the Gold database?

Line 127: Greengenes database. Wang et al. 2007 is the citation for the RDP classifier, please cite DeSantis et al. 2006 for Greengenes.

Line 128: Already gave the version of USEARCH.

Line 129: Were raw read counts, rarefied read counts or relative abundance used to generate UniFrac distances? Please clarify and justify.

Line 130: The authors need to include package numbers, individual functions, and the R version used. Also, scripts used for USEARCH, Trimmomatic, and R would be very helpful.

Line 133: What does top 15 genera mean? Does this mean the 15 most abundant genera across GTC, RT, and FR-2 samples?
Validity of the findings: Many of the results were difficult to interpret due to a general lack of statistical rigor, see points 1, 2 and 3 in the above section of this review, Experimental Design. For example, lines 179-181 report that GTC samples had higher diversity than FR samples but how was this analyzed?

Lines 182-190: see point 3 above in Experimental Design.

Line 198: Switch rho to r if Pearson correlations were calculated.

Lines 205-212: see point 2 above in Experimental Design.

Line 229: How do rhizosphere bacteria induce plant photosynthesis?

Line 247: No statistical tests were performed on diversity indices, significance cannot be determined.

Lines 248-250: Can the authors speculate why storage at room temperature does not always cause perturbations to microbial community composition? Does it depend on sample type?

Lines 258-260: What is intraobserver reproducibility? I’m struggling to follow the logic in this statement.

Lines 274-279: The conclusions will be strengthened if the authors can return to clear questions asked in the introduction and state how their method will alleviate the challenges of rhizosphere sampling in the field. The authors state that this method will be helpful when many samples are collected but don’t explain how. Processing many rhizosphere samples in the field will not be made easier by skipping the fastest step (placing tubes in freezer), so really this method is most useful when researchers do not have access to a freezer in the field.
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: GUANIDINE THIOCYANATE SOLUTION FACILITATES SAMPLE COLLECTION FOR PLANT RHIZOSPHERE MICROBIOME ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Sun et al. report on whether the treatment of peanut rhizosphere samples with guanidine thiocyanate (GTC) is a good way to preserve microbiome DNA in the field for later extraction and analysis. This is a useful question, and I expect many people working on plant microbiome studies will be interested in the answer. For the most part, Sun et al.’s report is professionally structured and written with appropriate figures and tables, and appropriate citations have been included. The raw data from this study have been made publically available.

My main concern about the basic reporting is that the manuscript was generally difficult to follow, due to a combination of minor grammatical errors throughout and some confusing structuring. I feel that the manuscript would benefit greatly from extensive copy editing to improve the grammar and structure. I have made a few suggestions along these lines in comments on the attached pdf.

In particular, I think the subject of the first paragraph of the Results (lines 150-161) should either be treated in the Methods, or be omitted/removed to supplemental information, and that background and citations given in the Discussion (lines 227-245) should appear in the Introduction instead. Also, samples FR-8d and FR-31d should be included in more of the text and figures.
Experimental design: The study is original primary research within the aims and scope of PeerJ. The research question is useful and timely, and the technical aspects of the study appear to be sound.

However, the experimental design does not fully address the research question as I understand it. The manuscript seems to be written as a test of GTC supplementation for preservation of intact microbial communities compared with sample storage at room temperature. The standard to which both GTC and room temperature storage are compared is cryopreservation (freezing at -70). GTC-treated samples were stored at room temperature for 24 hours and then frozen at -20 for an additional 1, 7, and 30 days before DNA extraction, but untreated samples were extracted after 2, 8, and 31 days at room temperature. Since no untreated samples were at room temperature for only 24 hours (and no treated samples were at room temperature for 2, 8 or 31 days), we can’t directly compare GTC addition and storage at room temperature. To put it another way, we can’t disentangle the contributions of freezing at -20 versus addition of GTC to the preservation of community profiles. I think a better test of the question as I understood it would be to compare samples treated with GTC and frozen after 24 hours with samples not treated with GTC then frozen after 24 hours, rather than left at room temperature for 2, 8, and 31 days.

Sun et al. demonstrate convincingly that GTC addition followed by 24 hours at room temperature prior to freezing at -20 does not significantly change the microbial community profile compared with immediate freezing at -70, which is a useful result. They also show that leaving samples at room temperature for 2 days and longer results in changes in the microbial community profile, which is also a good finding. However, I cannot tell from their study whether GTC addition preserves microbiome DNA any better than leaving samples at room temperature for 24 hours without any additive prior to freezing at -20. This manuscript should be rewritten to avoid giving the impression that GTC addition is directly compared with room temperature storage, because in my opinion the experimental design does not allow a meaningful comparison to be made.
Validity of the findings: The data from this study are publically available, and the findings appear to be valid in that the data are appropriately analyzed and visualized.

My main concern here is about comparing GTC treatment with room temperature storage for preservation of microbiome DNA, since I don’t think this is a valid comparison in this case (see comments above). Conclusions along these lines should be carefully rewritten to be consistent with what the results show.
Additional comments: I agree with the authors that immediate cryopreservation of samples in the field is usually not practical, and a good alternative for plant microbiome sample preservation is needed. One alternative practice is to store samples on ice while collecting in the field (eg. in a portable insulated container), and I wonder if the authors can comment on how they think this might affect microbial community profiles.


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: GUANIDINE THIOCYANATE SOLUTION FACILITATES SAMPLE COLLECTION FOR PLANT RHIZOSPHERE MICROBIOME ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I commend Sun et al. for producing a nicely revised manuscript. The introduction lays out the objectives of the study more clearly now. However, there are still some critical methods missing.

Line 40: Citation needed here

Line 76: Please state what ‘promotes stability’ actually means  here(e.g. no change in diversity or composition?).

Line 107: Please state that 100 mesh = 100 openings per square inch.

Line 172-174: Please state where this universal primer pair comes from.

Line 215: please change to p < 0.001, or something similar.

Line 219: This was supposed to be change to ‘illumina sequencing’.

Line 227-228: In order for the ANOSIM results to be interpretable, the reader needs some description of the analysis. Please include this in the methods. Readers will not know what R means in this context.

Figure 6: This is not interpretable. What is the y-axis? I recommend removing this figure. Fig. 5 is a nice representation of the compositional differences among sample types and the ANOSIM provides statistical support. Fig. 6 does not help with the comprehension of this result.

Line 267: It seems likely that storing rhizosphere samples at room temperature affects diversity and composition not only through DNA degradation but also through changes in the abundance of individual taxa. Tube at room temperature is a very different niche than the rhizosphere and likely selects for particular bacterial clades.

Line 277: Please remove subsequent analysis from this sentence and simply state that the method did not affect bacterial diversity or structure.

Table 1: The results from the significance tests don’t make a lot of sense for High-Quality Sequences. FR-8d RT and RT-2d are nearly identical in mean and variation but are significantly different? While FR-2d appears to be quite different yet is not significantly different. Please double check these results. Are values mean plus/minus standard error? Please state in caption. Also please be consistent with the rounding of numbers i.e. some values have a decimal place while others do not. Finally, this is the first I see any mention of stats (ANOVA – Dunnett’s T3). Please describe these analyses in the appropriate section, including why Dunnett’s test was performed.
Experimental design: Line 183-193: The statistical analyses used to obtain the results presented here are not described anywhere. Please provide a description of the analyses used in the ‘GTC Buffer and DNA extraction’ section.

Line 202: The statistical analyses used to obtain the results presented here are not described anywhere. Please provide a description of the analyses used in the ‘downstream data analysis’ section.
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: IMPACT OF AGRICULTURAL FARMS ON THE ENVIRONMENT OF THE PUCK COMMUNE: INTEGRATED AGRICULTURE CALCULATOR—CALCGOSPUCK
Review round: 1
Reviewer: 1

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: Annotated pdf is 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: IMPACT OF AGRICULTURAL FARMS ON THE ENVIRONMENT OF THE PUCK COMMUNE: INTEGRATED AGRICULTURE CALCULATOR—CALCGOSPUCK
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please, see attachment
Experimental design: Please, see attachment
Validity of the findings: Please, see attachment
Additional comments: Please, see attachment


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: IMPACT OF AGRICULTURAL FARMS ON THE ENVIRONMENT OF THE PUCK COMMUNE: INTEGRATED AGRICULTURE CALCULATOR—CALCGOSPUCK
Review round: 2
Reviewer: 1

Output:
Basic reporting: See attached PDF
Experimental design: See attached PDF
Validity of the findings: See attached PDF
Additional comments: See attached PDF. The authors must attend to the editorial edits in that PDF.  With that done, I have no objection to the publication of this paper.


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: IMPACT OF AGRICULTURAL FARMS ON THE ENVIRONMENT OF THE PUCK COMMUNE: INTEGRATED AGRICULTURE CALCULATOR—CALCGOSPUCK
Review round: 2
Reviewer: 2

Output:
Basic reporting: The work presents an important and current problem of monitoring and control of agricultural production in the aspect of water protection.
All substantive corrections brought by the authors of the publication are sufficient and satisfying. The work is suitable for publishing in PeerJ - the Journal of Life & Environmental Sciences.
However, the publication requires editorial corrections. In many places, there is no space between words. In Polish names, authors sometimes use Polish characters, and sometimes not (eg. Gdańsk - Gdansk). This should be harmonized. Some units in headers in the tables, they need corrections (eg. should be kg·ha-1).
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No comment


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

Input:
Title: HYBRID IDENTIFICATION FOR GLYCINE MAX AND GLYCINE SOJA WITH SSR MARKERS AND ANALYSIS OF SALT TOLERANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript focusses on identifying true hybrids from backcrosses of G.max and G. soja using molecular tools such as SSR markers. Salinity is a major obstacle in crop production, causing soil degradation or erosion and urgent attention is required. Authors have chosen molecular approaches to identify and propagate true hybrids which can sustain salinity at the same time increased yield. Authors used backcrosses or three-way crosses between two distinct yet relative crops and resulting hybrids were verified for polymorphism using SSR markers. Furthermore, authors evaluated salt tolerance, relative growth, and dry matter accumulation of particular hybrids and shown that their methods created true hybrids that are salt tolerant soybean germplasm. Manuscript was well written with professional language and literature work is thorough. Introduction part was very well written with potential problems of salinity and how this can be prevented. Authors need to check for sentence formation where they need to increase scientific language rather than just normal English. Tables are represented well however figures of electrophoresis looks unclear especially Figure 2 and Figure 3 B. Authors should mark the observed bands or either mark the ladder.
Experimental design: Manuscript meets the aims and scope of the journal and experimental designs are well presented. Authors are well versed in this field and they have used proper experiments to answer key questions. Authors approaches for identifying true hybrids using backcrosses or three-way crosses and SSR markers is not novel but many groups have used this particular technique and shown to be successful. Authors done an excellent job in providing details of treatment of strains for hybridization. PCR amplification, SSR-PCR reaction system to screen polymorphic patterns among parents of different cross combinations were well designed. Authors should give the list of primers in a table so that this can be helpful for future groups if they want to test them. Authors need to mention why they have chosen true hybrid group G for salt tolerant tests after molecular appraisal results. Why not C group that have more percentage of true hybrid. Salt tolerant and dry matter accumulation experimental methods are well designed.
Validity of the findings: Results part was written well and study shows original results from designed experiments but authors need to improve discussion part as they confirm the results but not giving detailed discussion. Results from DNA extraction and true hybrid identification was well explained. Authors mentioned in Line 172 that they have chosen combination 7 as the best one. On what basis? Did they selected based on banding pattern?  True hybrid selection results were well represented in the table but the explanation is kind of confusing from line 184 till 186. Selection of true hybrid based on banding pattern is interesting. Salt tolerance experiment results are slightly over interpreted. Authors mentioned in line 202 that G3 and G9 are roughly equal to their male parent 3060. However It looks like G9 is having higher salt tolerant coefficient than 3060 or G3 especially 1st and 100% plants. Dry matter accumulation results clearly show that G9 and G13 has the least drop compared to others. Conclusion part can be elaborated giving details of future work.
Additional comments: Authors have focused on identifying true hybrids from backcrosses of two different soybean crops using molecular tools such as complementary SSR markers. Authors main goal is to identify the true hybrid and further evaluate salt tolerant coefficient to see if the plants can overcome salinity at the same time maintaining proper growth rate. Authors have done excellent job in designing proper experiments for backcrosses or three-way crosses. Experimental procedures and results section was written well. However authors need to improve the discussion part in terms of results interpretation. Overall the manuscript was well written with minor revisions required. Please see some minor comments below.
Authors need to improve on sentence formation and also need to improve scientific language as some times very lament terms were used in the explaining the results.

Line 223-234 belongs to introduction part rather than discussion part.

Authors need to re write the whole sentence from line 139 to 144. Looks like there is issue in sentence formation and can’t understand what they are talking about.

Please remove So from line 252. What does it mean by “this work can be done more excellently” from Line 256. Please rephrase this sentence.

Authors need to re write the sentence from Line 265-270. Authors can mention that SSR marker technology can be a powerful tool for identifying true hybrids of soybean and this method can be of great significance in breeding of new salt tolerant soybean cultivars. Please consider this as minor 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: HYBRID IDENTIFICATION FOR GLYCINE MAX AND GLYCINE SOJA WITH SSR MARKERS AND ANALYSIS OF SALT TOLERANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this study the authors explored the combination of SSR markers and physiological index to identify soybean salt tolerant germ plasm. This is an interesting and thorough paper, although, its logic is largely based on previous studies (identification of soybean varieties, genetic map construction and genetic evolutionary relationship between species etc). SSR markers have also been used for variety identification and/or hybrid purity determination in rice, wheat, common bean, cotton, rape, peanut, apple, orange and psidium (Gaitán-Solís et al., 2002, Nandakumar et al., 2004; Dawson et al.,2013; Tuler et al.,2015 ). The authors established a straightforward soybean SSR-PCR system to determine parental co-dominants for hybrid identification. Further screening for salt tolerance, growth rate and dry matter accumulation resulted in identification of true hybrids while avoiding false positives. The results provided by the authors are consistent with their claims and can be published as is.


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: HYBRID IDENTIFICATION FOR GLYCINE MAX AND GLYCINE SOJA WITH SSR MARKERS AND ANALYSIS OF SALT TOLERANCE
Review round: 1
Reviewer: 3

Output:
Basic reporting: - The manuscript is not clear and unambiguous and it needs a professional English editing service.

- Background is sufficiently provided, but authors should stick to high-profile journal references

- There is an excess of tables (table 4 is the only important table), but figures are OK.

- Authors need to better clarifiy crosses; a figure could help on this. Authors also should consider if it is really necessary to detail all field trials before obtaining hybrids.
Experimental design: - The research question is relevant and meaningful, but authors were too wordy to have a well defined research question.

- Methods are detalied, but  the section "Plant materials and treatments" is too long and confuse. Authors, based in articles that describe breeding experiments, should make a shorter explanation to explain how they obtained hybrids. In a separate section, they can explain salinity tests. DNA extraction do not have a key reference.
Validity of the findings: Authors should be more concise to explain the novelty of their findings.
Additional comments: No additional comments


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

Input:
Title: HYBRID IDENTIFICATION FOR GLYCINE MAX AND GLYCINE SOJA WITH SSR MARKERS AND ANALYSIS OF SALT TOLERANCE
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors have focused on identifying true hybrids from G.max and G.soja using SSR markers. Authors have made considerable changes and improvements from their previous manuscript. Authors have also improved the scientific language with updated literature work. The figures were carefully marked with explanation in the text. Discussion part has been substantially improved. The use of SSR makers to identify hybrids and screening test for salt tolerance, growth rate and dry matter accumulation has significant advantage to improve salinity resistant crops. Overall the manuscript looks polished with clear discussion.
Experimental design: Authors done excellent job in designing suitable methods for back crosses, identification of true hybrids using SSR markers. Experiments to test the hybrids for salt tolerance, dry weight accumulation and growth rate were well designed.  Authors have explained well in the response to comments for this section and I am satisfied with the responses given especially for primers and the reason for using G group but not C group as true hybrids.
Authors did not made any new experiments from previous manuscript, so new comments.
Validity of the findings: As mentioned in my previous review comments, results part was written well and study shows original results from designed experiments but authors need to improve discussion part as they confirm the results but not giving detailed discussion. Authors have done excellent job in responses for comments in this section. I appreciate your changes in the true hybrid identification of different soybeans section from results. Appreciate the changes made to the manuscript and explanation and clarification of question related to G3 and G9 differences. Acknowledge the authors for revising the conclusion part and adding details for the future research.
Additional comments: Firstly, an excellent job by the authors on carefully revising the manuscript and giving feedback to the question that were addressed from the previous manuscript. The figures look much better from previous version with markings. Authors have also made significant improvement in scientific writing and giving new references. Overall the manuscript looks good and is worth published. Thank you for the comments and clarification from previous questions.