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: DYNAMIC SUCCESSION OF SUBSTRATE-ASSOCIATED BACTERIAL COMPOSITION AND FUNCTION DURING GANODERMA LUCIDUM GROWTH
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall, this paper is well-written, well-structured and interesting. Detailed comments are provided on the pdf of the manuscript, but some overarching comments are given below.
The choice of which figures and tables have been placed within the main body of the text versus the supplementary material would benefit from revision. Figs S1 and S3, and Table S1, would be more appropriate within the main body, along with a figure similar to Fig S2. Fig 2, on the other hand, could be placed in supplementary material.

Please make sure that in-text citations list papers in date order, from oldest to most recent.
Experimental design: I have some concern over aspects of the analysis, particularly regarding whether and how differences in sequencing depth were controlled for. I assume that the data were not rarefied or subjected to other normalisation procedures before NMDS and PERMANOVA. What was the read distribution between samples? Both techniques are sensitive to differences in sampling depth, which can produce false clustering (see Weiss et al. 2017 Microbiome 5:27). In the case of PERMANOVA, this can be compensated for by including sample depth as a predictor; for NMDS, colouring the points by sequencing depth allows the plot to be checked by artefacts. Whilst I am not familiar with LefSE analysis, if it looks at differential abundance the data need to be normalised before analysis.

Some further detail is required in the Methods section – see notes on the manuscript.
Validity of the findings: The discussion focuses quite heavily on contextual information and restatement of results. I think it would be improved by digging further into interpreting the results, and hypothesising what may underlie them.
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: DYNAMIC SUCCESSION OF SUBSTRATE-ASSOCIATED BACTERIAL COMPOSITION AND FUNCTION DURING GANODERMA LUCIDUM GROWTH
Review round: 2
Reviewer: 1

Output:
Basic reporting: At line 55: signficant should be significant
Line 87: bag should be bags
Line 117: were presented in details in should be have been described in detail in
Line 138: permuations should be permutations
Line 163: The high quality reads ranged from 25,996 to 69,618 OTUs between samples (Table S1). I believe the amount of reads is described here.
Line 249: Dominate should be dominating
Line 251: exits should be exist
Line 256: cause a decline the should be cause a decline in the
Line 278: The activities of bacterial community should be The activities of the bacterial community
Line 282: The reduction in substrate total nitrogen, phosphorus and potassium at the elongation stage highly supported our results. I believe this claim should be clarified.
Line 284: Increase should be increased
Line 297: secreted should be secrete
Line 309: when the moisture content was in high level should be when the moisture content was high
Line 310: that microbes produced should be that microbes produce
Line 314: be associated should be are associated
Line 315: are the key players for bacterial adaptation This piece of text makes the sentence faulty
Line 319: in bacterial community should be in the bacterial community
Line 326: pathway should be pathway
Line 334: of in the bacterial community should be of the bacterial community
Line 358: stage be crucial should be stage is crucial
Experimental design: I appreciate that you included pictures showing the experimental setup, this way other researchers are able to replicate your experiment. In the current version, it also became more clear what type of samples you have analysed. Good job.
Validity of the findings: Line 320: colonization mechanisms of the bacterial settlers that entered into the substrate from air: Here it is written for the first time that the bacteria are coming from the air. In my opinion, the effect of the bacteria entering the substrate from air (or from worker’s hands) could be one of the strongest in microbial composition development. Since this is so crucial, I do not understand why this aspect is not mentioned earlier in the article. Please consider this for the final version.

Line 331: fungus and the associated microbiome: To my opinion, you can not say that the bacterial community is associated with the fungus or its growth. In line 17 you also speak about G. lucidum-associated bacterial communities as well as in the Background. Again, you can not state this. For example, in many insect studies some bacterial genera like Providencia or Proteus are associated with the insect’s presence (i.e. Singh et al., 2014*). In the current study there is not enough evidence for the association of the bacterial community with the fungus’ presence, so please do not make these statements or suggestions. What I can agree with, is the term “substrate-associated bacterial composition” which is also used in the title of the article.
Additional comments: No other 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: DYNAMIC SUCCESSION OF SUBSTRATE-ASSOCIATED BACTERIAL COMPOSITION AND FUNCTION DURING GANODERMA LUCIDUM GROWTH
Review round: 2
Reviewer: 2

Output:
Basic reporting: This was within guidelines.
Experimental design: This was within guidelines
Validity of the findings: Good
Additional comments: Overall, I found the revised manuscript cleaner and more engaging and insightful. The authors did a good job revising the manuscript, and it is more streamlined and reads well.


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: DYNAMIC SUCCESSION OF SUBSTRATE-ASSOCIATED BACTERIAL COMPOSITION AND FUNCTION DURING GANODERMA LUCIDUM GROWTH
Review round: 2
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I would like to congratulate the authors on their very thorough revisions, which have greatly improved the quality of this article. I am very satisfied with the response to my previous points. However, I would request that the following minor alterations be made prior to publication:
Line 84: Remove the capital L from lucidum
Line 88: E, not Ei
Lines 128-129: The comment regarding barcoding should be in the section about PCR, rather than data processing
Line 239: Replace 'proved' with 'demonstrated'
Line 334: The phrase "indicating that they were the first settlers in the substrate" can be misleading. Although bacterial persistance does indicate that these bacteria were present early on, the more pertinant point is that they continued to be present rather than being replaced by other taxa.
Line 340-341: Fluorescent pseudomonads is a description, not a species name, so should not be in italics or capitalised
Table 4: Please provide P-values, rather than just significance codes
Fig 3: Relative abundance data may still cluster by sequencing depth on a NMDS plot (see Weiss et al 2017 Microbiome 5:27). Looking at Table S1, I am satified that this effect is not responsible for the primary pattern observed here. However, it is always advisable to check for sequencing depth effects by plotting. This may be done simply in R with the following code:
#Calculate depth (where samples are rows and OTUs columns)
depth<-(rowSums(OTUtable))
#Convert it to a value between 0-255, for later use in plotting
val<-max(depth)/255
grad<-depth/val
plot(NMDS$points[,2]~NMDS$points[,1], col=rgb(red=255,blue=0,green=0,alpha=grad,maxColorValue=255), xlab="NMDS1", ylab="NMDS2")


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: MULTI-OMIC PROFILING TO ASSESS THE EFFECT OF IRON STARVATION IN STREPTOCOCCUS PNEUMONIAE TIGR4
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study the authors used multi omics strategies to investigate the effect of iron starvation on pneumococci.
Experimental design: •	the authors mentioned that pneumococci were cultured in THB. Was this soley THB or was THB supplemented with yeast extract
•	the authors used desferoxamine meslate salt for iron starvation. How was the iron concentration in THB with and without DFO determined. Which concentration is available for pneumococci in THB
Validity of the findings: •	DFO effects on growth were tested using THB. The statement is that there was iron starvation did not cause a lag phase. However, when looking at the growth curves there seems to be a difference in growth and it is not clear whether this is a significant effect. Here, the values of the growth rates will be helpful
•	Transcriptomics: the authors used biological replicates and performed a MA plot analysis (after normalization of the data). The plot suggests that the variance of the individual transcriptomic experiments is high and that a high number of genes in the plot biological replicates show high standard deviations and are out of the range for replicates. Please comment on the reproducibility of the microarray analysis. This is in particular important because of the data shown in Figure 2 and Table 1 as well as Table S1. In the latter table only a few genes are depicted (see also text  line 263...) which do not reflecting the number of regulated genes described before.
•	The proteome analysis was done by 2-D-GE. There is a recent paper (doi: 10.1016/j.ijmm.2018.02.001. [Epub ahead of print] PMID: 29496408) that has demonstrated the effects of iron limitation on the pneumococcal proteome using gel free LC MS/MS analysis. Here different conditions and iron concentrations were used. The effects of iron starvation on the cell phasiology and cell division have been demonstrated. I recommend a comparison of the datasets and to include this study in the paper. This will significantly strengthen the submitted study.
•	How many replicates have been done for the 2-D-GE?
•	The MS analysis has been done with fixed modification of methionine. Why not with variable modifications?
•	 Regarding the metabolome analysis the energy charge of the samples has not been mentioned in the methods. This is crucial for the reproducibility of the intracellular metabolome data under the selected conditions.
•	Finally, a data integration approach would be advantageous, if possible
Additional comments: This is a study supporting earlier studies using a combined apporahc of multi-omics to demonstrate the physiological changes of pneumococci under iron starvation conditions


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: MULTI-OMIC PROFILING TO ASSESS THE EFFECT OF IRON STARVATION IN STREPTOCOCCUS PNEUMONIAE TIGR4
Review round: 1
Reviewer: 2

Output:
Basic reporting: The structure of the manuscript follows that required in PeerJ. Overall, the manuscript is written to a respectable standard although further detailed editing is required throughout the manuscript to ensure consistency in quality.
Introduction presents the context of the subject of this work and the necessity of inclusion of physiologically relevant conditions into experimental design.  The focus is towards cation limitation – namely iron – and its effects upon a representative strain of the major human pathogen Streptococcus pneumoniae.
Some specific background points lack suitable citations or are inaccurate. For instance, it is stated in lines 42-44 that “bacteria can express certain proteins called siderophores, specialized in uptaking divalent cations from the environment”.  Firstly, siderophores are more typically secondary metabolite rather than proteins and – in respect of iron – are typically involved in acquisition of trivalent ions i.e. ferric iron (Fe3+).  Does S. pneumoniae synthesise a siderophore or does it “scavenge” via other siderophores as well as heme?  Inclusion of a brief consideration of iron acquisition systems specific to S. pneumoniae would be appropriate, e.g. Ge & Sun 2014.
There are two recent publications which are relevant to cite.  These separately address metabolomics [Leonard et a., 2018] and proteomics [Hoyer et al., 2018] of S. pneumoniae under iron limitation. These will also be useful material for inclusion in Discussion.
In common with many presentations of omics data, summary Figures are provided in the text along with extended tables.  Although not visually engaging, it is necessary and appropriate to provide summary data and to present results in tabular format.  Among the figures, Supplementary Figure S1 in particular requires clarification: panel A indicates 8 samples termed A to H, each with a different colour line however only one line appears in the density x intensity plot (panel A).  This would seem correct assuming plots in panel B are correct.  Panel B presents an array x intensity plot which show appears to show identical range of values across all 8 arrays.  Is this correct? A re-evaluation and inclusion of extended legend would be helpful.
There is an extended table with processed data for microarray experiment as Supplementary Dataset and a URL for GEO database entry is indicated.
Experimental design: The manuscript describes a combination of omics approaches to a representative of a species of significant human pathogens.  The fundamental question and scientific approach fall within the scope of the journal.
The central purpose is to define alterations in expression (transcript, protein, metabolite) occurring in response to iron limitation.  This is a physiologically-relevant stress and mimics a key aspect in nutrient limitation occurring in tissues. Iron limitation is a widely applied condition for exploration of bacterial characteristics resembling in vivo and has been used with many bacterial, including Streptococci.  Two recent publications apply proteomics and metabolomics to S. pneumoniae and require consideration.
Experimentation employs a single bacterial isolate representing a high virulent clade of S. pneumoniae.  This strain is widely used by many researchers for a range of purposes and does not pose ethical issues.
The microbiological methods, though routine, are not entirely clear.  Standardisation is highly important given the sensitivity of omics methods to experimental variation.  Some further detail of culture procedures would be helpful. For example, were replicate cultures standardised by inoculum; was a “starter” culture prepared then a standard inoculum dosed into experimental cultures? Was culture carried out with shaking or static; was this in air, with added carbon dioxide or other atmosphere?  Was the desferoxamine concentration based on titration carried out by authors or based on previous publications?  Optical density at time of sampling is presented in Results.
Validity of the findings: The combination of transcriptomics, proteomics and metabolomics are presented and analysed individually rather than integratively.  The authors have previously carried out integration of proteomics and metabolomics data in a separate studiy with S. pneumoniae (Mitsuwan et al.,2017) and this could be a basis to extent interpretation in this manuscript.
Conclusions are broad and based around the combined omics approach and the specific issue of iron limitation on S. pneumoniae.
As noted in “Experimental Design” section, standardisation is particularly important in omics experimentation.  Replicates for Controls and Test samples are included and these are indicated as “biological replicates”. Can the authors verify that ,in the context of this manuscript, this multiple cultures used as experimental replicates within each the omics studies.
Metabolomics data presentation (Supplementary Figure S5) draws attention to experimental reproducibility.  The PCA plot shows that Control replicates were closely spaced, all falling in to single quadrant in the plot of PC1 and PC3.  Why was PC3 selected rather than PC2 which would, presumably, account for a greater proportion of sample variability?  Regarding the three iron-limited samples, each one falls into distinct quadrants in the PCA plot, suggesting a large extent of within-experiment variation.  This variation presumably contributed to low numbers of consistently assigned metabolites.  The authors should consider further the value of these analyses.
Discussion and Conclusions should take into account recent publications on proteomics and metabolomics of S. pneumoniae under distinct iron limitation conditions [Hoyer et al., 2018; Leonard et al., 2018] to broaden relevance.
Much of the Discussion is speculative in regard of function relevance of observed changes in transcript/protein/metabolite levels.  The final sentence in Introduction states the “[this study] may help to identify pathways or biomolecules that can be used as targets for therapies against pneumococcal infection” and this should be revisited towards end of Discussion.
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: MULTI-OMIC PROFILING TO ASSESS THE EFFECT OF IRON STARVATION IN STREPTOCOCCUS PNEUMONIAE TIGR4
Review round: 2
Reviewer: 1

Output:
Basic reporting: na
Experimental design: na
Validity of the findings: na
Additional comments: The reviewer has no further comments. The authors have adequately responded to the comments of the reviewers and improved significantly the manuscript.


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

Input:
Title: MULTI-OMIC PROFILING TO ASSESS THE EFFECT OF IRON STARVATION IN STREPTOCOCCUS PNEUMONIAE TIGR4
Review round: 2
Reviewer: 2

Output:
Basic reporting: No additional comments.
Experimental design: No additional comment.
Validity of the findings: The variability in metabolomics results remains a concern although not subject to over-interpretation.
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: SUITABLE OASIS SCALES UNDER A GOVERNMENT PLAN IN THE KAIDU-KONQI RIVER BASIN OF NORTHWEST ARID REGION, CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1、	line108—109： Temperature, precipitation and solar shortwave radiation are collected, but no contribution to the study is seen in the paper.
2、	Line109: Precision of data fusion ALOS with ETM should be 2.5m, not 30m?
3、	Line 123-131:The river basin and its relationships are not clear，the water balance is convenient to be calculated. The color of the map is not standardized.
4、	Line 125：The total area of the Kaidu-Konqi River Basin is different Line 90 , line 125-126.
5、	Line158: In figure 1, recommend you supplementary main river system and basin boundary; adjust color of various area; “Kaidu River Basin” doesn’t exhibit; account for empty patch in main figure; Scale unit adjusted to km.
6、	Line154: The water balance calculation in the study area is based on the land use data, but the imaging time, pretreatment process, classification method and classification accuracy of the remote sensing image are not explained.
7、	line156—157: 109 lines refer to ALOS data , 382 lines refer to the use of ALOS to obtain natural oasis area ( land use ) , which is 2.5 m after ALOS data fusion , but the 30m data referred to here is used to obtain land use . please account for The data sources of land use .
8、	Line164: The highest version of ArcGIS is 10.5, currently.
Experimental design: 9、	P168—170 the land use classification of USGS is simply introduced. How to merge it into the natural oasis and the artificial oasis?
10、	line171 : Since the study area is not of this type , the types of land use should be 6 .
11、P175  please replenish the information of spatial data projection.For the study area, the area data is very important. Based on the area error, the projection of spatial data is reconsidered.
11、	line190: The relationship between Kaidu - Konqi River Basin , Yanqi Basin and Konqi River Basin is unclear in the discussion of Figure 1 , and is suggested to be identified in Figure 1 .
12、	P204-205 This assumption is not seem realistic
13、	Line 229-230：In the calculation of hydraulic balance in 2020 and 2030, the area of oasis, groundwater depth,  ,social economic data, the natural vegetation water demand, artificial oasis water demand as a constant，why？
15. P228-229 The size of artificial oasis mostly depends on socioeconomic data. We should emphasize human activity factors. Assuming that 2013-2030 years of socio-economic data remain unchanged, it means to weaken human activities .
16  lineP254—255 The ecological water demand quota method is too simplified for ecological water demand , and the result maybe not determined . It is suggested that crop transpiration water consumption model should be used to calculate the ecological water demand .
17、lineP257: what is mean of each letter in the formula?
Validity of the findings: 18、line273-274: Artificial oasis uses unified quota calculation, ignoring the difference of different crops, increasing the uncertainty of the results. According to the relevant studies, the salinization phenomenon is more prominent in the study area, the local government is used to irrigate and
19、line427-429：why is the results of remote sensing images much larger than the results of Chen, please explain.
20、increase the water consumption of Salt discharge.
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: SUITABLE OASIS SCALES UNDER A GOVERNMENT PLAN IN THE KAIDU-KONQI RIVER BASIN OF NORTHWEST ARID REGION, CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: please see the General comments for the author.
Experimental design: please see the General comments for the author.
Validity of the findings: please see the General comments for the author.
Additional comments: The writting of this paper is very poor. There are many errors.
The methods to determine the suitable or optimal oasis area do not have robust physical base.
I don't think the current form shows contributions to the community as the methods are not novel and the results can not supported by the data.

1.The equation (7) is wrong, please carefully check the wording in the citation, especially the location of this item “10-5”. I do not agree with this formula, the reason is as follows: “Ep is the phreatic evaporation from construction land in an artificial oasis”, as I know the phreatic evaporation you used in your text (equation (11)) is the vegetation water use, not the construction land water use. And you had just classified the land use/cover into six types including the forest land, grassland, water, residence site, cultivated land and unused land. Did you mean that the construction land was the residence site? You also mentioned that “AA is the area of an artificial oasis”, however, I thought AA was the area of cultivated land, where you had mentioned above that artificial land included cultivated land and residence site, and you had already omitted the industrial and domestic water uses in the numerator of the equation (7).

2.Line 15, “and weather and socioeconomic data, suitable scales of oases were analyzed.” However, I did not the find the detailed weather data, except the introduction in the study region. Please add one figure about the detailed weather data, or just rewrite this sentence.

3.Line 251, The equation (6) is wrong, please add ∑ in the right side of the formula, and check carefully.

4.Line 259, the water quota of natural vegetation was 2250 m3 hm-2, therefore, the water quota was 225 mm, however, in Line 287, the water demand quota of the natural oases was 400 mm. Please unify the water quota. Similarly, water demand quota of the artificial oases was not unified.

5.Line 302, In the cited reference, the A was the optimal area of a natural oasis, however, in your text, you had changed to the optimal area of an oasis, and you used the same equation as the cited reference. Please check it carefully.

6.Line 475, “natural oasis occupies 60%, and artificial oasis occupies 40%”, however, the proportion of natural oasis and artificial oasis in Table 2 was not the rate.


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: SUITABLE OASIS SCALES UNDER A GOVERNMENT PLAN IN THE KAIDU-KONQI RIVER BASIN OF NORTHWEST ARID REGION, CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: please see the comments for the author.
Experimental design: please see the comments for the author.
Validity of the findings: please see the comments for the author.
Additional comments: The revised version improved much. All my comments have been addressed well.


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: FIRST USE OF MOLECULAR EVIDENCE TO MATCH SEXES IN THE MONSTRILLOIDA (CRUSTACEA: COPEPODA), AND TAXONOMIC IMPLICATIONS OF THE NEWLY RECOGNIZED AND DESCRIBED, PARTLY MAEMONSTRILLA-LIKE FEMALES OF MONSTRILLOPSIS LONGILOBATA LEE, KIM & CHANG, 2016
Review round: 1
Reviewer: 1

Output:
Basic reporting: This work responds to a need in the taxonomy of monstrilloid copepods that has been repeatedly advanced for many years (Suárez-Morales, 1994, 2005, 2011, 2017), i.e., linking males and females of species by molecular techniques.
The manuscript is very well written, Illustrations are very good, including high-quality line drawings, good half-tone photos and SEM micrographs (SEM-analyzed specimens are remarkably well processed as there is little or no contraction of the cephalothorax cuticle after processing. The taxonomic description is complete and accurate; the characters found in these  females are also remarkable, like the interesting, unique postero-ventral process of the genital double-somite, clearly identified and outlined in this work..
Experimental design: The unresolved issues presented in this ms and the lack of alternative explanations (even a moderate speculation) for these questions is my main criticism. The manuscript is  well written,  authors acknowledged the  advice by Dr. Mark J. Grygier, who polished the English text. Illustrations are very good, including high-quality line drawings, good half-tone photos and SEM micrographs (specimens are remarkably well processed as there is little or no contraction of the cephalothorax cuticle after SEM processing. The description is complete and accurate, it follows the highest current standards in copepod taxonomy.
Validity of the findings: Authors opened the discussion about the uncertain status of Maemonstrilla as a valid taxon and suggest that more  molecular data will be needed to define thisMonstrillopsis/Maemonstrilla dichotomy It is true that the finding and analysis of Maemonstrilla males will shed more light on the status of these two genera and their relations. Somehow the position they support in this work (i.e.recognizing that minor characters are not enough to link males and females (lines 797-797) contradicts the criteria used elsewhere (Jeon et al., 2018)where a similar set of microcharacters(i.e.,integumental ornamentation, pore /sensilla patterns) was deemed enough morphologic evidence as to establish a new genus of the Monstrilloida. Authors should decide if, based on their exploration of microcharacters among the monstrilloid copepods, these are enough to separate species, genera or link males and females.
Additional comments: An interesting, straightforward contribution that probably generates more questions than answers. Molecules are good tools, but comparative morphology is probably the main source to reach a solid classification within the group, which is clearly more complex than previously thought.The lack of appendages in these copepods hampers the exploration of homologies and the current limitations of molecular techniques will likely conceal their true phylogenetic links for some time.The evidence presented here is solid and well supported by data from different sources; a nice, professional work.


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

Input:
Title: FIRST USE OF MOLECULAR EVIDENCE TO MATCH SEXES IN THE MONSTRILLOIDA (CRUSTACEA: COPEPODA), AND TAXONOMIC IMPLICATIONS OF THE NEWLY RECOGNIZED AND DESCRIBED, PARTLY MAEMONSTRILLA-LIKE FEMALES OF MONSTRILLOPSIS LONGILOBATA LEE, KIM & CHANG, 2016
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written, clear and with sufficient context provided. I did enjoy reading the manuscript.

Very straightforward, I have only minor comments.
Experimental design: The experimental design is correct.
Validity of the findings: Data supports conclusions.
Additional comments: Please review (find and replace) M. longilobata by Mn. longilobata in Conclusion. Authors indicate that Monstrillopsis would be Mn. But then break the rule in Conclusion.

When citing support for COI species assignment, they do not cite Blanco-Bercial et al. (2014). It is OK to choose which citations to use for all authors, but this is the most extensive work to date on COI assignment on Copepods.

For the ITS region(s) including 5.8S, authors might want to check Bradford-Grieve et al. (2017). The regions are split, but 5.8s resulted completely conserved in all cases.

In line 719 (“A phylogenetic systematic evaluation…”) might appreciate the clarification that refers to morphology only.

Line 77: “much nucleotide sequence data has” should read “much nucleotide sequence data have”. Data is plural.

Line 178: correct Matercycler to Mastercycler

Blanco-Bercial L, Cornils A, Copley N, Bucklin A (2014) DNA Barcoding of marine copepods: assessment of analytical approaches to species identification. PLOS Currents Tree of Life Edition 1.

Bradford-Grieve JM, Blanco-Bercial L, Boxshall GA (2017) Revision of Family Megacalanidae (Copepoda: Calanoida). Zootaxa 4229, 183.


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: FIRST USE OF MOLECULAR EVIDENCE TO MATCH SEXES IN THE MONSTRILLOIDA (CRUSTACEA: COPEPODA), AND TAXONOMIC IMPLICATIONS OF THE NEWLY RECOGNIZED AND DESCRIBED, PARTLY MAEMONSTRILLA-LIKE FEMALES OF MONSTRILLOPSIS LONGILOBATA LEE, KIM & CHANG, 2016
Review round: 1
Reviewer: 3

Output:
Basic reporting: The Introduction and the Material and Methods show context. Some updates were suggested in the introduction (e.g. lines 54-59).
In the Systematic, the diagnosis is well detailed and described all the taxonomic characterists. The authors could make better use of the figures. In the female and male diagnosis, several taxonomic characteristic was not represented by figures, which are cited only in the description of the sexes (lines 262-313).
In the Molecular Analysis (lines 550-560), was suggested the use of a figure or table in order to illustrate the results.
The literature was well referenced, and the references were relevant. However, the references should be reviewed. There are references that was not cited, and reference that was not listed.
Figures are relevant and with high quality. Some suggestions were made in the labels.
The supplemental material is significantly and relevant.
Experimental design: Research question well defined, relevant and meaningful. The research fills an identified knowledge gap. Methods described with sufficient detail and informations.
Validity of the findings: One novelty is the proposal for the revised nomenclature for antennular setal armament.
The discussion was well substantiated, and the conclusions were according to the objectives.
Additional comments: The main proposals of the authors is demonstrate the conspecificity of individuals of the two sexes of  Monstrillopsis longilobata by using both morphological and molecular evidence, and present proposal for the antennular nomenclature explaining the general setal patterns by each sex. The topic is relevant and the purpose of the authors is remarkable. The authors made a meticulous work in relation to the description of taxonomic characters, and they made comparisons with the other known congeners of Monstrillopsis There are, however, some points that the authors should address in order to produce a better version of this manuscript. My principal comments and suggestions are in the pdf file.


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: TACKLING CRITICAL PARAMETERS IN METAZOAN META-BARCODING EXPERIMENTS: A PRELIMINARY STUDY BASED ON COXI DNA BARCODE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Belech et al.  developed a new pipeline HSTA  (Hidden States Taxa Assign) for DNA meta-barconding.Moreover, the authors evaluated the influence of universal primers amplification bias and the correlation between GC content with taxonomic assignment accuracy.
Due to the importance that meta-barcoding is assuming in ecology, biodiversity description and conservation, these kind of study are very welcome.
I found the manuscript clear and well written. Title and abstract reflect the content. Introduction is exhaustive and methodology and results clearly described making the paper understandable also by research without particular bioinformatic skills.
Experimental design: The research fits with the aims of the journal.
The research question is clear and meaningful.
The methods used are well described
Validity of the findings: A comparative benchmark, carried out by using  a “true” case study (community of terrestrial invertebrates) shows how  the HSTA greatly improve the accuracy over other commonly used taxonomic assignment pipelines.
Lastly, the results highlight the necessity to evaluate the effect of GC content and universal primer set in any DNA meta-barcoding experiment.
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: TACKLING CRITICAL PARAMETERS IN METAZOAN META-BARCODING EXPERIMENTS: A PRELIMINARY STUDY BASED ON COXI DNA BARCODE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Balech et al. investigate the impact of critical steps in the processing of amplicon data using the marker gene coxI which is commonly employed for meta-barcoding of animal populations. In particular, they have established a new approach for taxonomic classification and quantify their performance on mock community data and compare it with other established pipelines. Although the idea of using HMMs for classification of short sequencing reads is hardly a novel development, it is commendable that Balech and co-workers attempt to explore the effect of critical parameters in the assessment of taxonomic profiles using coxI, a question that has not been rigorously explored so far. I also found the manuscript to be well written and clearly accessible. I have however some concerns about the experiments performed that the authors should address, as well as relatively few remaining minor points.
Experimental design: 1. As far as I understand, there is no replication in the mock community sequencing. This is clearly insufficient. At the very least technical replication is necessary to robustly assess whether the differences in performance are significant or comparable to the variability between replicates.

2. The authors build a custom database from sequences found in the actual samples and compare their method with de novo OTU picking algorithms. This is not entirely fair as it would be more appropriate to use for instance a reference-based algorithm as well such USEARCH-ref (Edgar 2013) with the same custom database (which would bypass the need of a taxonomic classifier such as RDP).

3. Similarly, the authors should compare multiple taxonomic classification algorithms and not only RDP.
Validity of the findings: 4. An additional way to validate their approach would consist in retrieving published datasets and analyze them using the various pipelines. It would be relevant to see how large the resulting differences are and which methods consistently give similar results, etc. It would be possible to obtain OTU tables from various reference-based algorithms and for instance analyze their diversity using Bray-Curtis / UniFrac and PCoA, etc.
Additional comments: 5. I find Fig. 1 somewhat confusing. For example, it is not clear to me if the Sanger sequences (LocaDB) are also included in the reference DB (CDS Reference Seq DB) used for the RDP classifier. I suggest the authors improve the current version for clarity and provide a more detailed description in the methods text or legend.

6. I found no link to the implementation of their approach. Since this study presents a computational method for analyzing data it seems desirable to be able to make it available for other groups to use besides necessary to ensure replicability of the results. Similarly, I did not find a link to a public repository where the data was deposited.


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: TACKLING CRITICAL PARAMETERS IN METAZOAN META-BARCODING EXPERIMENTS: A PRELIMINARY STUDY BASED ON COXI DNA BARCODE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Unfortunately I have to persist in my previous comment concerning the lack of biological or technical replicates. Although I commend the effort the authors have put into this study I cannot recommend the manuscript for publication given this lack of replication.


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: SURFACE ELECTROMYOGRAPHIC ANALYSIS OF DIFFERENTIAL EFFECTS IN KETTLEBELL CARRIES FOR THE SERRATUS ANTERIOR MUSCLES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Line 28 - A reference here detailing how upward rotation maintains subacromial space and prevents rotator cuff impingement.  A decrease in subacromial space and rotator cuff impingement may be caused by many factors including, but not exclusive to scapular upward rotation.
Line 38 - This is the first mention of the term "overhead stabilizers".  It would be good to better define this earlier as it presents a little confusion for the reader.  Previous mentions serratus anterior actions as upward rotation or scapular stabilization.
Lines 49-57 -These lines highlight the concerns/limitations of EMG.  Potential limitations of measuring apparatus are typically seen in the Discussion section.
Line 47 -If there are any references highlighting the validity of EMG and serratus, it would be good to mention them here.  If not the serratus specifically, then another scapular stabilizer perhaps?
Experimental design: Line 66 - Any exclusion criteria include past medical history (i.e. history of rotator cuff impingement, shoulder surgery, etc.)  Any previous history may effect results.

Line 73 - How were the subjects randomized?  If the study is to be replicated, then specifics on randomization should be included.

Line 91 - How long between each trial?

Line 97 - Why was 25 lbs of the kettlebell and 30 yards distance chosen?
Validity of the findings: Line 149 - Is the line supposed to read:  8 had a large effect vs. 8 had a large difference?  The rest of the sentence discusses "effect".

Line 202 - There is confusion here.  There is listed the 2003 as submaximal voluntary dynamic contraction (SVDC) of the exercises vs the submaximal voluntary dynamic contraction (SVIC) movements.-----I am unsure of the difference here?  Possible grammatical error?

I always like a sentence or two referring to clinical implications of the study.  Is there a clinical implication that can be drawn from this study?
Additional comments: Great work here!  Thanks for the opportunity to review.


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: SURFACE ELECTROMYOGRAPHIC ANALYSIS OF DIFFERENTIAL EFFECTS IN KETTLEBELL CARRIES FOR THE SERRATUS ANTERIOR MUSCLES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This article is, on the whole, well written in an understandable manner; however, minor proofreading and revision may be needed at lines 29-31, 208-211.

Regarding potential influences on EMG activity readings, I feel that a reference should be cited at the end of lines 48-52; however, if the Kuriki article cited in line 53 addresses these concerns, a simple re-wording of the sentence would suffice.
Experimental design: Well designed experiment.  For clarification, what is the rationale for performing the protocol post-throwing?  Would discussion of potential decrease in MVIC due to potential fatigue be warranted, as well as directing potential future investigation to include assessing throwing athletes in a "fresh" state?

Regarding protocol, I believe it would be beneficial to include the specified rest time prior to performing each trial; while neuromuscular fatigue is not uniform across the population, this would give some indicator of potential fatigue influencing repeated trials for the study design.
Validity of the findings: Data appears to be well collected and analyzed.

Regarding the conclusion, I feel that it may be necessary to narrow the scope of the conclusion statement, regarding adult male throwers.
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: SURFACE ELECTROMYOGRAPHIC ANALYSIS OF DIFFERENTIAL EFFECTS IN KETTLEBELL CARRIES FOR THE SERRATUS ANTERIOR MUSCLES
Review round: 1
Reviewer: 3

Output:
Basic reporting: Abstract:

Line 12: write out electromyography (EMG) the first time you use it in abstract
line 14: change "roughly college age" to "men ages xx-xx"
line 14: change to "professional baseball pitchers";
line 16: remove "after a brief break" since you explain that in next sentence.
lines 21-25: for clarity, i would include "EMG amplitude" or "EMG signal" into those sentences when talking about the results.

Introduction:

Overall well written and succinct.  Nicely illustrates the background and reason for the study. I would recommend moving the purpose followed by the hypothesis to the end of the introduction.

Line 32: do people specifically use it for “recovery”?  I would consider removing that word if possible. (if recovery is removed consider modification to line 46 as well)
Line 33-34: Change to “ When performed with correct technique, kettlebell carries…”
Line 35: remove “often”
Line 42: I would refer to figure 4 and 5  to illustrate the positions. Figures will need to be renumbered if this change is made.

Methods:

I would move line 69-70 on IRB approval to first sentence of this section. move consent info found in lines 67-69 to second sentence.
Please use consistent horizontal shoulder abduction angles in relation to each other. Try to clarify what zero degrees is. At times 45 is used but at other times 90 degrees and 125 degrees. I typically think of the arm forward flexed to be zero degree and figure 5 to be 90 degrees.
Line 60: add city,state of driveline baseball
Line 72: change “ask” to “recruited”
Line 73: discuss method of randomization
Line 87-88: please clarify the description in figure 2 and 3 to better reflect what is occurring in the picture

Statistical analysis

Nice work explaining this section and how filters are applied.

Results

Clearly written.
Line 171-175 – I would recommend 3 significant digits for P values

Discussion

Nice opening paragraph restating purpose and your most important findings.
Line 196 – change “this study” to “it” as it appears you are referring to the ekstrom study
line 211-213 – I would reword or remove “especially pertinent in nature because of fickle behavior of EMG
Experimental design: Well designed project with purpose and method clearly stated.  Study would be easy to replicate because of detail within this paper.
Validity of the findings: This is an exercise that is widely done but the exact arm position to activate the serratus anterior has not been well established previously.  These findings begin to help the understanding of what muscles are being trained with this kettlebell exercise.
Additional comments: Well done study!  Excited to see more of this type of research from your research group!


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: SURFACE ELECTROMYOGRAPHIC ANALYSIS OF DIFFERENTIAL EFFECTS IN KETTLEBELL CARRIES FOR THE SERRATUS ANTERIOR MUSCLES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No Comment
Experimental design: No Comment
Validity of the findings: No Comment
Additional comments: Great work!  Looking forward to more follow-ups on this topic.


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: SURFACE ELECTROMYOGRAPHIC ANALYSIS OF DIFFERENTIAL EFFECTS IN KETTLEBELL CARRIES FOR THE SERRATUS ANTERIOR MUSCLES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Well done.  Rephrasing this section addressed previous concerns.
Experimental design: Concerns were addressed well in this section.  Regarding line 116, phrasing "around" as "approximately" or "as near to 30 seconds as possible" may aid future investigators in repeating the procedures by limiting ambiguity.
Validity of the findings: Well done study.
Additional comments: Thank you for the opportunity to review this manuscript and I look forward to seeing more data from your group in the future.


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

Input:
Title: SURFACE ELECTROMYOGRAPHIC ANALYSIS OF DIFFERENTIAL EFFECTS IN KETTLEBELL CARRIES FOR THE SERRATUS ANTERIOR MUSCLES
Review round: 2
Reviewer: 3

Output:
Basic reporting: all my concerns were addressed. looks great!
Experimental design: all my concerns were addressed. looks great!
Validity of the findings: all my concerns were addressed. looks great!
Additional comments: all my concerns were addressed. looks great!


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 RESTORATION OF THE ENDANGERED SAMBUCUS PALMENSIS AFTER 30 YEARS OF CONSERVATION ACTIONS IN THE GARAJONAY NATIONAL PARK: GENETIC ASSESSMENT AND NICHE MODELING
Review round: 1
Reviewer: 1

Output:
Basic reporting: Abstract
L21: Please delete “resolution”

Intro
L53-55. Whittaker & Fernandez-Palacios (2007) is a very general reference. Maybe think about using more specific references such as Caujapé-Castells et al. (2010) here instead. Also, a future threat for range-restricted endemic species on islands might be climate change (see e.g. Harter et al. 2015). This could be mentioned here.

Caujapé-Castells, J., Tye, A., Crawford, D. J., Santos-Guerra, A., Sakai, A., Beaver, K., Lobin, W., Florens, V. F. B., Moura, M., Jardim, R., Gómes, I. & Kueffer, C. (2010) Conservation of oceanic island floras: present and future global challenges. Perspectives in Plant Ecology, Evolution and Systematics, 12, 107-129.

Harter, D. E. V., Irl, S. D. H., Seo, B., Steinbauer, M. J., Gillespie, R., Triantis, K. A., Fernández-Palacios, J. M. & Beierkuhnlein, C. (2015) Impacts of global climate change on the floras of oceanic islands - projections, implications and current knowledge. Perspectives in Plant Ecology, Evolution and Systematics, 17, 160-183.

L66-76. I think this section (describing the study species) belongs in the methods with a separate heading (“Study species”).

L66-68. Please give a reference for this statement.

L83 “recent bottleneck”. What kind of bottleneck do you mean? A genetic bottleneck? Please be more specific here because this could mean multiple things.

L90-93. Out of interest: It seems like disturbances (such as fire) increase the reproduction success of S. palmensis. Would this be a possible conservation approach for future conservation efforts to increase the genetic diversity of the populations?

Figures
As you’re only dealing with a single species, I think one (or several) pictures if S.p. would help to visualize what kind of species it is and what sort of habitat it occupies. This could be included into Fig. 1.

Fig1.
Inlay A. Most people won’t know where or what La Gomera is. I would suggest to include a map of the North Atlantic and Canary Islands to precisely locate where the island lies.
Also, is it necessary to show other protected areas besides the national park? As far as I recall the other PAs are not mentioned in the MS and all these colors make things confusing.

Fig2.
Maybe considering adding a simple plot of the temperature and precipitation values of all natural and reintroduced individuals. You could draw convex hulls around their distributions to visualize the differences between natural and reintroduced. Or is this meant by 2a? However, from the caption and the figure it is not clear what the PCoA is showing and what the axes mean.

Fig3.
“Countor lines” I can’t see any counter lines in the maps. They are obviously too thin or the maps too small.
“whether the species is present or not”. SDMs do not show presence or absence of species. They show the environmental suitability.
3b). I was wondering why the SDM of all occurrences shows a smaller and more confined distribution than the subset only using reintroduced occurrences. This seems weird to me and is totally counterintuitive. Wouldn’t a larger set of occurrences with a wider environmental distribution lead to a larger area of suitability? Can you verify that this map is correct? If yes, can you discuss this issue in the discussion?

In general, all labels are too small in Fig3. Please increase label size! Also, choosing red and green as colors for the points of reintroduced and natural occurrences does not make sense, if your suitability map also includes red and green (in addition, 10% of men are colorblind with regard to red/green!). I cannot recognize the green points on the map. Maybe it would be better to have a regular digital elevation model (or something similar) to show the points and leave out the points in the SDM maps. These four maps could be combined to a 2x2 panel making all of the maps bigger in the final publication.
Experimental design: Material and methods
L114. “localities”. I think what you mean here is “sites”. I assume that you are using the direct translation from Spanish “localidades” but this does not sound right in English. Please check this throughout the MS.

L208. “projected TO La Gomera island”

L216. “402 presence cells”. As far as I understand you only use occurrence data from La Gomera, although the species has a wider distribution (Tenerife, La Palma, Gran Canaria) to model the distribution of S.p., right? This might lead to a truncation of the species’ distribution (by ignoring the distribution of S.p. on other islands which could differ in environmental conditions than the occurrences on La Gomera). This might result in a biased (or skewed) SDM because not the full niche of the species is considered. Is data from other islands available to model the complete distribution of S.p.? I assume the Atlantis database has a too coarse resolution for your approach. If additional data is not available, could you at least discuss this issue in the discussion. You already mention possible truncations there and I think this aspect should be mentioned as well.

Results
L283. Better write “we found two possible best values for K according…”

L316-318. Sentence unclear. Please rephrase!
Validity of the findings: Discussion
In general the discussion is very Canary-centric! To draw interest of a wider readership, I suggest to broaden the discussion by also using literature from other regions, at least from other archipelagos that encounter similar issues.

L325. “or high mortality rates of young plants” Does this have to do with introduced herbivores? Introduced herbivores selectively browse juvenile endemics because they are most palatable to them. If yes, you could expand on this issue, e.g. by citing the large body of literature that exists for the Canary Islands:

Cubas, J., Martín-Esquivel, J. L., Nogales, M., Irl, S. D. H., Hernández-Hernández, R., López-Darias, M., ... & González-Mancebo, J. M. (2017). Contrasting effects of invasive rabbits on endemic plants driving vegetation change in a subtropical alpine insular environment. Biological Invasions, 1-15.

Irl, S. D. H., Steinbauer, M. J., Messinger, J., Blume-Werry, G., Palomares-Martínez, Á., Beierkuhnlein, C., & Jentsch, A. (2014). Burned and devoured-introduced herbivores, fire, and the endemic flora of the high-elevation ecosystem on La Palma, Canary Islands. Arctic, antarctic, and alpine research, 46(4), 859-869.

Garzón-Machado, V., González-Mancebo, J. M., Palomares-Martínez, A., Acevedo-Rodríguez, A., Fernández-Palacios, J. M., Del-Arco-Aguilar, M., & Pérez-de-Paz, P. L. (2010). Strong negative effect of alien herbivores on endemic legumes of the Canary pine forest. Biological Conservation, 143(11), 2685-2694.

Irl, S. D. H., Steinbauer, M. J., Babel, W., Beierkuhnlein, C., Blume‐Werry, G., Messinger, J., ... & Jentsch, A. (2012). An 11‐yr exclosure experiment in a high‐elevation island ecosystem: introduced herbivore impact on shrub species richness, seedling recruitment and population dynamics. Journal of Vegetation Science, 23(6), 1114-1125.

L410ff. “Recommendations for conservation actions” Although I like this section and it offers some good suggestions and direct support for conservation, I somewhat miss a discussion on how protected areas are able to conserve and restore rare endemics. For example, a recent study from La Palma showed that protected areas generally harbor more rare endemics than non-protected areas (Irl et al. 2017). You could test, for example, how much of the suitable area calculated by the SDM lies within and without of protected areas to see if conservation goals are realistic or not.

Irl, S. D.H., Schweiger, A. H., Medina, F. M., Fernández‐Palacios, J. M., Harter, D. E.V., Jentsch, A., ... & Beierkuhnlein, C. (2017). An island view of endemic rarity—Environmental drivers and consequences for nature conservation. Diversity and Distributions, 23(10), 1132-1142.
Additional comments: Rodriguez-Rodriguez et al. et al. present an interesting study on the restoration of a highly endangered tree species from the Canary laurel forest (Sambucus palmensis) using a population genetics as well as a species distribution approach on the island of La Gomera. They analyze natural and restored populations, model the environmental niche of the species to assist conservation and extract some very concrete information for future conservation/restoration efforts (by providing a list of candidate individuals for future cuttings). All in all, I like the combination of modern techniques to assist ongoing conservation/restoration efforts. However, I have some issues that should be clarified before proceeding to publication. I hope you find my comments helpful, however I have to state that I’m not an expert on population genetics so I cannot comment this part (especially the methods).


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 RESTORATION OF THE ENDANGERED SAMBUCUS PALMENSIS AFTER 30 YEARS OF CONSERVATION ACTIONS IN THE GARAJONAY NATIONAL PARK: GENETIC ASSESSMENT AND NICHE MODELING
Review round: 1
Reviewer: 2

Output:
Basic reporting: Rodriguez-Rodriguez and colleagues performed a population genetics analysis to infer the genetic diversity of one of the most endangered Canary island endemic plants, Sambucus palmensis, on the island of La Gomera. This plant species has been target species of conservation management for the past 30 years, however, the management mostly consisted of vegetative propagation of a few individuals, leading to concerns that there could be a serious risk of genetic impoverishment and inbreeding, eventually leading to the extinction of the species. The sampling included all 402 individual plants known in the wild on La Gomera (47 natural and 355 planted). Analysis of seven microsat regions revealed indeed a high proportion of clones but there is still a relatively high genetic diversity in the total population, which can be used - in combination with niche modelling results - for planning of future management strategies.
The study is well structured and written in good English. The introduction is adequate and gives sufficient background for the general readership of PeerJ. The only information I could not find is an estimate of the total number of individuals of Sambucus palmensis in the wild (all four islands). The figures are fine but again, I would prefer a distribution map including all four islands, instead of only La Gomera. All the raw data seems to be available, but I could not find a research permit number, even though most (all?) of the study was performed in a protected area, where such permits are certainly required. Please add this important information.
Experimental design: The authors report original primary research addressing an interesting question: can we maintain small populations of endemic plants even if we have to rely mostly on vegetative propagation. This is a pressing question on islands like the Canaries, where a lot of time and money is invested in such programs. The methods are described in sufficient detail and seem adequate. The only surprise to me is that no material from the other three islands with Sambucus palmensis populations (La Palma, Tenerife, Gran Canaria) was included, even though Tenerife and La Palma populations were already focus of a previous study (Sosa et al. 2010). Since it seems to be very rare on those other islands, this should be an easy task (in terms of additional samples) and would make the study much more comprehensive and meaningful. With samples from all islands, we would know the genetic diversity of the species as a whole (not only the La Gomera population), it would be possible to compare values between islands and most importantly, the species distribution modelling would make much more sense.
Validity of the findings: The findings are robust and discussed in a meaningful way. The suggestions for the species management, especially the list of individuals to be used for propagation, will be very useful for the Garajonay National Park staff. However, they will not be very useful for management of the S. palmensis populations on the other islands and we cannot infer, how useful (or not) it could be to transfer plants between islands.
Additional comments: In general, this is a nice and useful study. However, in my opinion, a more comprehensive sampling with Sambucus palmenis individuals from all 4 islands would be much more interesting for the broader island biology community. Focussing on La Gomera alone seems a bit strange to me and doesn't give us the big picture needed for a really holistic approach to long term management of the species.
I don't know how much additional effort would be needed to include those other populations (and how many individuals there are on the other islands, Gran Canaria only 2, Tenerife: ?, La Palma: ?) but the study would definitely benefit a lot.


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: BIOMECHANICAL EVIDENCE SUGGESTS EXTENSIVE EGGSHELL THINNING DURING INCUBATION IN THE SANAGASTA TITANOSAUR DINOSAURS
Review round: 1
Reviewer: 1

Output:
Basic reporting: see General comments for the author
Experimental design: see General comments for the author
Validity of the findings: see General comments for the author
Additional comments: Review of “Biomechanics suggests extensive eggshell thinning during incubation in a titanosaur dinosaur” by Hechenleitner et al.

This paper suggests that eggshells of titanosaur dinosaurs would have been through the process of dissolution during incubation based on mechanical analyses of the unusually thick eggshells. The main idea is clear and makes good sense. The paper is, in general, well-written, and the results are interesting. However, the following questions and concerns should be addressed before it may be considered for publication in PeerJ.

1.	The main results of this paper are based on biomechanics; more details about the mechanical analyses should be provided. For example, what element types and meshes were used in the finite element analysis? How was the angle for the boundary conditions determined? An important assumption used in the present study is that the eggshell breaks when the displacement at the load point equals the thickness. Juang et al. reported in a recent paper that the eggshells of many avian species fractured at a displacement to thickness ratio of about 0.3 (see Fig. 5(b) in Juang et al “The avian egg exhibits general allometric invariances in mechanical design," Scientific Reports, 7, 14205, Oct. 2017). This ratio varies with species and almost all eggshells fractured when it reaches one. Although the actual ratio may vary with species, I agree that a ratio = 1 may be used as a simplified criteria to determine the fracture force. However, I suggest the authors to cite the above-mentioned reference and to elaborate a little more on this.

2.	Some megapodes species, such as Macrocephalon maleo, also use burrow nesting with vegetal decomposition, solar radiation and/or geothermalism as incubating strategies. (see the corresponding author’ earlier work PeerJ 3:e1341, 2015). However, Maleo’s eggshell thickness is very thin, compared to that of other species with similar egg weight (Maleo: thickness = 0.38 mm, egg weight = 222 g, and Grus Antigone: thickness = 0.61 mm, egg weight = 217 g, see Juang et al. Scientific Reports, 7, 14205, Oct. 2017). If thick shell was an adaptation to geothermal environment, why did not Megapodes evolve thicker shells similar to the Sanagasta eggs, but, on the contrary, evolve a much thinner shell even thinner than “normal” avian ones?

3.	What does “The new results” in line 169 mean? How do they reinforce the idea that the eggs of all titanosaurs were spherical? The connection between the current research and the reference studies should be elaborated more for the reader to understand what the authors are trying to convey from the text itself.

4.	Please consider improving some phrasing for readers to comprehend more easily. For example, lines 40-42, 68-71, 74-76, 109-112, and 225-226. Also, more description should be provided for Figure 3. What does the numbering of the red dots mean? The explanation for Figure 3 in the Results section is not easy to understand, either. The data sources and the number of samples should be included in Table 1.


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: BIOMECHANICAL EVIDENCE SUGGESTS EXTENSIVE EGGSHELL THINNING DURING INCUBATION IN THE SANAGASTA TITANOSAUR DINOSAURS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The present manuscript (Ms. Ref. No. #24881) presents the results from investigations of the Biomechanics suggests extensive eggshell thinning during incubation in a titanosaur dinosaur. The article by Martín Hechenleitner et al. on biomechanics of a titanosaur dinosaur is well constructed and well presented. The wording and phrasing of the whole text is well written. The title of the paper is very informative.
All of the figures are relevant and are of high quality, well labelled and described.  The research question is well defined and is pertinent and important.  This research work fills the knowledge gap that how the thinning below 2 mm would have allowed these titanosaurs to hatch.
Experimental design: Normally the thickness of the titanosurid eggshells varies from 1.00-4.8 mm but the present record of thick eggshells from Sangasta locality of about 7.9 mm is quiet interesting and certainly helps for the nesting micro environments. The main aim of this manuscript is to test the mechanical implications of the thickest egg shells and how it pretentious the success of hatching. The authors have mentioned about the locality Auca Mahuevo in the abstract and text but not have clearly mentioned about the relation of these titanosaur eggs with newly erected Fusioolithus baghensis (Fernandez and Khosla, 2015) known from Late Cretaceous deposits of Argentina and India. This is the only titanosaurid egg which has the confirmed the presence of embryonic remains in the eggs from Argentina (Chiappe et al., 1998). In size, shape, micro and ultrastructiral studies indicates similarity between Late Cretaceous eggs of India and Argentina.  The introduction part needs to define in a more detail manner. The authors should write in detail some of the earlier important works of Simon (2006) who erected the oospecies Patagoolithus salitrlensis  and M. patagonicus  (Calvo et al., 2009). The work of Khosla and Sahni (1995); Vianey-Liaud et al. (2003); Salgado et al. (2007, 2009) and Fernandez (2013, 2016) is completely missing, which needs to be added.  I suggest that authors should start and improve the introduction description at lines 33- 42 to provide more justification for your study (specifically, you should expand upon the knowledge gap being filled). It is no where mentioned about the recent work on Indian and Argentinean dinosaur eggshells. The authors should also add that to date Argentinean titanosaurid eggshell parataxonomy has been revised by Fernandez and Khosla (2015) and has been restricted to five oospecies (Megaloolthus cylindricus, M. Jabalpurensis, M. megadermus, Fusioolithus baghensis and F. berthei, Fernandez and Khosla, 2015). The English language of at least two paragraphs should be enhanced to make certain that an international audience can obviously appreciate the present text. Some instance where the language could be enhanced includes lines 130-144. The current phrasing makes understanding complicated. The authors should add about how many number of samples they used for the present study in the methodology part. In order to make the manuscript more strong add the following references:
Ferna´ndez MS. 2013. Ana´lisis de ca´scaras de huevos de dinosaurios de la Formacio´n Allen, Creta´cico Superior de Rı´o Negro (Campaniano- Maastrichtiano): utilidades de los macrocaracteres de intere´s parataxono´mico. Ameghiniana. 50(1):79–97.
Fernandez and Khosla, A. 2015. Parataxonomic review of the Upper Cretaceous dinosaur eggshells belonging to the oofamily Megaloolithidae from India and Argentina. Historical Biology, 2015, Vol. 27, No. 2, 158–180.
Khosla A, Sahni A. 1995. Parataxonomic classification of Late Cretaceous dinosaur eggshells from India. J Paleontol Soc India. 40:87–102.
Salgado L, Coria RA, Ribeiro CM, Garrido A, Rogers R, Simo´n ME, Arcucci AB, Rogers KC, Carabajal AP, Apesteguı´a A, et al. 2007. Upper Cretaceous dinosaur nesting sites of Rı´o Negro (Salitral Ojo de Agua and Salinas de Trapalco´-Salitral de Santa Rosa), northern Patagonia, Argentina. Cretaceous Res. 28:392–404.
Salgado S, Ribeiro CM, Garcı´a RA, Ferna´ndez MS. 2009. Late Cretaceous Megaloolithid eggs from Salitral de Santa Rosa (Rı´o
Negro, Patagonia, Argentina): inferences on the titanosaurian reproductive biology. Ameghiniana. 46(4):605–620.
Simo´n ME. 2006. Ca´scaras de huevos de dinosaurios de la Formacio´n Allen (Campaniano-Maastrichtiano), en Salitral Moreno, provincia de Rı´o Negro, Argentina. Ameghiniana. 43(3):513–518.
Vianey-Liaud M, Khosla A, Garcı´a G. 2003. Relationships between European and Indian dinosaur egg and eggshells of the oofamily Megaloolithidae. J Vertebr Paleontol. 23(3):575–585.
Validity of the findings: The data provided in eggshell mechanical properties, egg morphology, statistical analysis and results are excellent. I suggest the authors to expand slightly the text of statistical part. It would be nice if the authors add more about hatching, paleoenvironments of these thick eggshells from Sanagasta. A separate paragraph about the paleoenvironmental and palaeoecological implications in the discussion part would make this manuscript strong and will be much appreciated by the international audience. In lines 235-237 the reference of Garcia et al. (2008, Paleovertebrata) should be added because they made comparative study between Megapodes and titanosaur eggs and their hatching patterns.  Overall the data used in this manuscript is vigorous, statistically sound, and controlled. The conclusions are well stated, linked to original research question and should add more about palaeoenvironments and comparative hatching pattern of Megapodes and titanosaur eggs.
Additional comments: The present manuscript  is well constructed, well presented and well written. The title of the paper is very informative. All of the figures are relevant and are of high quality, well labelled and described.  This seems to be a unique work on the biomechanics of the titanosaurid eggshells. I strongly recommend that the manuscript should be accepted after minor 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: BIOMECHANICAL EVIDENCE SUGGESTS EXTENSIVE EGGSHELL THINNING DURING INCUBATION IN THE SANAGASTA TITANOSAUR DINOSAURS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This  is a relatively short paper that purports to indicate that the particularly thick sauropod eggshells reported from one location are due to the nesting environment. They support a previous paper by using primarily FEA to suggest the eggshell was initially very thick and then etched by environmental acid to a thickness where the hatchling could hatch. I am not sure that there is much that is that novel in the study. This impression is reinforced by the lack of any real detailed description of the FEA methodology and there seems to be just an extrapolation of data from Hahn et al. to the larger dinosaur eggs.

Much more is needed to explain the methodology here to provide a sound context for the results.
Experimental design: The data seem to be based on single specimens (often a consequence of dealing with fossils) or from existing published data. The methodology was based primarily based on modelling the characteristics of the outline shape of the egg.

Given that this is an on-line journal it is unclear why any supplementary materials is required - surely methods and results could be included in the main paper.
Validity of the findings: Basically, the conclusion is that sauropod eggs were spherical - already well known and that the thick-shelled examples would have been etched by an acidic environment to a thickness that would allow a hatchling to escape. This idea has already been published and the problem I have with the paper is that there is a lack of clarity and depth as to why this particular study is any different from previous studies.

The authors need to better address the topics concerned and explain how their short paper adds to our understanding of the topic.
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: ODOR-DEPENDENT TEMPORAL DYNAMICS IN CAENORHABITIS ELEGANS ADAPTATION AND AVERSIVE LEARNING BEHAVIOR
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article is nicely reported. Language throughout is clear and professional. The introduction and background sections reference relevant literature and give appropriate context to the work done. The structure conforms to PeerJ standards. Appropriate raw data is supplied, although additional labeling would be helpful for clarity. Figures are relevant and well labeled, with a few improvements suggested below.

1. Odor memory in this paper is odor adaptation, which is best given clarification (e.g., as in Cho et. al 2016) to distinguish from other forms
2. To improve consistency and facilitate comparisons, all figure data should be presented as uniformly as possible, including axis scales, axis label positions, start times on x-axis, etc. For example, in Figure 4, methylpyrrole graphs begin at 0 minutes whereas others begin at 20 min.
3. Similarly, organizing graphs in Figs. 3 and 4 in the same positions (for those odors present in both) would help comparison.
4. In Table 1, benzyl proprionate and butyric acid have equal responses in AWA- and AWC- strains, yet the conclusions of which neurons are required to detect each differ. Please clarify.
Experimental design: This work represents original primary research within the scope of PeerJ. The research question answered was well-defined and meaningful, potentially providing useful insight into the timing of odor memory in a set of attractive odors sensed by AWC by timing of EGL-4 nuclear accumulation. The experimental work duplicated or modified existing techniques and were performed to accepted ethical standards. Methods were mostly described in sufficient detail to replicate results.

1. For quantification of EGL-4 translocation, additional method detail would be helpful to understand data variability and confidence. The metric of % animals with nuclear EGL-4 would seem to require a binary assessment of each individual (i.e. yes/no for nuclear expression). But is translocation sudden or gradual? How ambiguous or clearly distinguished were animals with accumulation of EGL-4? Example images demonstrating EGL-4 accumulation and the counting method for accumulation assessment will improve clarity for Figure 4.
Validity of the findings: Data appears well-gathered, with appropriate controls taken; however, substantial statistical concerns are present as described below. As a result, there are some unclear links to the conclusions stated in the article. Further, both late-trending odors appeared saturated in early behavior tests, possible affecting conclusions.

1. Statistical analysis is missing from the primary conclusion of this paper: the correlation of temporal dynamics of odor memory with dynamics of nuclear accumulation of EGL-4. The speed of memory formation is quantified as the time to reach 50% of the total change in attraction index (AI) over 120 minutes, but since there is variability in AI at each time point, there is also uncertainty in the 50% change time. This uncertainty should be reported, such as by standard deviation (SD) or 95% confidence interval. Similarly, timing of nuclear accumulation is quantified as the time to reach translocation in 50% of animals from a curve fit to discrete time points, each with measurement variability. Therefore, SD or 95% confidence intervals for these values should be reported. These data are summarized in Table 2, which should also list the SD’s or 95% confidence intervals, with appropriate significant figures. Finally, the correlation of behavior change to EGL-4 localization should be made with statistical comparisons taking into account these uncertainties.
2. Regression data for Figure 4 is overfit to available data (a 4th-order polynomial to 6-7 data points). The data appears appropriate for a sigmoid function fit, which would contain a regression parameter directly related to the inflection point, a good metric of timing.
3. The authors rightfully concern themselves with odor concentration, which can affect odor dynamics, adaptation rates, which neurons respond, etc. Here, test concentrations were chosen by optimizing for greatest behavior change over 2 hours. However, it appeared that some odors (e.g. 4-chlorobenzyl mercaptan and 2,4,5-trimethylthiazole) had initially high and stable AI (with low variability and small error bars compared to other data points), indicating possible saturated attraction. Could this effect alone delay the behavior change and make these odors appear late-trending?  Instead, normalizing concentrations for the same baseline attraction, such as concentrations resulting in a non-saturated value of AI around 0.75, rather than maximal behavioral change, may better elucidate differences in odor memory and attraction. This would also allow for comparison figures overlaying odors to demonstrate behavioral shifts that may correlate to EGL-4 accumulation.  Alternatively, observing similar late-trending changes at lower concentrations of these odors would lend confidence to the conclusions that EGL-4 translocation timing determines odor memory timing.
4. The authors mention initial testing of 150 odors, from which they identified dozens of attractive odors (it would be helpful to include all these initial data). These were further narrowed down to a subset of AWC-detected odors, and one AWA-detected odor for testing with behavior, from 5 odors were chosen for studying EGL-4 accumulation. What was the rationale for including or excluding data? For example, behavior change to butanone seems one of the most early-trending (Fig. 3), compared with 4-chlorobenzyl mercaptan (late-trending), but data for EGL-4 localization isn’t included here.
Additional comments: This article investigates numerous attractive odors to assess odor memory and timing in the AWC neuron, testing an interesting hypothesis that timing of memory formation in AWC follows timing of EGL-4 accumulation in the nucleus. Through their screen, the authors identify several odors showing high attraction sensed by AWC, including many previously untested, and demonstrate through a dynamic chemotaxis assay format that C. elegans form an odor memory through adaptation, resulting in decreased attraction over time. While the assays are well-stated and performed, variability in raw data and in timing metrics call for statistical analyses to determine whether the odor memory timing correlates properly to the EGL-4 accumulation timing. If after further statistical analysis this correlation holds, the resulting story yields useful insight into the mechanisms of odor memory regulation and timing.


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: ODOR-DEPENDENT TEMPORAL DYNAMICS IN CAENORHABITIS ELEGANS ADAPTATION AND AVERSIVE LEARNING BEHAVIOR
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is well-written and generally clear, although I have a major problem with how the experiments are framed in terms of “memory” (see 3 and General comments). The main difficulty I found with the basic reporting is how the real-time odour behaviour assay worked – I do not see how it tests different “memory” formation time-courses. From what I can understand, you allow a population of worms to migrate and note their position every 10 minutes over a 120 minute time period (figs 2A and 2B). You then determine whether different odours have different time courses in their responses (using the 50% change as a key criterion), which you nicely correlate with EGL-4 nuclear localisation. You argue that this is better than looking at independent groups, and is certainly easier to study. My main concern here (apart from the fact that this is poorly explained) is that this has nothing to do with ‘memory’. If you described this simply as changes in odour response over time (or adaptation), it would be so much clearer.
Experimental design: I cannot find how many replicates you carried out for each R-TOB assay. This should be given in both the text and the figure legend. This also affects your statistical tests (such as they are) and your use of standard errors to demonstrate variability. You claim that your R-TOB is better than the usual assay it reduces experimental variability between populations – you could show this by using a box and whisker plot. It is not clear to me how you compared the effects of different odours on your 50% change criterion, or how you compared slopes produced by different odours. Some kind of statistical analysis needs to be carried out here.
Validity of the findings: I find it hard to understand why the authors have chosen to frame their work in terms of learning. All of the previous articles they cite refer, correctly in my view, to adaptation to describe the phenomenon studied here. There is no operant or classical conditioning taking place in these experiments (these are generally taken to be ‘learning’), for there is no reinforcer. The same applies to ‘short term’ and ‘long term memory, which are not, as far as I can see, appropriate terms, for they are not linked to the normal use of these terms – here they refer instead to a decline in attraction and then to repulsion (if I have understood things correctly).

As far as I can understand it, this study has explored changes in olfactory response over time, during a continuous stimulation. There are two prime ways that this could take place – either on the membrane, in terms of changes to receptor/second messenger activity, or at the synaptic level, whereby the cell may no longer be transmitting a response. The transformation of attraction to repulsion may not be a direct consequence of the receptor cells that you are observing and manipulating, but instead to the output of the whole system following continuous stimulation – they are certainly not the equivalent of LTM and STM.

This phenomenon more appropriately termed adaptation and I feel quite strongly that the whole article needs rewriting/reframing along these lines. If the authors have a good case to maintain their use of ‘memory’, they must make it explicitly, explaining why ‘adaptation’ is no longer the appropriate framework for this kind of study. It may be that I have missed some recent developments in the worm world, but it seems to me that the authors have mistakenly over-interpreted here. Adaptation as a basic sensory process is just as interesting as memory formation! The explanations of what has taken place here, in terms of intracellular activity are potentially important, at a far more fundamental level in terms of a) sensory neuron function and b) the activity of a neuronal network governing behaviour in a model organism. This is the way that the article should be framed, I think.
Additional comments: I found this article much easier to understand once I realised it wasn't about memory as I understand it, but instead about adaptation. I think the correlation of behavioural changes and EGL-4 nuclear localisation is really nice, and if you carry out the kind of mainly literary changes I am suggesting (assuming the Editor agrees), I think this will be a really useful contribution.


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: ODOR-DEPENDENT TEMPORAL DYNAMICS IN CAENORHABITIS ELEGANS ADAPTATION AND AVERSIVE LEARNING BEHAVIOR
Review round: 2
Reviewer: 1

Output:
Basic reporting: Revision addresses adaptation terminology and improves consistency of data figures.
Experimental design: The revised figure panel clearly describes the EGL-4 translocation assay.
Validity of the findings: The revision addresses some of the prior review comments. However, it doesn’t address the main concern regarding the authors’ primary conclusion that differences in adaptation and EGL-4 translocation timing are odor-specific. Both “late-trending” odors (4-CM and TMT) had very high initial AI’s which did not change much over the first 70-80 min (i.e., the measurement appeared saturated). Therefore, the time to reach 50% of the change between 30 and 120 minutes is necessarily larger than for an odor that shows an early AI decline (assuming similar rates of AI decline across odors, which appears to be the case). It is possible (or likely) that the same odors would have lower initial AI's at lower concentration. If so, would AI's be stable over the first 70-80min, like at the higher concentrations tested, or decline sooner, like the "early trending" odors?

In short, since only one concentration was chosen for each odor, it is unclear that differences in adaptation timing are inherent to specific odors instead of concentration-dependent.  (For example, is there a significant correlation between initial AI and adaptation timing across all odors at the concentrations tested?)

Regardless of the cause, the authors show nicely the correlation between timing of behavior adaptation and EGL-4 translocation. The specific claim that odors are inherently “early-trending” or “late-trending” should only be made if the alternative that odor concentration determines early- or late-timing is ruled out, such as by testing 4-CM and TMT at lower concentrations. Alternatively, the discussion should include both possible interpretations of the data.

Also, as indicated previously, a monotonic function such as a sigmoid fit, would be better than a polynomial fit for translocation data.
Additional comments: The revised article is an improvement and clearly demonstrates a correlation between delayed localization of EGL-4 and delayed adaptation in chemotaxis behavior. However, the conclusion that these timing differences are inherent to specific odors isn’t fully supported, as they could also depend on concentration (e.g. one odor could be early-trending at one concentration and late-trending at another). Evidence should be presented toward one interpretation, or both should be included equally.


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: ODOR-DEPENDENT TEMPORAL DYNAMICS IN CAENORHABITIS ELEGANS ADAPTATION AND AVERSIVE LEARNING BEHAVIOR
Review round: 2
Reviewer: 2

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: This is much better, and I am beginning to understand what the authors intended. The absence of food is clearly a negative reinforcer for these very hungry animals.

However, despite the role of insulin signalling in the decline in attraction (p3/lines 11-13) you cannot simply conclude that this is learning. As you now state, adaptation is also taking place – teasing apart the two effects is difficult. Although I accept that a) confusing terms have been used in the literature in the past and b) the adp mutant is apparently specific to learning, I do not understand how your real time assay only measures learning, and not adaptation. You have a paragraph on p11 lines 4-19, which I have now read three times and do not understand how “short-term adaptation and aversive learning can be resolved in the real-time behavior assay” in non-mutant worms, which are mainly what you study in the next section.

If I am correct, and you cannot in fact separate them, then you need to do some further editorial work, including in the title and the abstract, clarifiying this wherever you make claims about memory/learning. The fact that the literature is confused is not a justification for perpetuating that confusion! You really need to explain this very clearly, because at the moment, although you have nuanced the rest of the article, this section, and indeed the title, are still focusing on learning when it seems to me that you have two entwined phenotypes – learning and adaptation.

If I am mistaken, I am happy to be corrected, but you should consider that other readers may be similarly confused, and some editorial clarification might be advised.

You therefore need to make sure that you don’t simply write about aversive learning, so please add ‘adaptation and’ before ‘aversive learning’ at 7/13, 8/17, 9/3

Also:
8/22 replace ‘molecular pathways involved in associative learning’ by ‘the molecular pathways involved’
9/6 delete ‘odor memory behaviour
10/14 replace ‘aversive learning’ by ‘change in attraction’


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: RNA INTERFERENCE-MEDIATED SILENCING OF GENES INVOLVED IN THE IMMUNE RESPONSES OF THE SOYBEAN POD BORER LEGUMINIVORA GLYCINIVORELLA (LEPIDOPTERA: OLETHREUTIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Manuscript passes on all criteria.
Experimental design: Pass
Validity of the findings: Pass - please see comments concerning some minor revisions to clarify significance of findings.
Additional comments: The manuscript by Ran et al. entitled “RNA interference-mediated silencing of genes involved in the immune responses of the soybean pod borer Leguminivora glycinivorella (Lepidoptera: Olethreutidae)” describes the identification of innate immunity genes from a transcriptomic analysis of a lepidopteran pest species, and provides evidence that RNAi-mediated knockdown of some of these immunity genes has serious impacts on the survival of the treated insects. The authors identified 41 immune-related genes using sequence comparisons and phylogenetic analyses with other known immune genes from other insects. The gene sequences’ identities were further supported by examination of predicted modular domains, providing additional evidence for homology with other known immune genes. The authors selected 11 genes to target for RNAi-mediated knockdown, and demonstrated that several genes were essential for development and growth, and that the dsRNAs could potentially be used for insecticidal control of this pest. Given that RNAi has been particularly challenging in many lepidopteran insects, their demonstration of RNAi efficacy in this insect, while previously documented in one of their previous studies, is still worthy of note, as this study illustrates the potency of immunity genes as possible RNAi targets for pest insect control.
The experiments were well described and conducted. The paper was very well written, with some good explanations for many of their findings. I believe that the paper is definitely worthy of publication, as it has provided an excellent application of transcriptomic analyses with its RNAi bioassays. I have only a few suggestions/questions for them to address:

Main points (page numbers refer to the PDF document, including PeerJ’s instructions pages)
1.	On page 19 the authors state: “… larvae treated with Lgitype-1 dsRNA were more sensitive to pathogens, with approximately 50% of the larvae infected by bacteria even in the absence of an artificial pathogen inoculation.” There are no data provided in the manuscript to support this statement, and no mention in the Methods of how bacterial infections were observed or measured. There was no mention in the Methods of artificial pathogen inoculation. To provide definitive proof that the genes under examination in their study are involved in immunity, the best approach would be to challenge the RNAi-treated insects with infections and determine, quantitatively, if the infection progressed faster. Rather than ask the authors to conduct such experiments at this stage, I would suggest that they simply delete or modify this statement, and equally importantly, indicate within their paper that definitive proof of the role of these genes in immunity awaits infection bioassays. The omission of these experiments does not detract from their findings that these genes may play a role in development and immunity. Perhaps many of these genes play dual roles (e.g. Toll’s role in dorsal patterning during embryogenesis, and then in immunity later), being more critical for development during the larval phase, and then more relevant as immunity genes in adults.

2.	Pages 19 notes mortality of the larvae after only three days of feeding on five (5) of the 11 dsRNAs [Toll5s, Serpin2, PGRP-LB, PGRP-LB2b, Chaoptin], and on page 20, it was noted that five dsRNAs induced significant RNAi-mediated knockdown by this time-point [PGRP-LB2b, Toll5b, Toll7b, Toll9b, I-type1]. However, the two lists do not really correspond, with the exception of PGRP-LB2b. Can the authors offer some explanation as to why mortality was observed in those 3-day feeders when transcript knockdown was not considered significant (e.g. PGRP-LB, Chaoptin), or was only mildly knocked down (e.g. ~10% for Toll5a, 20% Serpin2)? Can the authors relate the early mortality to those particular genes’ functions, and similarly, indicate why some of the other dsRNAs took considerably longer (15 days) to have an impact on the survivorship of the insects?

3.	On page 21, the authors noted that PGRP-LB2a, when knocked down by RNAi, resulted in arrested development, but commented that PGRP-LB2b did not have a role in development, as no such phenotype was observed when the latter was knocked down. However, as noted above, PGRP-LB2b killed the insects early, so could that not also mean that the 2b gene is essential for development, and in fact, is more critical than 2a? Some further elaboration on the possible roles of 2b could be helpful.

4.	The authors comment on page 19 that PBS treatments were used as negative controls, but there is no evidence of these treatments in any graphs.

5.	On page 23, the authors state “Thus, LgI-type-1 exhibits isopeptidase activity…” but as there is no experimental data for this, it would be better to state “Thus, LgI-type-1 may have isopeptidase activity”.

Minor points (minor typos).
6.	Page 9, Line 7. Change: “highly efficient of RNAi to” to “efficiency of RNAi in”
7.	Page 13, line 6. Delete “of”
8.	Page 13, line 8. Insert “two” before “pooled” for clarity – if I understood the method accurately(?).
9.	Page 20, line 16. Insert “and” before “helps”