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: 2

Output:
Basic reporting: The article provides sufficient background information to understand the relevance of the stated research objective. The study's findings are relevant to this objective.

Below, I provide extensive suggestions that I hope the authors will find helpful for improving the manuscript. These recommendations seek to insure that the text is uniformly clear, that appropriate references are consistently cited, and that all figures and tables are properly prepared.

Note: Page numbers below refer to the PDF supplied to this reviewer, with the manuscript itself beginning on PDF page 4.

INTRODUCTION
p. 9, lines 1-9: This paragraph would benefit from revision. Most notably, it’s odd that in the last sentence an older reference (Terenius et al., 2011) is cited as “recently increased” information to counter the conclusions of a newer reference (Shukla et al., 2016). In addition, this sentence is grammatically incorrect. To better captures the authors’ intent, I recommend removing the opening phrase to produce this revised sentence: “However, RNAi is particularly successful when targeting genes involved in immune responses (Terenius et al., 2011).” Furthermore, the flow of this paragraph could be enhanced by switching the fourth (“The effectiveness of…”) and fifth sentences (“To date, applying RNAi technology…”) and then replacing “To date” with “However” (and now removing “However” from the last sentence of the paragraph).
p. 9, lines 10-18: In the first sentence, a research article on planthopper genomics is cited to support a factual statement about D. melanogaster and B. mori innate immune system. A more relevant reference should be cited instead.
The second sentence of this paragraph is somewhat convoluted and hence difficult to decipher; dividing this sentence in two at the first comma would help. The authors should clarify that PGRPs can activate the two pathways or induce a proteolytic cascade. Finally, it’s unclear if the final phrase (“which are critical for defending…”) refers to antimicrobial peptides or the activated/induced responses.
p. 10, lines 1-6: To better connect the opening sentence to the preceding paragraphs, insert a transition phrase such as “To identify immune-related genes…” at the beginning.
METHODS
p. 11, lines 8-11: The references cited at the end of this paragraph are not relevant to the closing sentence. A more appropriate reference might be Altshculer et al. (1990), McGinnis & Madden (2004), or another BLAST program reference.
p. 11, line 13-17: The Tamura et al. (2011) reference cited in the previous paragraph is more relevant to the first sentence of this paragraph. Appropriate references for the web sites identified in this paragraph are available at those sites (e.g., Clustal Omega, PMID:21988835; SMART, doi:10.1093/nar/gkx922).
p. 12, line 5: Only two supplementary tables were included in the package to review. In this package, Table S2 is labeled “Primers used for synthesising dsRNA and analysing candidate genes.”
p. 12, line 15: The reference is erroneously duplicated.
p. 13, lines 6-7: Change “of per biological replicates” to “per biological replicate.”
RESULTS
p. 14, line 5: It would be helpful to explicitly label the three groups in Table S1.
p. 14, line 9: The comma should be removed.
p. 14, lines 10-12: This sentence seems out of place. Perhaps it would fit better at the start of the next subsection, “Immune signalling molecules” (p. 16, line 17).
p. 15, line 12: The authors should use the more specific term “ortholog” (instead of homologue).
p. 17, line 18: Fig. S2B displays an amino acid sequence alignment of the two L. glycinivorella Snake proteins, not of the three Serpin proteins, as this sentence would suggest.
p. 18, lines 5-7: Table S1 (“Details regarding the immune-related genes of Leguminivora glycinivorella”) includes two defensin genes, not just one.
p. 19, line 14: Not all cuticles are black in Fig. 5; the RNAi treatments causing black cuticles should be briefly identified in the text.
p. 19, line 16: This data is apparently not shown, so this should be (parenthetically) noted in the text.
DISCUSSION
p. 20, lines 15-19: This paragraph would benefit from revision. The first sentence has a grammatical error that should be corrected (and says insects three times). The second sentence should briefly note why these are of interest (or be removed). The third sentence should be clarified: Presumably hundreds of genes were identified in this transcriptome, with 41 encoding immune-related proteins. I suggest revising as follows: “In this study, we identified 41 genes in the L. glycinivorella transcriptome encoding components…”.
CONCLUSION
p. 23, lines 13-15: Two grammatical errors present: “would” should be “will” and the comma should be removed.
REFERENCES
Some references are not listed in alphabetical order, including Hughes (2012); Imler & Bulet (2005); Joga et al. (2016).
FIGURES
Figure 1: In the legend, “bootstrap values” should be changed to “bootstrap percentages” and D. melanogaster should be italicized.
Figure 2: (A) In the legend, “bootstrap values” should be changed to “bootstrap percentages.” (B) It should be noted in the legend that the blue bar indicates the transmembrane domain. A period is missing at the end of the last sentence of the legend.
Figure 3: As noted elsewhere, the p-values must be corrected for testing multiple hypotheses; if p-values have been adjusted, this should be noted here (and the procedure used should be indicated in the Methods section). Also, the legend should mention what the error bars indicate (apparently not ±SD or ±SE since they are not symmetrical about the mean). Finally, the legend should state that this is the “Mortality rate of larvae…”.
On the graph, the y-axis should be relabeled “Mean mortality (%)” and its maximum value should be 100%, since mortality cannot exceed this value.  Also, the sample labels should be larger (and written at an angle to provide sufficient space).
Figure 4: Similar to Fig. 3, the legend should state that this is the average (or mean) body weight and should mention what the error bars indicate (apparently not ±SD or ±SE since they are not symmetrical about the mean), as well as if the p-values have been adjusted for testing multiple hypotheses. Unless the measurements were accurate to 0.01 mg, the numbers on the y-axis should be whole numbers.
I’m surprised that no significant difference in mean body weight was detected for Lgitype-1, which shows similar means and variances as with LgToll-5b; in particular, 9d means and variances are less than for LgToll-5b.
Figure 5: GFP control larvae should be included for comparison. What is CK in the 12th panel?
Figure 6: As noted for Figures 3 and 4, the legend should describe the error bars and whether p-values were adjusted for multiple testing.
SUPPLEMENTS
Fig. S1: If GNBP1 and 2 also from D. melanogaster, then this should be designated (as with DmGNBP3).
Table S1: The headers of Columns B and E point to footnotes that are not present at the bottom of the table. Abbreviations for some insect species noted in Columns J and K are included at the bottom of the table, but Bm and Pm are missing.
Table S2: The Column C header is misspelled (it should be “Product”).
Experimental design: The authors present a thorough examination of the potential of immune-related genes as RNAi targets for control of the soybean pod borer (SPB), Leguminivora glycinivorella. While the authors have conducted a largely well-designed experimental protocol to address their well defined research questions, the experimental description has a major flaw that must be addressed prior to publication. Two supplementary tables referred to in the text, which contain information necessary to replicate the experiments, are missing from the package provided to this reviewer. This major issue and a few more minor issues are detailed below.
METHODS
p. 11, line 4: The method used to create unigenes should be described or an appropriate reference should be cited.
p. 11, lines 8-11: The list of immune-related genes used to complete the sequence similarity searches with tBLASTn should be included. Table S1 (but not the cited Table S2) identifies some insect orthologs, but it’s not clear that this was the entire list used for the tBLASTn search. Perhaps this list is one of the missing supplementary tables (see “General comments for the author” section). This list should include GenBank identifiers (GI or Accession.Version numbers) and names of homologs from D. melanogaster or other organisms.
p. 12, line 5: Only two supplementary tables were included in the package to review. In this package, Table S2 is labeled “Primers used for synthesising dsRNA and analysing candidate genes.”
Validity of the findings: While the authors provide much convincing evidence in support of their conclusions, the manuscript has two major flaws that may compromise the validity of the findings. Foremost, the authors must explicitly address the issue of multiple hypothesis testing. Furthermore, features of the gene expression studies to confirm RNAi-mediated gene silencing must be remedied as described below. Finally, I also note some additional minor issues.
METHODS
p. 13, lines 4 & 17: There is no indication how p-values were corrected for testing multiple hypotheses (i.e., Bonferroni or a more sophisticated correction). If the p-values have not been adjusted, then many of the study's conclusions are questionable.
FIGURES
Figure 6: How can GFP expression levels be used as a control? Unless larvae were transgenic, SBP does not express GFP. And what are expression levels relative to? I would expect expression levels to be relative to the 0d values for each gene, which should then all be set to 1.00, but this is not the case in Figure 6. Along with the description of the normalization method, the calculation of relative expression levels should also be explicitly described in the Methods section.
RESULTS
p. 16, lines 11-13: Several of these designations are problematic, since they incorrectly suggest close evolutionary relationships between distant members. For example, the designation for LgToll-6c suggests that it is monophyletic with LgToll-6a and -6b. However, as shown in Figure 2, LgToll-6c shares the same common ancestor with LgToll-7a/7b and LgToll-6a/6b, and is therefore equally related to all four members. Similarly, the LgToll-5a/5b designations are misleading since these L. glycinivorella homologs are equally related to DmToll3, 4, and 5. Finally, LgToll-9b is also not monophyletic with LgToll-9a and should be renamed.
p. 19, line 6: Too many significant figures (42.86%) exaggerate measurement accuracy; change to 43-92%. Also refer to Fig. 3 here.
p. 19, line 7: The PBS data should be added to Figure 3. If not appropriate, then the text should mention (parenthetically) that this data is not shown.
DISCUSSION
p. 21, lines 7-10: It should be noted that the LgPGRPs presumably exhibit diverse activities, since this wasn’t tested directly.
p. 22, line 16: Earlier (p. 19, line 6) the maximum mortality rate was stated as 92%, not 93%. Correct either sentence to resolve this difference.
p. 23, lines 6-8: This sentence is incomplete. Consequently, I’m unable to understand the sentence that follows, which argues that LgI-type-1 exhibits isopeptidase activity.
Additional comments: The authors present a thorough examination of the potential of immune-related genes as RNAi targets for control of the soybean pod borer (SPB), Leguminivora glycinivorella. While the authors have conducted a largely well-designed experimental protocol to address their research questions and provide convincing evidence to support their conclusions, the manuscript has several major and numerous minor issues that should be addressed prior to publication. Foremost, two supplementary tables referred to in the text that are required to replicate the experiment are missing from the package provided to this reviewer. Second, the authors must explicitly address the issue of multiple hypothesis testing and some aspects of data presentation. Third, flaws in the gene expression studies to confirm RNAi-mediated gene silencing must be addressed. In addition to these significant issues (highlighted in bold), I also provide extensive suggestions that I hope the authors will find helpful for improving the manuscript.

Notes:
Page numbers below refer to the PDF supplied to this reviewer, with the manuscript itself beginning on PDF page 4.
As mentioned, the manuscript refers to Tables S1-S4, but the downloaded package contained only two tables. When the text refers to Tables S2 and S3, it apparently corresponds to Tables S1 (“Details regarding the immune-related genes of Leguminivora glycinivorella”) and S2 (“Primers used for synthesising dsRNA and analysing candidate genes”), respectively, in the downloaded package.


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: 3

Output:
Basic reporting: manuscript has clear and concise English use and sentence structure. Sufficient references in the field of study were cited. The article, figures, and tables are suitable for professional publication.
RAW DATA SHARING" Sequences mRNA are listed in file, which is good, IF these have been submitted into NCBI, or similar public database the assembled sequences accession numbers and the website where located NEED to be included.  Authors have tried to submit short archive sequences, which is not sufficient. Please add into text where suggested (Results).
Conclusions and summary support hypothesis.
Experimental design: Manuscript fits within the aims and scope of journal.

Research is of significant interest and active research field, filling and adding to the knowledge gap in RNAi.

Investigation appeared to be of suitable replication and analyses, with suitable use of statistics and gene analysis software, and standards.

Methods described in sufficient detail and information to replicate.
Validity of the findings: Impact and potential assessment of application was reasonable and followed from the results logically.

Conclusions well stated, and linked to results, displayed well in the figs/tables included.

Data files with mRNA and protein sequences, phylogeny, etc. well presented and support conclusions.
Additional comments: Well done, nice research and of signficant impact for lepidopteran studies.  It was interesting that with so many lepidopteran species cannot induce RNAi post feeding, yet your insect appeared to work just fine.
A future study may want to try and determine WHY the RNAi method worked so well in your experiment.


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: 2
Reviewer: 1

Output:
Basic reporting: The authors have made considerable revisions to the manuscript and I am satisfied with the changes.
Experimental design: The Methods have had sufficient revisions and are now clear.
Validity of the findings: The data are robust and the conclusions are appropriate.
Additional comments: I'm satisfied with the revisions.


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: 2
Reviewer: 2

Output:
Basic reporting: The author has addressed my comments and recommendations from my previous review. Some of the changes in the text have grammatical errors, but can be comprehended.
The figures have been revised as I recommended. However, I was unable to open the .emf file of Fig. S1 on my Macintosh computer.
Experimental design: The author has addressed my comments and recommendations from my previous review.
Validity of the findings: The author has addressed my concerns regarding Bonferonni correction due to testing multiple hypotheses.
Additional comments: The author has done a thorough job addressing my concerns and suggested revisions. Good 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: UNFAMILIAR FACE MATCHING WITH PHOTOGRAPHS OF INFANTS AND CHILDREN
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper describes important research currently missing from the research literature and I believe it should be published in PeerJ once the issues listed below are addressed. I commend the authors for writing a very interesting and well thought out paper. It is simple but effective.

Please ensure you report effect sizes throughout. There are some missing.

Lines 207-213 – this section is slightly confusing as you report results of a ‘benchmark test’ – I would move this sentence down to the next paragraph? You then report the t-tests - % correct, sensitivity and criterion. Please additionally report whether hits and false alarms significantly differed from chance – sometimes these effects can be illuminating, and after all you report the descriptives in Table 1.

Line 213 – you then return to the GFMT. Is this the long version of the GFMT? If so, please report trial numbers. And also explain why here you use the long version, later the short version (p 338).
Line 224 and Table 1 – why not report hit and FA rates and run t-tests comparing with criterion?
Line 230 – would it be possible to report confidence intervals when making this passport officer estimation?
Line 309 – also report hits and false alarms t-tests and effect sizes.
Experimental design: Meets all standards
Validity of the findings: Meets all standards.
Additional comments: Line 234 and 321– I think here you should have run a quick follow up study testing why sex of the infants was not informative in assisting ID judgements, as the results suggest there may be something unusual about the images you used. I would ask a few participants to make sex judgements to each infant image. It should not take long, and it would not need many participants but would answer the question as to whether sex information was somehow missing from your images, that was available in the other studies listed in Line 234. It might suggest that with a different set of images of infants, the results for the sex-incongruent results would differ. However, if the editor feels this is not necessary for publication then I am happy for you to leave as is.


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

Input:
Title: UNFAMILIAR FACE MATCHING WITH PHOTOGRAPHS OF INFANTS AND CHILDREN
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is clear and well-written. However, I have several suggestions for improving the quality of the manuscript further.

1. The review of the current face matching literature in the introduction is rather sparse and could be more comprehensive. For example, some key studies are missing from the introduction that set the context of the study, such as Burton et al.’s (2010) work with the GFMT showing baseline accuracy rates of 80% as a best-case scenario, and White et al.’s (2014) work with passport officers. Likewise, there is room for discussion of within-person variability in relation to Experiment 2 (see, e.g., Fysh & Bindemann, 2018; Megreya et al., 2013), and how this impacts face matching performance.

2. In the General Discussion (Lines 486-487), the authors write that “children’s faces are more homogenous than adult faces, displaying lower levels of between-face variability.” This is a logical point, but difficult to reconcile with the findings of Experiment 3 – if infant faces are homogenous, then couldn’t we logically expect a response bias in the direction of classifying faces as the same identity, rather than as different?

3. Would it be possible to also provide an example mismatch trial for the Infant-Infant matching task?

4. The link between Experiments 1 and 2 is not explicitly stated, although the rationale is straightforward. A few lines at the end of the discussion for Experiment 1 to introduce the motivation for Experiment 2 would help clarify this.

5. There is little discussion of the findings of Experiment 2. These could be contextualised in line with the current face matching literature (e.g., within-person variability).
Experimental design: The research question is timely and relevant to face matching in practical settings such as passport control. There is clear value in understanding the extent to which child and infant photographs can be accurately matched. However, I find some aspects of the current experimental design to be problematic. These concerns are specified in further detail below.

1. For Experiment 3, the authors note that they did not restrict themselves to same-sex pairings for mismatch trials in the infant-infant and infant-child matching tasks (Line 373). If this is the case, why are differences between same-sex and different-sex pairings not reported as they are in Experiments 1 and 2? In general, this consistent aspect of the design across experiments is problematic, given that this introduces a clear distinction between match (always same-sex) and mismatch trials (sometimes same-sex), and it isn’t clear as to why the researchers chose to construct their mismatch trials in this way.

2. In line with the above point – given that the trial types are so different here, I do not think that it is appropriate to collapse accuracy across match and mismatch trials when analysing performance. Instead, Experiment 3 would be far more informative if the data were analysed via a 2 (trial: match vs. mismatch) x 3 (matching task: infant-infant vs. infant-child vs. GFMT) repeated measures ANOVA.

3. I also have some further concerns about the selection criteria used for stimuli in Experiment 3, namely that items in the new infant-infant and infant-child matching tasks were based on by-item accuracy from Experiments 1 and 2. If my understanding of the first two experiments is correct, then this means that for each match trial, 30 data points were available, but only 1 data point was available per mismatch trial because these were randomly generated for each participant. Is this correct? If so, then these seem to be rather loose criteria for selection of mismatching stimuli to be included in the final test.

4. In Experiment 3, it is reported that 37 participants were recruited, and then in the results it is reported that data from three participants was excluded, with the analysis being based on the remaining 37 participants. This detail should be amended and/or clarified in the ‘Participants’ section of Experiment 3.
Validity of the findings: The findings are interesting and novel. Considered together, this research suggests that it is extremely challenging to match images of two infants (Experiment 1), as well as infant-to-child photographs (Experiment 2), and that these are notably more difficult than matching two (highly optimised) images of adults (Experiment 3). There are some caveats to this work that should be addressed, however, and there is room to extend these findings further. Again, suggestions for improving the current set of results are provided below.

1. The researchers should consider including some reliability measures for the infant-infant and infant-child matching tasks (e.g., Cronbach's alpha or Split-Half Reliability).

2. In general, the sample sizes are rather small across all experiments, and differences between the construction of the tasks used makes it difficult to assess whether the results are actually replicating between Experiments 1 and 2 to Experiment 3. It would be worth re-running Experiment 3 with a greater number of participants to replicate the main findings (i.e. that infant-infant and infant-child matching is more difficult than matching adult faces), as well as clarify the marginal findings (e.g., correlations between tests), which may have been unstable due to the low sample sizes (e.g., Schönbrodt & Perugini, 2013).

3. The researchers may also want to consider examining how accuracy for infant-infant and infant-child matching relates to additional, more difficult tests of face matching (e.g., Kent Face Matching Test, Model Face Matching Test, Good Bad Ugly Face Test, etc.).

4. In Experiment 1, why was accuracy compared to performance in the GFMT as found by Bobak, Dowsett, et al. (2016), as opposed to Burton et al. (2010)? Likewise, why is performance in Experiment 2 also not compared to GFMT levels of accuracy?
Additional comments: In general, this research explores an important set of questions and I would like to see the findings published, following some revisions. I hope that the suggestions that are supplied here will be of some value moving forward with 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: EXPRESSIONAL AND FUNCTIONAL INTERACTIONS OF TWO APIS CERANA CERANA OLFACTORY RECEPTORS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript by Lina Guo et al entitled ‘Expressional and functional interactions of two Apis cerana cerana olfactory receptors’ describes the expression and pharmacological characterisation of odorant receptors found in the Eastern honeybee. The authors expressed the receptors in insect cell line and then performed a series of molecular, biochemical and signalling assays to determine their functions in an in vitro system and in the context of food sensing/antennae function. The olfactory receptors are considered as understudied group of GPCRs and the authors should be commended for performing these studies. I have some suggestions, which I believe will improve the manuscript.

In the introduction, the authors should include what is known about the signalling/G protein coupling preference of these odorant receptors.

It would be helpful if the authors show the amino acid sequences of the two receptors and highlight the regions which were targeted for the generation of the antibody and explain why these regions were chosen.

The manuscript has series of mistakes, listed below which should be corrected:

Grammatical errors and missing words in sentences such as seven receptors which should read seven transmembrane receptors, conclution which should read conclusion etc.. Please carefully read the manuscript and make corrections.

Figure 1: Panel A, texts appear squashed and receptor band (second from right) for OR2 is misaligned - please rectify. Panel B, please include molecular weight in the blot.
Figure 2: Panel C, some cells appear yellow. Why? Please rectify.
Figure 3: Labelling (e.g. -, +) appear misaligned - please correct. Also please confirm in figure legend if the data was calculated relative to a house keeping gene (eg.beta actin) using the deltadelta to the power -2 analysis as indicated in the method.
Figure 4: Panel B and C please include the labelling in the quantification graphs in the same way as panel A. Also, include molecular weight for the blots and the antibody used in the blots (either in the figure itself or figure legend).
Figure 6. Please make the tables bigger and also include the maximum responses (efficacy) of the ligands. Please provide a brief explanation in the figure legend how the data was analysed. It says % maximal response. Which ligand and at what concentration the authors use as the reference/maximal response here?
Figure 8. It is not obvious in the text or the figure legend what the labelling on top of each bar graph (a,b,cd etc..) means. Please provide explanation in either the results section or figure legend.
Table 1: Also include the maximal responses (efficacy) in addition to potency (EC50).
Experimental design: Whilst the experiments were well designed, there are information which the authors should include/mention:

The authors should provide a brief rationale for measuring calcium output. Is calcium signalling considered to be the primary signalling pathway relevant for antennae function/sensing or is calcium assay used simply to narrow down the ligand choices?

The authors should also include a non transfected control in this assay.

The authors should provide the source of the receptor construct. Did the authors clone them from the honeybee or are they synthetically made/purchased from a company?

The authors should provide information on the molecular weight of AcerOr1 and AcerOr2 on the western blot data. Does the molecular weight correlate with the nominal molecular weight predicted from the DNA sequence? Or is it altered as to indicate posttranslational modification?
Validity of the findings: I have questions regarding the following observation:

Activation of AcerOr1 with a range of odorant molecules resulted in calcium elevation, a response generally thought to be through Gαq G-proteins. This response is augmented in the presence of the co-receptor AcerOr2 for a number of compounds tested.

1. Can the authors provide evidence that the two receptors interact via direct/indirect mechanism by performing co-IP etc..

2. Is the augmented response maintained in other signalling pathways (such as ERK, IP3, cAMP, arrestin recruitment, receptor phosphorylation/internalisation) linked to AcerOr1.
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: EXPRESSIONAL AND FUNCTIONAL INTERACTIONS OF TWO APIS CERANA CERANA OLFACTORY RECEPTORS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The text needs editing and typo corrections. This needs a professional input into the presentation style and content.

The discussion of the heteromeric receptors as being distinct has not been distinguished from differences in receptor expression levels and solely homomeric functional receptors.

A more focused article is needed.
Experimental design: Seems fine, but the evidence of expression is poorly presented and the justification for the knockout experiments is unclear (it reads like it is just extra data to pad the article). The evidence for heteromeric receptor function needs to be more rigorous.
Validity of the findings: Findings not validated in respect to heteromeric receptor expression. Most of the findings are not important, so the authors need to focus on what is actually worth saying and only provide that data required to substantiate that evidence.
Additional comments: Main criticism: The only data providing any new knowledge is the figures 5, 6 and 8. The rest is very pedestrian and superficial. Moreover, the data has not been used to demonstrate evidence of heteromeric expression.

L19: Transient transfection and cell surface expression of AcerOr1/2 in sf9 cells is useful, but why is it interesting to then knock out their expression with dsRNA?

L60: The argument for requiring sf9 cells is not robust. Please expand the argument by pointing out specific advantages. Many neuronal receptors from have been studied extensively in unrelated cell lines (HEK293, HeLa, COS-7) and these have yielded most of what we know about their pharmacology.

L65: The paragraph on RNAi is superficial and not relevant.

L70: The paragraph is not related to actions studied in this paper. Better would be a discussion of what is known about which receptors respond to which ligands.

L99: Vector construction does not provide sufficient detail for this to be repeated.

The methods read more like lab protocols that published methods. What is the %PFA used? This is important if the PM integrity needs to be intact to detect surface only staining (PFA may permeabilise cells, depending on concentration and duration.

Figure 1. DNA digest panel is trivial and should be removed. Showing only the selected band is undesirable and the whole lane needs to be shown for clarity (perhaps in the supplemental figures), otherwise specificity is unclear. Are the receptors devoid of N-glycosylation?

Figure 2. A higher magnification is required to demonstrate cell surface staining.

Figure 3/4 is useful if the knockout approach were to be used in native cells, to demonstrate that it works. It is not interesting when done on a cell line alone as this is expected.

Figure 5 is interesting but I am unsure as to what the co-expression results mean. Does this suggest a heteromeric receptor? Or is this equivalent to two separate homomers? Interpretation of this requires the relative expression levels between the cell lines to be known. The text claims that this figure indicates expression level, but it does not as this implies that function is directly proportional to expression, regardless of composition of Or.

Figure 6/7. The same applies as referred to in figure 5. Interesting but what does the co-expression data mean (hetero or 2 homos)?

Figure 8. No indication of error for n=3. A dose response curve (with error bars) should be given instead of panel A, which is then just repeated in panels B-D. If plotted on the same graph the relative potency will be clearer.

Table 1. Does the significance justify the exact values give for EC50, especially when the error does not match this confidence)? I doubt that very much (eg. 4.975 +/- 0.45.

Discussion. This section is way too long for the data presented, mostly because it repeats the results. The discussion claims evidence of heteromeric expression but this has not been demonstrated to me.

Q. Are sf9 cells devoid of endogenous Or expression? So that homomeric receptors are confirmed.

It strikes me that the authors are inexperienced at submitting professional research articles and would benefit from local expert advice.


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: EXPRESSIONAL AND FUNCTIONAL INTERACTIONS OF TWO APIS CERANA CERANA OLFACTORY RECEPTORS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The introduction provides the reader with a good scope of the literature and expression systems other researchers have used to functionally explore insect ORs however there are areas that require further clarification and re-writing –

The opening paragraph of the introduction (line 33-40) in general is confusing.  Line 38/39 –the authors state ‘These seven receptors are not related to any other receptor family’ – I think what the authors are referring to here are the fact that GPCRs are seven transmembrane spanning receptors. This becomes more confusing when the author goes from ‘seven receptors’ here to ‘hundreds of ORs’ from line 41 onwards.  The authors need to be clearer as to what they mean. This needs to be re-written for clarity.

Line 76, could the authors elaborate here and give examples of the tissues that have been found to possess different OR levels.

The author covers AmOr11 function in the honey bee (line 70 onwards) however from here it is not quite clear why AcerOr1 and AcerOr2 was chosen for investigation – I think this needs to be explained and covered better in the introduction (maybe ideally placed between line 78 and 79).
Experimental design: The methodology section provides a good level of detail and experimental information for repetition of conditions.

Major – Can the authors insert a section to inform the reader of how they processed Western blotting and conducted densitometry and any normalisation carried out (if any) against β actin loading controls.

Minor corrections/updates –
Line 120 – could the authors state the concentration of G418 required to generate the stable cell lines.
Line 132 – could the authors state the concentration of PFA used to fix their cells.
Line 144 – could the authors state the components of the lysis buffer used for Western blotting experiments.
Validity of the findings: Results –
Figure 1 – title is generic and not very informative. ‘Effects of transfection’ is vague.  Could the authors reword this so that the specific effects being investigated is more clearly stated.  The images in figure 1A and B appear to be representative. Could the authors please indicate in the legend how many repetitions of these experiments were conducted.  Figure 1A – the font size on the lane labelling needs to be increased so it can be read more clearly.  Figure 1B –  The alignment of the wells presented for each of the panels do not match up to one another.  Could the authors state if these images are reprobes from the same membranes or sample re-runs.  There is no control panel (example β actin) to demonstrate equal loading across the sample wells.  This needs to be included.  OR protein size information needs to be included either in the figure or legend information.

Figure 2 – Could the authors please indicate in the legend how many repetitions of these experiments were conducted.    The subcellular localisation of AcerOr1 and Acer Or2 in the IF images provided is not entirely clear at the current magnification.  Could the authors provide images that offer increased magnification so that subcellular features of the receptor are more clearly depicted.

Figure 3 – The annotation in the graph presented in Fig 3A needs to be better aligned to the corresponding bars.  The authors have *** in the figure panels but the figure legend only indicate P* and P**.  Can the authors define the P*** in the legend to coincide with their presence on the graphs and the statistical analysis used with any post test conducted.

Can the authors comment upon the low expression levels of AcerOr1 mRNA and AcerOr2mRNA in Fig 3E/F (without dsRNA) compared to the other panels (A-D).  Also, the dsAcerOr1 seems to be more effective and selective for knockdown of the AcerOr2 (fig 3D) compared to Fig 3B, yet co-treatment with dsAcerOr1/dsAcerOr2 is most variable (3E/F).

Figure 4 – Can the authors annotate the blots in A, C and D to indicate protein band size for each panel.  The β-actin blot in Fig 4A looks upside down.  Based upon the representative AcerOr2 panel in Fig 4B, I am not convinced that AcerOr2 is significantly reduced.  The quality of the blots in the AcerOr2 panel is poor and the βactin panel lane 3 appears to be more reduced than the AcerOr2 levels which raises doubt as to the equal loading of protein between samples.  Can the authors define the P*** in the legend to coincide with their presence on the graphs and the statistical analysis used with any post test conducted for these experiments.

For the combination dsRNA experiments, the authors have chosen 500ng of dsRNA yet these conditions did not appear to significantly affect mRNA levels in the experiments in Fig 3 F. Could the author comment upon this please.

I would advise the authors to revise lines 278-286.  The data presented in Figure 5 A/B/C needs to be described better in the results text.   There is insufficient information to support the figure as to the experiments conducted and the nature of compounds selected for screening.  Based on the results text it is not clear what cells are being tested in panels A-C.  This needs to be signposted better.    The title in Figure 5 needs corrected – remove ‘a’ in ‘to a various’.  The information in the legend states that bars indicate standard deviation then they state that data points represent mean/SEM.  Can the authors clarify what they define as bars versus data points.  This is confusing and needs to be clearer.

Given that the authors provide a dedicated table for all EC50 values (table 1), I would ask the authors to remove the individual tables from beneath panel A-C.   The authors need to make sure that they insert the units into the EC50 values in the results text where appropriate (line 287 onwards).  The units should also be clearly presented in Table 1.  The curve fitting software used to derive the EC50 values obtained in Figure 6A-C needs to be inserted into the figure legend and the nature of any equations used (i.e. Hill equation).  The information in the legend related to the panels need to be corrected.  Based on the legend information, the authors have mixed up Figure panel B and C.  The authors need to correct the legend information – there are no bars presented here yet the authors state ‘Bars indicate standard deviation based on three independent experiments’.  Please edit accordingly to accurately reflect the data presented.

The results text related to Fig 6 (line 287-292) is very brief and does not support the figure content very well.  The EC50 values cited for linolenic acid (line 289) in the results text are different to the values presented in Table 1.  It is not clear why the authors have focussed specifically on that one EC50 value.

Figure 7 needs to be described better in the results text.  The authors need to provide information related to the concentration of odorants used to perform the experiments conducted in Figure 7.

Major comment – The excitation and emission wavelengths for Fluo4 and GFP are similar which often leads to interference in calcium flux assays when cells express GFP. The authors used dsGFP as a control in their experiments, can the authors comment upon how the presence of GFP in their cell system impacted their calcium imaging.  This needs to be clearly stated.

Figure 8 – Line 305: Based upon the data obtained so far, it is not clear why these three odorants were selected for further investigation.  This needs to be explained better in the text.  The results text that corresponds to figure 8 is minimal and insufficient to support the data presented. The same applies to the information provided in the figure legend.  In its current form, the legend does not support the data presented in panels A-D.  Despite the information provided related to the different letters at the top of each bar, it is not clear what a, b, c, d, cd actually correspond to by way of ‘significance’. The authors need to revise and re-write the content of the results text and legend to make sure that this is clearer.

Minor - Typographical error, Line 412 - Conclusions
Additional comments: Whilst the authors cover a vast body of literature throughout the manuscript related to the importance of ORs in odor recognition processes for a host of insects, one of the aspects that is lacking in detail are the known signal transduction pathways triggered upon OR activation in response to odorants.  Information related to the G-proteins that couple to ORs and their second messenger pathways activated really needs to be included.  The conclusions from the study related to odor recognition for AcerOr1 and AcerOr2 relies upon data derived principally from calcium imaging experiments.  This is really only one output that has been explored therefore the ability of these odorants to trigger other signalling pathways downstream of AcerOr1 and AcerOr2 is still unknown.  The authors need to state why this pathway was considered to be the most appropriate for the receptors studied.  In the GPCR field, ligand bias and bias signalling is becoming more apparent.  Whilst the ligands tested for the AcerOr2 expression systems only revealed VUAA1-mediated calcium activity, the potential for other pathways to be activated downstream of AcerOr2 (other than calcium) by the other odorants has to be considered and discussed.  This is a major limitation of the current investigation as no other signalling pathway was explored.


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: EXPRESSIONAL AND FUNCTIONAL INTERACTIONS OF TWO APIS CERANA CERANA OLFACTORY RECEPTORS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript can be improved by making the sentences easier to follow and correcting sentences that do not make sense such as  "So functional characterization of AcerOr1 do not through Gαq G-proteins can also stably transformed Sf9 cells". There are also some confusing sentences especially whether Or1 and Or2 are behaving as ion channels or G-protein coupled receptors.  As such, it is unclear whether the increase in calcium signal is a result of the ionotropic property of the proteins or that these proteins activate G-protein dependent signalling leading to calcium elevation.  The authors should clarify this.
Experimental design: Experimental design seems fine. There are minor mistakes that can be addressed easily such as the primers for AcerOr2 which are written as both 'forward primer' and the calcium response which does not have a unit.
Validity of the findings: The authors need to be cautious with regard to dimers (e.g. Or2+Or2 leading to the formation of ion channel) especially that no evidence is provided in the manuscript.
The observation that calcium signalling is augmented when Or1 is co-expressed with Or2 is interesting and may play a role in fine tuning the sensitivity of odor sensing. However the authors do not provide evidence how this is achieved. The authors should provide evidence for the idea that these proteins form dimers by performing additional experiments such as designing minigene to disrupt the dimer or co-immunoprecipitation. Otherwise the co-transfection data becomes uninterpretable and should be omitted. Any mentions of a dimer should also be removed.
Additional comments: Please carefully revise the manuscript to make it easier to follow.


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: EXPRESSIONAL AND FUNCTIONAL INTERACTIONS OF TWO APIS CERANA CERANA OLFACTORY RECEPTORS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript has been dramatically changed since it's original submission in a way that has improved the clarity of the research findings.  I feel that the authors have made a serious attempt to address most of the concerns raised from the previous peer reviewers.

I have minor comments that I feel could be easily addressed by the authors -
The abstract needs to be improved from Line 19-23.  The author needs to be more clear on what exactly revealed 'distinct changes to concentration response curves' and what those distinct changes were.
Can the authors provide details as to the signalling cascade that results in opening of ion channels (line 30-31).
Remove 'is' on line 54.
Amend the font of the text in line 171
The reference on line 178 is incomplete and requires a date.
The results text from line 246-256 needs to be organised better.  Whilst it is great to have the numerical information, there has to be a better balance of descriptive text rather than just relay EC50 values compiled in table 1.
Lines 290-291 need to be written better - this line in its current form it does not make sense.

Figure 1 title - check the text for formatting - It is not clear what the title of this figure is.
For some reason the Western blot panels look over-processed (A) and the images in panel B look as if the signals are extremely high.
Figure4 legend for (A) mentions 'at the same concentration of 10-10M' ... this is confusing given the data presented in panel A which is a dose-response curve. This needs to be corrected.
The formatting of Table 1 needs more careful consideration so that the information is presented clearly.
Experimental design: The research question has been simplified in a way that unnecessary data has been removed. I feel this has made the paper more straightforward.
The methods has been updated to include the key information for repetition.
Validity of the findings: I feel the authors need to elaborate further on the point they made in their discussion regarding what their data indicate.  On lines 356-359 the authors state that their results indicate that AceOrs could function as a G protein-coupled receptors in vitro.  The functional data that is presented in the paper is merely demonstrating calcium response EC50 values so I feel the authors need a stronger argument for this statement to be true.  At no point do the authors really explore the GPCR nature of the AcerOrs.  This point needs to be better addressed at the experimental level before such claims can be made.  I would urge the authors to consider this point in their 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: SORPTION TO SOIL, BIOCHAR AND COMPOST: IS PREDICTION TO MULTICOMPONENT MIXTURES POSSIBLE BASED ON SINGLE SORBENT MEASUREMENTS?
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper „Sorption to soil, biochar and compost …“ by Kah et al. describes an important aspect of sorption studies that definitely should be considered in many investigations dealing with the immobilization of pollutants to a sorbent.
Experimental design: The experiments described in this study have been well designed and have resulted in useful insights about sorption processes in a multicomponent system. This is a considerable progress compared to the all too common one-factor sorption studies.
Validity of the findings: Though I am generally quite happy with the paper, I suggest that the authors might consider a few minor issues:
•	The readers of the article might be interested to get a little more information about the rationale of the selected experimental design. What was the reason for selecting 5% biochar and 10% compost as additive to soil? A conclusive comparison of the sorbents is not made easier if varying amounts of the materials have been used. Another option would have been to add e.g. equivalent amount of organic carbon with the sorbent.
•	In the abstract it would be useful to indicate not only the changes in pyrene sorption by the added sorbents to soil as a multiple of the soil sorption but also to define which amount of added sorbent has caused these changes.
•	The authors rely heavily on the Freundlich model of sorption isotherms. Although it may well be that this is the most appropriate model for the specific experiments, it would be useful to mention why not alternative models like Langmuir or Dubinin-Raduskevic have also been tested for comparing the performance of different models.
•	Figures 2, 3, 4: it is not very fortunate to use only dark colors to show different treatments. Black can hardly be distinguished from dark-green and brown. More contrast is recommended.
•	Tables S4, S5: it is not very fortunate to use in both tables the abbreviation Std. as in one case standard deviation, in the other case standard error is meant. The usual abbreviations are s.d. and s.e.
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: SORPTION TO SOIL, BIOCHAR AND COMPOST: IS PREDICTION TO MULTICOMPONENT MIXTURES POSSIBLE BASED ON SINGLE SORBENT MEASUREMENTS?
Review round: 1
Reviewer: 2

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: This is a neat piece of work on the sorption of pyrene to biochar, soil and compost, and combinations thereof. The study's originality is in the combination of compost and biochar. The rest of the science presented, that binding at carbonaceous sorbents is less strong in the presence of soil or sediment (the "attenuation" effect), has been known for over 10 years.
The work is technically sound, with both passive samplers and batch sorption experiments.
Some issues I have with the study include;
1.	My most important question is: where are the DOC concentrations? There is a lot of argumentation around them, and that they could possibly change apparent Kd-values, but pyrene is not so very hydrophobic, so one needs high DOC concentrations to increase aqueous concentrations of pyrene. How high were the concentrations (if they were not measured, prepare dummy samples and do measure them), and would any effect on overall sorption be expected, calculated based on assumed K_DOC values for pyrene?
2.	Plot all sorption isotherms as log-log plots, now it is hard to see the low-concentration points
3.	Do not apply a Langmuir-like dual-mode sorption model for the sorbents, the requirements for Langmuir sorption are not fulfilled (monolayer coverage, homogeneous sorption sites). Just use a dual mode Freundlich isotherm,
CS= fsoilKDCW + fsorbKF,sorbCWn_sorbent
And derive n_sorbent from the sorption isotherms for the pure sorbents.
4.	Give the MS a grammar check, there were some faulty sentences, e.g. line 73-74, line 90, line 328
5.	It would be nice to find out whether the observed attenuation is a "real" phenomenon or only a kinetic thing – cite Hale et al 2009 (Hale, S. E., Tomaszewski, J. E., Luthy, R. G., & Werner, D. (2009). Sorption of dichlorodiphenyltrichloroethane (DDT) and its metabolites by activated carbon in clean water and sediment slurries. Water research, 43(17), 4336-4346) who observed that the fouling of AC by organic matter with regard to DDT adsorption was a kinetic phenomenon- after 2-3 years the sorption to AC in the presence of sediment was the same as sorption to clean AC. It is probably not possible to stretch the current measurements for such long times, but at least cite and discuss the possibility that this is a temporary phenomenon.
6.	Line 60: of course strong sorption to a sorbent inhibits availability for degradation, but the fractions unavailable for degradation are also unavailable for uptake. More nuanced discussion needed.
7.	Line 91: "contribution of DOC to sorption" – depends what you want to know. If you look at health effects, stick to the POM-based free concentrations. If you want to investigate transport, the total concentrations including DOC-bound ones are needed.
8.	Line 307-308: apart from that this sentence is a bit meaningless, I also disagree: measuring freely dissolved concentrations with passive samplers is not SO difficult…..


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: HOW WELL DO FORCE FIELDS CAPTURE THE STRENGTH OF SALT BRIDGES IN PROTEINS?
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is written in good English and easy to follow. The new work is clearly placed within the field, even including some historic contributions. Art work is relevant and well prepared.
Experimental design: The work performed is original and appears sufficiently detailed to allow reproduction, but lacks key simulations to support the claim made in the title.
Validity of the findings: Specifically, the paper deals with the interrogation of salt bridges on the surface of the protein GB1 by MD simulations with several force fields (FFs) and solvent models. Despite observations of several salt bridges in PGB1 by X-ray crystallography, NMR failed to detect the presence of stable ionic bridges, meaning that these interactions in solution are weak or absent (main conclusion from the work by Tomlinson 2009). Free energy calculations in the current work argue that MD overestimates ionic contributions with the FFs tested. This can be considered an extension of the study by Chong and co-workers (Debiec 2014) on amino acid analogues, with ditto conclusion. The authors did not address the fundamental question whether simulations in a crystal form of the protein could have explained the difference of the solution NMR and X-ray observations. This would be one way to test whether the MD force fields are any good.

A second shortcoming is that the authors have not included the newly developed ff15ipq FF, which is supposed to have mitigated problems of overemphasizing energetics of salt bridges (Debiec 2016).

Making these two important controls would allow the authors to make true their title: How well do force fields capture the strength of salt bridges in proteins? With the current data the question is still open.
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: HOW WELL DO FORCE FIELDS CAPTURE THE STRENGTH OF SALT BRIDGES IN PROTEINS?
Review round: 1
Reviewer: 2

Output:
Basic reporting: •	The overall clarity of the manuscript is high, the figures are high quality, well labeled and described, and the authors’ raw data is provided.
•	The authors provide context including the importance of salt bridges and prior simulation work. However, it should be made clearer that the work described was focused on fixed-charge force fields, and the benefits and limitations of this approach briefly explained.
Experimental design: •	The research described is relevant and overall well-designed, and the methods described in sufficient detail.
•	In lines 237-241, the authors state that:
In order to be conservative and not overestimate the calculated values by including e.g. solvent mediated interactions (as it is unclear how much they contribute to the experiments), we included only conformations where the nitrogen–oxygen distance is < 5.0 Å.
The selected cutoff of a minimum nitrogen-oxygen distance 5.0 Å is actually generous and includes conformations in which the nitrogen and oxygen are not in direct contact. A more conservative cutoff would be 4 Å ; this will yield a decrease in the populations listed in Table 1, but should not impact the conclusions. The use of the minimum nitrogen-oxygen distance as the coordinate should also be clarified.
Validity of the findings: •	The authors’ findings are robust and validated by testing of alternative simulation methods, and their conclusions are well-stated. As in the introduction, the conclusions should make clear that their findings apply to fixed-charge force fields in particular. It is worth mentioning that work on model systems, including the cited Debiec et al. 2016 paper, suggests that polarizable force fields yield salt bridge interactions in better agreement with experiment than the tested fixed-charge force fields.
Additional comments: •	The authors should provide some discussion of the potential impact on their results of differences between the bonded parameters of the tested force fields, which may impact the conformations accessible to the interacting side chains of interest.
•	In lines 224-228 the authors state that:
In the case of the K39–E35 and K58–D55 pairs, additional minima are observed
where the shortest of the two oxygen–nitrogen distances is ~ 6 Å – 10 Å (Figs. 1C and 1D). These correspond to solvent-separated ion pairs, where one or more solvent molecules sit between the amino acid side chains between the pairs and effecting the electrostatic interacting of the cation and anion (Collins, 1997; Marcus & Hefter, 2006; Zhou & Pang, 2017).
Based on the results shown in Supplemental Figure 2, the solvent-separated ion pair is also observed for the K12-E23 salt bridge, most clearly for CHARMM27 and AMBER ff03w. In addition, the location of the minima, in terms of the shortest oxygen-nitrogen distance, is closer to 4-7 Å rather than 6-10 Å.
•	Supplemental Figure 2 refers to “Amber ff03” rather than “Amber ff03w”


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: TWO NEW SPECIES OF PRIMULINA (GESNERIACEAE) FROM LIMESTONE KARSTS OF CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article needs significant improvements of the English grammar and style throughout.  There were places that citations were barely paraphrased from the source material (Lines 45-48).  There are more than enough citations and proper background is given, but it is hard to follow.  Table 1 and 2 should be condensed to show the significant differences that one would use to separate the taxa efficiently.  It might be more useful to see a dichotomous key to the taxa as opposed to the tables.  Figure 1 would be better called "Illustration of Primulina davidioides." Although Figures 3 and 4 are beautiful, I think that again a single figure noting differences would be more effective.  The purpose is to quickly notice the differences and be able to compare with other publications or field specimens.
Experimental design: I am okay with the methods there appears to be enough replication and specimens viewed from many sources.
Validity of the findings: I have no doubt that these are two new species.  There are obvious differences shown but the overall paper could be much more concise.
Additional comments: You have done an extensive amount of work and I am happy to see two wonderful new species.  I hope that you are able to edit the grammar and style.


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: TWO NEW SPECIES OF PRIMULINA (GESNERIACEAE) FROM LIMESTONE KARSTS OF CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Figure 1.
In the photograph (Fig. 3) and manuscript, P. davidioides has three staminodes. However, I cannot find the third staminode in Figure 1-B. I recommend you to use another illustration or to add the third staminode in the illustration.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Dear authors,
Hong et al. found two new Primulina species in limestone karsts of Southern China, and taxonomic investigations for the plants were conducted based on detailed examination of morphological anatomical features. I consider your manuscript to be well written, and the new Primulina introduced in this study will be good species. In addition, I think that this work may have a good contribution to the understanding of the plant diversity in China. Nevertheless, I found some minor points to add/change. Please see following comments.

Specific comments:

Page 7, L 52. I think that “Fig. 1” cited at the end of the sentence is inadequate and unnecessary. Please delete it.

Page 10, L96. “Japan”

Page 10, L108-109. You should explain the validity of the basis, why one could argue that P. lunglinensis is closely related to P. davidioides. What kind of floral and/or leaf morphology? Please clarify.

Page 12, L157. “vegetative appearance” is ambiguous. Please explain the details of that.

Page 14, L184. “November” or “December”, be consistent.


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: TWO NEW SPECIES OF PRIMULINA (GESNERIACEAE) FROM LIMESTONE KARSTS OF CHINA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The English quite poor in grammar and style and requires a substantial input prior publication.
References are sufficient, but need reassessment after final revision of the MS
Structure: The discussion is too long and over most parts irrelevant to the presented data, i.e. the morphological description of two new species. It is unclear what the purpose of the discussion is. Removing the irrelevant or too general parts and moving the family info to introduction, little it left. This is perhaps not the best place to discuss the floral diversity of a genus when only two new species are described and without any hypothesis to test. A discussion here could surround the wider morphological affinities of the new species in the genus. Only the two comparative species are mentioned, but the vegetative habit of P. davidioides is very generic and its occurrence in other species could be discussed, and the floral affinities in a wider genus-wide context, but compared to other specific species, not just in general terms.
Some parts from the discussion are better placed in the introduction to introduce the plant family Gesneriaceae. This is rather absent in the introduction at present.
The conservation assessment should go before the discussion separately under each species with detailed justification for the categories and subcategories chosen.

 Self-contained, though the discussion too general and mostly irrelevant.
Experimental design: Ok
Validity of the findings: Further specific comments:
Line 43: Add Möller et al 2016 Guihaia here for an updated account of endemic gesner genera in China.
Line 78: LSIDs are not available for the new species, but are apparently a requirement of PeerJ
Line 85: More details on the nature of material deposited is needed, e.g. herbarium specimens? spirit preserved? what tissue samples were deposited?
Line 93: How were type images consulted in IPNI?

Line 108: The diagnosis needs more focus on fewer main characters and a listing of the respective characteristics for P. lunglinensis. Other characters to consider are given below:
	P. lunglinensis 	P. davidioides
Corolla	with two yellow ridges on floor	with yellow ridges
Filaments	red	white
Petiole	0.6-8 cm 	1-2 cm
The leaves and large bracts of the new species are very similar to P. lutea. This can be discussed in the notes/discussion.
Lines 126+: These yellow lines are difficult to see in the photos. Are these located on ridges as in P. lunglinensis?
Line 132: describe anthers coherence.
Lines 157+: see comments for diagnosis for P. davidioides re characteristics of P. luzhaiensis.
Line 157: the leaves and their arrangement are very common in Primulina and thus characters of those are not useful.
Line 175: Are they really fused, or coherent by long papillae as in Saintpaulia? See Weberling 1981: Morphologie der Blueten und der Bluetenstaende, Ulmer Verlag, page 131.  Please check for both species
Line 195: These numbers are out of date. Check Möller et al 2016 Guihaia
Line 190+: The discussion is mostly not relevant to the two species described here. The beginning seems like a good introduction of the family and genus in China.
Lines 254+: The conservation part is greatly repeat of earlier text and can be reduced and focussed on the two species and their threats, to explain their categorisation.
Lines 294+: The references need adjustment at the end of the revision of the MS.
Additional comments: see above


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: TWO NEW SPECIES OF PRIMULINA (GESNERIACEAE) FROM LIMESTONE KARSTS OF CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: English of the newly added text still occasionally to be corrected.
Spelling mistake of Gesneriad (line 86).
Experimental design: ok
Validity of the findings: The conservartion assessments need more details, which will provide important baseline data as future reference point.
However, the proposed categories need furter thoughts and perhaps if uinsufficient knowledge exists, they maybe DD, data deficient. See comments in MS.
Additional comments: Needs some more work as described above and in the annotated MS 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: DIVERSITY AND ABUNDANCE OF CONSPICUOUS MACROCRUSTACEANS ON CORAL REEFS DIFFERING IN LEVEL OF DEGRADATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: An excellent study with few shortcomings, written in good academic English.
Experimental design: Although Underwater Visual Census techniques are used in a number of studies on Decapoda, they do have a large amount of inherent bias towards highly mobile, conspicuous and easy to identify species.  It is therefore not surprising that only one species of Alpheus is recorded.  Unquestionably however, several more species of that genus would have been running around on the transect lines, moving under rocks and rubble.  It would be good to see some critical text discussing how sampling limitations of a UVC could potentially influence the results.
Validity of the findings: Asides from the above comment on UVC, the findings seem in line with other work.
Additional comments: Although multivariate statistics are highly appropriate for this type of study, I would not think that the calculated diversity indices would be parametric in nature and thus should not be analysed with ANOVA.

It would be good to include sources used to identify the species, was this largely based on UW photography guides or was primary taxonomic literature used?  In this regard it appears odd that Mithraculus coryphe was the most abundant species, usually M.sculptus is far more abundant.  Perhaps also discuss how the divers were trained in identification, and any bias between them.  I would also query why UW photography was not used to get an ID for some taxa, certainly a taxonomist could easily have identified the majority to genus, if not species level of those listed at family level and above. Using "Caridean A"  is rather odd as shrimps can easily be identified to family level, and that does raise questions about the ability of the divers to correctly ID taxa.  And finally, Cinetorhynchus fasciatus (please not correct spelling of genus) does not occur in the Atlantic !  There are only two known species of that genus in the Atlantic, C.rigens and C.manningi.  Again this raises some questions about the accuracy of UVC identifications used herein


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: DIVERSITY AND ABUNDANCE OF CONSPICUOUS MACROCRUSTACEANS ON CORAL REEFS DIFFERING IN LEVEL OF DEGRADATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript provides a description of the abundance of crustaceans on two coral reefs that differ in benthic community structure and explores the role of degradation and roughness on crustaceans. Despite decades of studies on coral reefs, studies like this one still are lacking, and reef ecologists continue to focus on fishes and stony corals so that quantitative data on other taxa remain rare. This reason alone makes a compelling reason to publish this study, and indeed the manuscript is well written and very nicely supported by literature. However, I cannot support publication in this format:

1. This study remains an analysis of two reefs at a single time point using 30 transects at each site. The authors need to make a stronger case that this study has general value. I am confident this can be done, but there seems little attempt to do this in the current version. Even the notion that this is a contrast of a degraded and less degraded reef is ambiguous, as no data to this effect are presented, although some citations to this effect are added at line 127. It would greatly strengthen this study to add a little time series context to Fig. 2.

2. The analysis of benthic roughness by the “HAS” index is exceptionally weak, and even the application of the better-known rugosity index is done in a non standard way. This is surprising since one of the authors has published a very nice review on reef roughness. At a time when ecologists are using increasingly sophisticated tools to quantify benthic roughness, the HAS method, which is just a qualitative ranking, is not an acceptable tool. The rugosity method was conducted with un-weighted transect which would not conform to the benthos (this method is usually done with a weighted chain). The same tape was used to measure benthic community structure, and the low resolution of this method (10 points 10 cm apart down a 10 m line) surely contributed to the high variance in the benthic data (Fig. 2). Taken together, it is hardly surprising that the reefs did not differ in roughness.

In general, given the simplicity of this study and the limited generality of the outcome, this would need to be greatly trimmed in length to justify publication.
Experimental design: Weak
Validity of the findings: Very narrow -- two reefs one time point. Generality needs to be established.
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: DIVERSITY AND ABUNDANCE OF CONSPICUOUS MACROCRUSTACEANS ON CORAL REEFS DIFFERING IN LEVEL OF DEGRADATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: no further comment
Experimental design: no further comment
Validity of the findings: no further comment
Additional comments: The authors have adequately addressed my review comments, and I thus recommend publication.


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

Input:
Title: BCD BEAM SEARCH: CONSIDERING SUBOPTIMAL PARTIAL SOLUTIONS IN BAD CLADE DELETION SUPERTREES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Authors present an improvement of their previously introduced Bad Clade Deletion (BCD) algorithm, a polynomial greedy supertree method. Supertree methods, which consist to assemble partial phylogenies to a large and unique one while minimizing conflicts, constitute a major and widely studied problem in phylogenetics. BCD minimizes the number of matrix columns deletions to resolve the input matrix conflicts (the input matrix contains cladistics information of all input trees). Here, the paper presents a beam search algorithm (BCD BS) that improves the efficiency of BCD. At each step of the supertree construction (refinement), BCS BS considers simultaneously k partial solutions instead of 1. Naturally, reconstructed supertrees are (slightly) better with the beam stream technique (with k=25 in experiments) than without, while running times increase linearly according to k.

The paper is globally clear, well written, and adequately structured. Algorithms are sufficiently detailed (but not necessarily in the best way, see below) and experimentations perfectly show the efficiency of the proposed mechanism.

However it is certainly possible to significantly improve the description of the problem and especially the methods by adding figures and algorithms. This would provide a better understanding of the contribution, especially for a reader who is not already familiar with MCD and BCD. As is stands, the article is quite short but dense in technical descriptions.
In the phylogenetic trees preliminaries, some definitions seems not perfectly clear (induced subtree, parent tree, lines 84-87).

Very few typos noted:
- Abstract: both beam -> Both beam
- line 216: solution -> solutions
- line 396: Table ?? -> Table 1
Experimental design: see (1)
Validity of the findings: Good.
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: BCD BEAM SEARCH: CONSIDERING SUBOPTIMAL PARTIAL SOLUTIONS IN BAD CLADE DELETION SUPERTREES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Everything here is basically ok. The MS is well structured and clearly written and it is easy to follow what the authors have done and why they have done it. The results are also presented clearly and accurately.

The English does need a bit of polishing, however, especially later on in the MS. Nothing major and nothing that detracted from the article, but a bit of spit and polish would be good.
Experimental design: This is an interesting MS that makes a useful advance toward supertree methodologies. The problem with almost any (meaningful) phylogenetic analyses is that heuristic searches have to be used to get around the NP-complete nature of the problem. Therefore, any polynomial time solutions are most welcome!

I can't really dissect the math behind the new method (so a review from a mathematician is definitely needed), but I can say that the testing of their method with both simulated and empirical data is robust and shows the performance of the different methods under a range of conditions. Thus, I am confident that the comparative results are accurate.
Validity of the findings: For the most part, see my comments above. The experimental design is thorough and well performed such that it is my opinion that the results regarding the comparative performance of the different methods are accurate.
Additional comments: Some more minor and /or specific comments that I had:

L13: It's not really true that differing process can lead to conflicts because even the same one (e.g., incomplete lineage sorting, ILS) can cause gene trees to disagree with one another and still be accurately for the evolutionary history of that gene. On the flip side, different evolutionary processes (e.g., ILS and horizontal gene transfer) could, by chance, lead to the same result.

L48: But was the quality any good per se? It might be the best result, but still not a very good one.

L57: State-of-the-art tends to mean the newest, which MRP definitely isn't. Perhaps "established"?

L61: Add an "s" to "branch length".

L88: "taxa set" should be "taxon set", here and throughout.

L98- Spell out "1-1".

L186: "partial solutions".

L210: "two graphs have"

L230: Explain what "non-decreasing weights" are? I take it that this is something different than simply increasing weights?

L236: Delete the word "do".

L264: log to the power of 3???

L281: Is such a guarantee even possible? OR does the problem fall into the NP-complete/hard class such that it might be possible.

L282: What does "high probability" mean here exactly? Rather vague.

L309: Specify that it is outperformed WRT accuracy.

L314: Simulated data, however, often have the disadvantage that the signal is too strong such that almost any method does well.

L346ish: If the true tree is unknown, how can one measure the false positives or negatives? Explain.

L353: Some rough numbers would be helpful in this paragraph. For instance, can one say that the performance increase was usually two-fold better (or something like that)? (As in the next paragraph.)

L364: Although the two-fold increases are mentioned here, some real numbers would be good too. A two-fold increase on a running time of 10 seconds is trivial, but not for 10 days!

L368: "As expected, the beam search is".

L373: "whereas the running time increases only linearly for".

L380: Define "suboptimal".

L382: So it would appear that BCD requires some form of branch length or (bootstrap) support?

L395: Improves WRT what?

L396: Add the Table number.

L398 Any idea why? Have you tried to see how much conflict there is in the data set? If there is very little then perhaps all methods point to the same (obvious) solution.


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: BCD BEAM SEARCH: CONSIDERING SUBOPTIMAL PARTIAL SOLUTIONS IN BAD CLADE DELETION SUPERTREES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors fully took into account the remarks made after the first submission. The article was already nice and very pleasant to read. Complementary figure and pseudo-code make the contribution and algorithm easier to understand. New Table 1 and extreme cases instances are also judicious additions.
Experimental design: Rigorous and replicable study. The experimental setup is well described. The Java code is provided and publicly available.
Validity of the findings: The efficiency of BCD Beam Search is experimentally assessed, and conclusions are supported by appropriate experiments.
Additional comments: Minor remarks and typos:
- line 361: "bats" should be emphasized, and "see Jones et al. 2002" included in parentheses
- line 381: instanceS


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: BCD BEAM SEARCH: CONSIDERING SUBOPTIMAL PARTIAL SOLUTIONS IN BAD CLADE DELETION SUPERTREES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Fine.
Experimental design: Improved with the additional explanation and the added empirical samples.
Validity of the findings: Again, improved with the added empirical examples.
Additional comments: The revisions to the paper, although relatively minor, have strengthened what was already a good paper describing an interesting supertree method and I recommend that the paper be published as is.


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

Input:
Title: GORGONOPSIAN THERAPSIDS (NOCHNITSA GEN. NOV. AND VIATKOGORGON) FROM THE PERMIAN KOTELNICH LOCALITY OF RUSSIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a very solid paper that makes several important contributions, including the recognition of an endemic Russian clade of gorgonopsians and anatomical details on the palate of the Russian species.  Below I raise four substantive issues to be addressed in a revision, plus a bunch of minor edits.

Comment 1:  Figures 4 and 5 should be combined, so the reader doesn't need to go back-and-forth between the two.  In other words, the all of comparative figures should include both photos and drawings on one page (as already done for Figures 8 and 9).

Comment 2: Gorgonopsians and therocephalians are typically considered sister taxa, and the authors seem to agree with this view, given the comparisons they make (e.g., Lines 651-652).  However, the outgroup used for the phylogenetic analysis is Biarmosuchia (viz. Hipposaurus and Biarmosuchus). No rationale is provided.
The phylogenetic analysis should be re-run with a mid-Permian therocephalian used as the first outgroup (e.g., Lycosuchus or Glanosuchus).  If nothing changes in the results, a line can be added to this effect in the revised manuscript.  However, if the results change substantially, then more substantial edits will be needed.

Comment 3: Based on the results of the phylogenetic analysis, the authors propose to recognize two major subclades with Gorgonopsia: Inostrancevioidea and Gorgonopioidea.  First, this the phylogenetic results need to be confirmed when the appropriate outgroup is used (see Comment 2). Second, the authors fail to propose a phylogenetic definition for the new taxa, suggesting the need to wait for more robust support from subsequent analyses, before doing so.  You can't have it both ways-either provide phylogenetic definitions or don't propose the clade names.  Using a new clade name but not providing a definition is a disservice to future workers.  If the authors want to stick with their cautious approach, using "Russian clade" and "African clade" as place holders in the discussion is totally appropriate.

Comment 4: Seeing as this paper names a new species, describing the holotype in detail is very important.  Unfortunately, the current description of the postcrania is very superficial and should be supplemented in the revision.

The remainder of my comments are minor line edits or suggestions:

L33-36: Smiley et al. (2008) identified a gorgonopsian from the Permian of Niger.  It might be worth mentioning this occurrence, since it falls nicely between the southern and northern records mentioned.

Smiley, T. M., C. A. Sidor, O. Ide, and A. Maga. 2008. Vertebrate fauna of the Upper Permian of Niger. VI. First evidence of a gorgonopsian therapsid. Journal of Vertebrate Paleontology 28:543-547.

L55-56: Rephrase as: The first Russian species, Inostrancevia alexandri, remains the best-known gorgonopsian from the… (clearly it is not the best known taxon)

L66-67: Explain or rephrase "at an alarming pace"

L212-215: What is shown in Figure 5 for the septomaxilla is unlike the condition observed in most therapsids.  This should be better explained in the text.  Is the area damaged?  Is it real and a transitional morphology from what is seen in pelycosaur-grade synaspids to what is seen in therapsids?

L214: Add "(i.e., facial") between posterior and process.  Facial process is the standard term.

L238: Replace "identical" with "similar"  (They can't be a different size and identical)

L235-248: Please discuss any evidence available that the 'twinning' of postcanine teeth on the right side is real.  For example, does preparation shown that no alveoli are present in between the pairs of teeth?  I'm a little concerned that one of the diagnostic features of the species is apparently absent on the left side of the specimen.  More explanation or justification seems appropriate.

L297: Replace "mid-parietal suture" with "midline suture between the parietals"

L307: Replace "from comparison with" with "based on the configuration seen in"

L318: Add "and medial" after "anterior"

L368: Be more specific than "noted above"

L396-397: The description about the septomaxilla and maxilla is unclear (e.g., maxilla is described as "taller and shorter") and should be rewritten.  What is the anterodorsal portions of the maxilla?

L472: How can there be 2 citations for the "only existing" analysis?  Rephrase to "the only published cladistic analysis of gorgonopsians (Kammerer 2017)."

L474: Insert "to" before "better"

L488-489: Rephrase for clarity.  I think you're referring to the body of the premaxilla.

L490: Sidor (2003) not in literature cited.
Sidor, C. A. 2003. The naris and palate of Lycaenodon longiceps (Therapsida: Biarmosuchia), with comments on their early evolution in the Therapsida. Journal of Paleontology 77(5):153-160.

L490: Delete "internal"  It's either choana or internal naris.

L513-518:  I was a little confused by this section.  A new figure showing the 3 character states would definitely benefit future workers.

L541-543: This is confusing as written.  Rephrase to: "in Sycosaurus nowacki (UCMZ T878), a specimen Kemp (1969) previously described as Leontocephalus intactus."

L578-579:  This is a little confusing because "height" isn't being used in standard vertical orientation here.  Please rewrite.

L626, L702: Rephrase to avoid using ambiguous terms like "one node up" and "main burst".

L653-660: See comment #3.

L707: Rephrase to "specimens of Eriphostoma" to avoid using a taxon name as an adjective.
Experimental design: No comment.
Validity of the findings: See comment about choice of outgrip in the phylogenetic analysis.  Otherwise, no comment.
Additional comments: Interesting paper and good job.


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: GORGONOPSIAN THERAPSIDS (NOCHNITSA GEN. NOV. AND VIATKOGORGON) FROM THE PERMIAN KOTELNICH LOCALITY OF RUSSIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: I have commented on my opinions on the figures, I wish them to be altered from their current state but in general they are still relatively good, and do not dramatically dampen the manuscript.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Peer Review:
Gorgonopsian therapsids (Nochnitsa gen. nov. and
Viatkogorgon) from the Permian Kotelnich locality of Russia

The authors Kammerer and Masyutan, present extremely important new findings of a basal gorgonopsians from a relatively underworked locality the Kotelnich of Russia. They anoint the new species Nochnitsa geminidens and provide a long awaited re-description of the taxon Viatkogorgon ivakhnenkoi (Tatarinov, 1999).

There are some minor corrections/suggestions I placed in the manuscript, however there are a few major points to bring up here. First, what of the postcrania of Viatkogorgon, how does this compare to Nochnitsa geminidens, I would have like to have seen this described too, it seems gorgon postcranial remains are all to glanced over.

Additionally, and I find most important that there are two major subgroups distinguished here (or recognized) these being the Inostrancevioidea (containing the Russian taxa Inostrancevia, Pravoslavlevia, Sauroctonus, and Suchogorgon) and Gorgonopioidea (containing all African gorgonopsians). While these groups are likely valid, that is I do generally agree with the author, there is an issue in recognizing these clades and not formally diagnosing them here, or even attempting to do as much. I understand that definitions may change, but currently the Rubidgeinae (a large clade of robust African gorgons) also lacks a formal definition, and this whole business of naming clades without providing diagnoses does not sit well with me, It would even be better to just refer to them as an un-named clade until this can be done formally. I suggest a tentative diagnosis is made, including all uniting characters and phylogenetic definitions at present, at least this gives the reader a sense of real support for the naming of these groups.

I feel it would be more than helpful to have a locality map and strat column given the emphasis here of the locality. To be honest, I don’t know why the authors really didn’t do this already since they added a geologic context section.

This leads me to my final point,  in general the figures could have been made with more care, particularly some of the line drawing are not very helpful to interpret the anatomy, unless some attempt is made to show depth, with stippling I would say that these should be revised.

If these changes are made I would gladly recommend this article for publication.

Sincerely,

Arjan Mann


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: GORGONOPSIAN THERAPSIDS (NOCHNITSA GEN. NOV. AND VIATKOGORGON) FROM THE PERMIAN KOTELNICH LOCALITY OF RUSSIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: In this paper, the authors describe two basal gorgonopsians from the important Kotelnich locality in Russia’s Permian, one of them providing the basis of a new genus and species. The paper further examines the complicated evolutionary relationships of gorgons with emphasis on their global radiation during the middle-to-late Permian transition.

The finding that Russian Inostranceviinae diverged early is an interesting concept, and the overall updated taxonomy and new cladistic definitions will be an important contribution. I do, however, suggest more clarity in the definitions, and I address this in the section below (‘Experimental Design’).

In sum, the project is well researched, the paper is structured well and the existing illustrations are composed well, although I would like to see better use of illustrations (including a geology figure and more labeling of the cladogram Fig. 10). Overall, I would recommend this study for publication with only some minor tweaks.
Experimental design: Geology and Age:
My limited understanding of the Kotelnich locality is that there are fossil-bearing deposits at multiple levels that are either middle or early-late Permian (or both). Fossils are distributed vertically throughout the lower member, and the new gorgon KPM 310 is said to come from the middle of the lower member. It would be most useful if this could be illustrated in a stratigraphic log, but I understand if the data are unavailable for this level of detail. The authors should consider figuring the geologic/stratigraphic context if possible.

Choices on Taxonomy:
Unfortunately, the definitions aren’t as explicit as they could be, further muddying how paleontologists discuss these groups. For example, the text refers to “Gorgonopids” and “Inostranceviids/Inostranceviines,” but these nodes aren’t labeled on the cladogram in Figure 10. Is “Inostranceviidae” equivalent to the node labeled “Inostrancevioidea” in Figure 10?

Two options: (1) For the sake of preserving the term “Gorgonopidae” as it frequently appears in the literature, I would recommend defining the family as inclusively as possible, encompassing the common ancestor of Inostranceviinae and Rubidgeinae and all of its descendants (specifically, the node labeled ‘66’ in Fig. 10). That would only exclude Nochnitsa and Viatkogorgon, essentially reassigning them as non-gorgonopid gorgonopsians. Another option (2) would be to constrain the family by the genus Gorgonops (e.g., all more closely related to Gorgonops than to Eriphostoma and Inostranceviids), but then that would taint the previous literature that has called all these other taxa gorgonopids as well. Hence, my pitch to go inclusive.

Whichever option the authors choose, the important thing is that the definitions are clear and that the cladogram in Figure 10 is adequately labeled. Then we can all start speaking the same language.

Data Repository:
Because gorgon cladistic analyses are so few, I could imagine this matrix being useful to many paleo researchers. The authors should find a repository for the Nexus file, include a complete character list (not just a discussion of state changes from previous publications, which makes replication tedious and difficult), and include a statement or link in the manuscript. MorphoBank would be ideal.
Validity of the findings: I generally agree with the findings, but I think more effort in demonstrating the age of these occurrences (aided by a figure) would give greater confidence in the timing of the early gorgonopsian radiation (is it middle Permian? Is it early-late Permian?). See my comment above on the geology of Kotelnich and its major members.
Additional comments: Minor comments are copied below and marked-up in the attached PDF:

Intro:
lines 29-31 – Gorgonopsians are not “abundant” (see Smith et al., 2012, Forerunners of Mammals: Chapter 2) nor are they “omnipresent.” Rephrase this.

Lines 660 – Clarify: “Belong to [the African gorgonopioid] clade”

Lines 679-694 – The relevant biogeographic discussions of therocephalians by Huttenlocker et al. (2015, JVP) Huttenlocker & Sidor (2016, JVP) and Huttenlocker & Smith (2018, PeerJ) are missing from the ‘Discussion’ section. For example, the 2015 and 2016 papers are invoked in the mention of sister-taxon relationships, but are not cited. How does the gorgonopsian pattern mirror (or not mirror) those already discussed in therocephalians? I would emphasize that it is different in the respect that the gorgons show fewer sister-taxon pairs, but the early dichotomy of major groups is congruent with the finding that so many therocephalian subgroups also include basal Russian representatives. I don’t know what this means, but it’s something to chew on.

Additional References:

Smith, R., Rubidge, B., & Van der Walt, M. (2012). Therapsid biodiversity patterns and paleoenvironments of the Karoo Basin, South Africa. Forerunners of Mammals: Radiation, Histology, Biology. Indiana University Press, Indianapolis, Indiana, 30-62.

Huttenlocker, A. K., Sidor, C. A., & Angielczyk, K. D. (2015). A new eutherocephalian (Therapsida, Therocephalia) from the upper Permian Madumabisa Mudstone Formation (Luangwa Basin) of Zambia. Journal of Vertebrate Paleontology, 35(5), e969400.

Huttenlocker, A. K., & Sidor, C. A. (2016). The first karenitid (Therapsida, Therocephalia) from the upper Permian of Gondwana and the biogeography of Permo-Triassic therocephalians. Journal of Vertebrate Paleontology, 36(4), e1111897.

Huttenlocker, A. K., & Smith, R. M. (2017). New whaitsioids (Therapsida: Therocephalia) from the Teekloof Formation of South Africa and therocephalian diversity during the end-Guadalupian extinction. PeerJ, 5, e3868.